Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors describe a method to probe both the proteins associated with genomic elements in cells, as well as 3D contacts between sites in chromatin. The approach is interesting and promising, and it is great to see a proximity labeling method like this that can make both proteins and 3D contacts. It utilizes DNA oligomers, which will likely make it a widely adopted method. However, the manuscript over-interprets its successes, which are likely due to the limited appropriate controls, and of any validation experiments. I think the study requires better proteomic controls, and some validation experiments of the "new" proteins and 3D contacts described. In addition, toning down the claims made in the paper would assist those looking to implement one of the various available proximity labeling methods and would make this manuscript more reliable to non-experts.

Strengths:

(1) The mapping of 3D contacts for 20 kb regions using proximity labeling is beautiful.

(2) The use of in situ hybridization will probably improve background and specificity.

(3) The use of fixed cells should prove enabling and is a strong alternative to similar, living cell methods.

Weaknesses:

(1) A major drawback to the experimental approach of this study is the "multiplexed comparisons". Using the mtDNA as a comparator is not a great comparison - there is no reason to think the telomeres/centrosomes would look like mtDNA as a whole. The mito proteome is much less complex. It is going to provide a large number of false positives. The centromere/telomere comparison is ok, if one is interested in what's different between those two repetitive elements.

We appreciate the reviewers' point here. In fact we selected the mitochondrial DNA as a target for just the reason that the reviewer notes. mtDNA should be spatially distinct from the nuclear targets and allow us to determine if we were in fact seeing spatially distinct proteins at the interorganelle (mtDNA vs. telomeres/centrosomes) and intraorganelle (telomeres vs centromeres) levels.

But the more realistic use case of this method would be "what is at a specific genomic element"? A purely nuclear-localized control would be needed for that. Or a genomic element that has nothing interesting at it (I do not know of one).

We have now added two studies in Figure 4 and Figure 5 detailing the use of OMAP to investigate specific genomic elements. In this case the Hox clusters (HOXA and HOXB) and haplotype-specific analysis of X-chromosome inactivation centers in female murine (EY.T4) cells. The controls in these cases are more specific, in line with those suggested by the reviewer as we (1) compare HOXA and HOXB with or without EZH2 inhibition using the same sets of probes and (2) specifically compare the region surrounding the XIC in female cells for the inactive and active X chromosomes.

You can see this in the label-free work: non-specific, nuclear GO terms are enriched likely due to the random plus non-random labeling in the nucleus. What would a Telo vs general nucleus GSEA look like? (GSEA should be used for quantitative data, no GO). That would provide some specificity. Figures 2G and S4A are encouraging, but a) these proteins are largely sequestered in their respective locations, and b) no validation by an orthogonal method like ChIP or Cut and Run/Tag is used.

We performed GSEA on the enrichment scores for the label-free proteomics data from the SAINT output in Figure 1D and that several of these proteins (e.g., those highlighted in Figure 2A: TERF1, CENPN, TOM70) have already been extensively validated to co-localize to these locations.

To the reviewers request for additional validation, we analyzed ChIP-seq data for several proteins to determine if they were enriched surrounding specific loci. In the case of the HoxA/B analysis, we found that HDAC3 and TCF12 were enriched at HOXB compared to HOXA, and SMARCB1 and ZC3H13 were enriched at HOXA compared to HOXB (Figure 4C). HDAC3 and TCF12 ChIP data confirmed increased peak calls at HOXB and SMARCB1 and ZC3H13 ChIP data confirmed increased peak calls at HOXA for these four selected proteins (Figure 4D).

You can also see this in the enormous number of "enriched" proteins in the supplemental volcano plots. The hypothesis-supporting ones are labeled, but do the authors really believe all of those proteins are specific to the loci being looked at? Maybe compared to mitochondria, but it's hard to believe there are not a lot of false positives in those blue clouds. I believe the authors are more seeing mito vs nucleus + Telo than the stated comparison. For example, if you have no labeling in the nucleus in the control (Figures 1C and 2C) you cannot separate background labeling from specific labeling. Same with mito vs. nuc+Telo. It is not the proper control to say what is specifically at the Telo.

We agree with the reviewer that compared to mitochondrial targeting, there could be non-specific nuclear comparisons. We note again though that we purposefully stayed away from using the word “specifically” when describing the proteomics work developed here. The reason being that we are not atlasing a large number of targets to define specificity. Instead, we highlight in Figure 2 that we did observe differences in proteins associating with telomeres and mitochondrial DNA. That may be non-specific, and in fact, this is also why we decided to include two nuclear targets to determine what might be specifically enriched. Thus, we compared centromeric and telomeric protein enrichment as determined by OMAP and observed consistent differential enrichment of shelterin proteins at telomeres (Figure 2I) and CENP-A complex members at centromeres (Figure 2J). We could have done the relative comparisons to no-oligo controls, analogous to how CASPEX compared targeted analyses to no-sgRNA controls (PMID: 29735997). However, we found that the mitochondrial targeted samples were generally better as a comparator because (1) we have clear means to validate differences and (2) the local environment around DNA is being labeled.

I would like to see a Telo vs nuclear control and a Centromere vs nuc control. One could then subtract the background from both experiments, then contrast Telo vs Cent for a proper, rigorous comparison. However, I realize that is a lot of work, so rewriting the manuscript to better and more accurately reflect what was accomplished here, and its limitations, would suffice.

Assuming the nuclear control was the same, It is unclear how this ratio-of-ratios ([Telo/Ctrl]/[Cent/ctrl]) experiment would be inherently different from the direct comparison between Telo and Centromere. Again, assuming the backgrounds are derived from the same cellular samples. More than likely adding the extra ratios could increase the artifactual variance in the estimates, reducing the power of the comparisons as has been seen in proteomics data using ratio-of-ratio comparisons in the past (Super-SILAC).

(2) A second major drawback is the lack of validation experiments. References to literature are helpful but do not make up for the lack of validation of a new method claiming new protein-DNA or DNA-DNA interactions. At least a handful of newly described proximal proteins need to be validated by an orthogonal method, like ChIP qPCR, other genomic methods, or gel shifts if they are likely to directly bind DNA. It is ok to have false positives in a challenging assay like this. But it needs to be well and clearly estimated and communicated.

We appreciate the reviewers' point here. To be clear, we have not made any claims about new proteins at specific loci. Instead we validated that known telomeric and centromeric associating proteins were consistently enriched by DNA OMAP (Figure 2). We also want to emphasize that while valuable, the current paper is not an atlasing paper to define the full and specific proteomes of two genomic loci. We instead show how this method can be used to observe quantitative differences in proteins enriched at certain loci (HOXA/B work, Figure 4) and even between haplotypes (Xi/Xa work, Figure 5).

(3) The mapping of 3D contacts for 20 kb regions is beautiful. Some added discussion on this method's benefits over HiC-variants would be welcomed.

We appreciate the reviewers' point here and have added the following text to the discussion: “Additionally, we show that this method is also able to detect DNA-DNA contacts through biotinylation of loop anchors. Our approach functions similarly to 4C[86]. However, our approach of biotin labeling of contacts does not rely on pairwise ligation events. Thus, detection of contacts through DNA O-MAP will vary in the sampling of DNA-DNA contacts in comparison.”

(4) The study claims this method circumvents the need for transfectable cells. However, the authors go on to describe how they needed tons of cells, now in solution, to get it to work. The intro should be more in line with what was actually accomplished.

We took the reviewers point and have worked to scale down the DNA OMAP experiments while revising this manuscript. As noted in Figure 5, we have been able to scale this work down to work on plates with ~10x fewer cells than with our initial experiments. This is on top of the initial DNA OMAP work in Figure 1 and 2, as well as our additional work in Figure 4, where we are using 30-60 million cells in solutions which is still 10x less material than previous work (PMID: 29735997). Thus, the newest DNA OMAP platform uses ~100x fewer cells than previous work.

(5) Comments like "Compared to other repetitive elements in the human genome...." appear to circumvent the fact that this method is still (apparently) largely limited to repetitive elements. Other than Glopro, which did analyze non-repetitive promoter elements, most comparable methods looked at telomeres. So, this isn't quite the advancement you are implying. Plus, the overlap with telomeric proteins and other studies should be addressed. However, that will be challenging due to the controls used here, discussed above.

As noted above, we have added Figures 4 and 5 to address the reviewer concerns by targeting multiple non-repetitive loci (HOXA and HOXB clusters and a 4.5Mb region straddling X-inactivation center on both the active and inactive X homolog). Targeting the regions around the X-inactivation center shows the potential to perform haplotype-resolved proteome analysis of chromatin interactors.

For the telomeric protein overlap, we tried to do this specifically in Figure 1F, we agree with the reviewer that the controls used dramatically change the proteins considered enriched. The goal of the network analysis was to show (1) that we identify proteins previously observed in telomere proteomic datasets and (2) that we gain a more complete view of proteins based on capturing more known interacting proteins than many previous methods as was noted for the RNA OMAP platform (PMID: 39468212). For example, we observed enrichment of PRPF40A in the telomeric DNA OMAP data. From the Bioplex interactome, PRPF40A was observed to interact with TERF2IP and TERF2, suggesting that through these interactions PRPF40A may colocalize at telomeres. Similarly, we observed enrichment of SF3A1, SF3B1, and SF3B2. The SF3 proteins are known regulators of telomere maintenance (PMID: 27818134), but have not previously been observed in telomeric proteomics datasets, except now in DNA OMAP.

We have added the following text to the Results to clarify these points:

“To benchmark DNA O-MAP, we compared the full set of telomeric proteins to proteins observed in five established telomeric datasets (PICh, C-BERST, CAPLOCUS, CAPTURE, BioID)12,14,16,35,36 (Figure 1F). DNA O-MAP captured both previously observed telomeric interacting proteins (shelterins) as well as telomere associated proteins (ribonucleoproteins). We identified multiple heterogeneous nuclear ribonucleoproteins (hnRNPs) previously annotated as telomere-associated, including HNRNPA1 and HNRNPU. HNRNPA1 has been demonstrated to displace replication protein A (RPA) and directly interact with single-stranded telomeric DNA to regulate telomerase activity37–39. HNRNPU belongs to the telomerase-associated proteome40 where it binds the telomeric G-quadruplex to prevent RPA from recognizing chromosome ends41. We mapped DNA O-MAP enriched telomeric proteins to the BioPlex protein interactome and observed that in addition to capturing proteins from previously observed telomeric datasets (Figure 1F), DNA O-MAP enriched for interactors of previously observed telomeric proteins. Previous data found RBM17 and SNRPA1 at telomeres, and in BioPlex these proteins interact with three SF3 proteins (SF3A1, SF3B1, SF3B2). Though they were not identified in previous telomeric proteome datasets, all three of these SF3 proteins were enriched in the DNA O-MAP telomeric data. Furthermore, through interactions with G-quadruplex binding factors, these SF3 proteins are regulators of telomere maintenance (PMID: 27818134). Taken together, this data supports the effectiveness of DNA O-MAP for sensitively and selectively isolating loci-specific proteomes.”

Reviewer #2 (Public review):

Summary

Liu and MacGann et al. introduce the method DNA O-MAP that uses oligo-based ISH probes to recruit horseradish peroxidase for targeted proximity biotinylation at specific DNA loci. The method's specificity was tested by profiling the proteomic composition at repetitive DNA loci such as telomeres and pericentromeric alpha satellite repeats. In addition, the authors provide proof-of-principle for the capture and mapping of contact frequencies between individual DNA loop anchors.

Strengths

Identifying locus-specific proteomes still represents a major technical challenge and remains an outstanding issue (1). Theoretically, this method could benefit from the specificity of ISH probes and be applied to identify proteomes at non-repetitive DNA loci. This method also requires significantly fewer cells than other ISH- or dCas9-based locus-enrichment methods. Another potential advantage to be tested is the lack of cell line engineering that allows its application to primary cell lines or tissue.

We thank the reviewers for their comments and note that we have followed up on the idea of targeting non-repetitive DNA loci (HOXA and HOXB clusters and a 4.5Mb section of the X chromosome on each homolog) in the revised manuscript (Figures 4 and 5).

Weaknesses

The authors indicate that DNA O-MAP is superior to other methods for identifying locus-specific proteomes. Still, no proof exists that this method could uncover proteomes at non-repetitive DNA loci. Also, there is very little validation of novel factors to confirm the superiority of the technique regarding specificity.

Our primary claim for DNA OMAP is that it requires orders of magnitude fewer cells than previous studies. Based on comments along these lines from both reviewers, we performed DNA OMAP targeting non-repetitive DNA loci (HOXA and HOXB clusters and a 4.5Mb section of the X chromosome on each homolog) in the revised manuscript (Figure 4 and 5). For the X chromosome targeting, we used ~3 million cells per condition with methods that we optimized during revision. When targeting HOXA and HOXA, we were able to identify HDAC3 and TCF12 enrichment at HOXB compared to HOXA as well as ZC3H13 and SMARB1 enrichment at HOXA compared to HOXB, which is consistent with ChIP-seq reads from ENCODE for these proteins (Figure 4C, D). Both the HOXand X chromosome work help to address limitations noted in the Gauchier et al. paper the reviewer notes as both show progress towards overcoming “the major signal-to-noise ratio problem will need to be addressed before they can fully describe the specific composition of single-copy loci”.

The authors first tested their method's specificity at repetitive telomeric regions, and like other approaches, expected low-abundant telomere-specific proteins were absent (for example, all subunits of the telomerase holoenzyme complex). Detecting known proteins while identifying noncanonical and unexpected protein factors with high confidence could indicate that DNA O-MAP does not fully capture biologically crucial proteins due to insufficient enrichment of locus-specific factors. The newly identified proteins in Figure 1E might still be relevant, but independent validation is missing entirely. In my opinion, the current data cannot be interpreted as successfully describing local protein composition.

We analyzed ChIP-seq reads for our HOXA and HOXB (Figure 4C,D) which recapitulate our findings for four of our differentially enriched proteins. We also note that with the addition of the nonrepetitive loci (Figures 4 and 5), we have performed DNA OMAP on seven different targets (telomeres, pericentromeres, mitoDNA, HOXA, HOXB, Xi, and Xa) and identified expected targets at each of these. The consistency of these data, which mirrors the consistency of the RNA implementation of OMAP (PMID: 39468212), reinforces that we can successfully enrich local proteomes at genomic loci.

Finally, the authors could have discussed the limitations of DNA O-MAP and made a fair comparison to other existing methods (2-5). Unlike targeted proximity biotinylation methods, DNA O-MAP requires paraformaldehyde crosslinking, which has several disadvantages. For instance, transient protein-protein interactions may not be efficiently retained on crosslinked chromatin. Similarly, some proteins may not be crosslinked by formaldehyde and thus will be lost during preparation (6).

Based on this critique we have gone back through the manuscript to improve the fairness of our comparisons and expanded the limitations in our discussion section.

To the point about fixation, Schmiedeberg et al., which the reviewer references, does describe crosslinking requiring longer interactions (~5 s). Yet, as featured in reviews, many additional studies have found that “it has been possible to perform ChIP on transcription factors whose interactions with chromatin are known from imaging studies to be highly transient” (Review PMID: 26354429). We note similar results in proteomics analysis in Subbotin and Chait that state that the linkage of lysine-based fixatives like formaldehyde and “glutaraldehyde to reactive amines within the cellular milieu were sufficient to preserve even labile and transient interactions (PMID: 25172955).

(1) Gauchier M, van Mierlo G, Vermeulen M, Dejardin J. Purification and enrichment of specific chromatin loci. Nat Methods. 2020;17(4):380-9.

(2) Dejardin J, Kingston RE. Purification of proteins associated with specific genomic Loci. Cell. 2009;136(1):175-86.

(3) Liu X, Zhang Y, Chen Y, Li M, Zhou F, Li K, et al. In Situ Capture of Chromatin Interactions by Biotinylated dCas9. Cell. 2017;170(5):1028-43 e19.

(4) Villasenor R, Pfaendler R, Ambrosi C, Butz S, Giuliani S, Bryan E, et al. ChromID identifies the protein interactome at chromatin marks. Nat Biotechnol. 2020;38(6):728-36.

(5) Santos-Barriopedro I, van Mierlo G, Vermeulen M. Off-the-shelf proximity biotinylation for interaction proteomics. Nat Commun. 2021;12(1):5015.

(6) Schmiedeberg L, Skene P, Deaton A, Bird A. A temporal threshold for formaldehyde crosslinking and fixation. PLoS One. 2009;4(2):e4636.

Reviewer #3 (Public review):

Significance of the Findings:

The study by Liu et al. presents a novel method, DNA-O-MAP, which combines locus-specific hybridisation with proximity biotinylation to isolate specific genomic regions and their associated proteins. The potential significance of this approach lies in its purported ability to target genomic loci with heightened specificity by enabling extensive washing prior to the biotinylation reaction, theoretically improving the signal-to-noise ratio when compared with other methods such as dCas9-based techniques. Should the method prove successful, it could represent a notable advancement in the field of chromatin biology, particularly in establishing the proteomes of individual chromatin regions - an extremely challenging objective that has not yet been comprehensively addressed by existing methodologies.

Strength of the Evidence:

The evidence presented by the authors is somewhat mixed, and the robustness of the findings appears to be preliminary at this stage. While certain data indicate that DNA-O-MAP may function effectively for repetitive DNA regions, a number of the claims made in the manuscript are either unsupported or require further substantiation. There are significant concerns about the resolution of the method, with substantial biotinylation signals extending well beyond the intended target regions (megabases around the target), suggesting a lack of specificity and poor resolution, particularly for smaller loci.

We thank the reviewers for their comments and note that we have followed up on the idea of targeting non-repetitive DNA loci (HOX clusters and part of the X chromosome) in the revised manuscript (Figures 4 and 5).

Furthermore, comparisons with previous techniques are unfounded since the authors have not provided direct comparisons with the same mass spectrometry (MS) equipment and protocols. Additionally, although the authors assert an advantage in multiplexing, this claim appears overstated, as previous methods could achieve similar outcomes through TMT multiplexing. Therefore, while the method has potential, the evidence requires more rigorous support, comprehensive benchmarking, and further experimental validation to demonstrate the claimed improvements in specificity and practical applicability.

We have made the comparisons as best as possible. In fact, we found it difficult to find examples of recent implementations of many of these methods. Purchasing the exact mass spectrometers or performing every version of chromatin proteomics would be well beyond the scope of this work. On the other hand, OMAP has already generated data for three manuscripts. We are making the claim that using the instrumentation and methods available to us, we were able to reduce the number of cells required to analyze a given genomic loci. We then applied TMT multiplexing to further improve the throughput and perform replicate analyses. To fully validate that one protein exists at one loci and no other would require exhaustive atlasing of protein-genomic interactions which would be well beyond the scope of this single paper. Similarly, ChIP for every target identified to assess an empirical FDR would be well beyond the scope of this work.

Recommendations for the authors:

Reviewing Editor Comments:

In summary, all three reviewers raised major concerns about the limitations of the method, many of which could be resolved by more precise and transparent language about these limitations. If you choose to resubmit a revised version, you should address questions like: What scale does "individual locus" refer to? At what scale can the method map protein-DNA interactions at individual targeted loci, rather than large repetitive domains? What is the estimated false discovery rate for a set of enriched proteins? The eLife assessment for this version of the manuscript is based on reviewer concerns. Note that this assessment can be updated after receiving a response to reviewer comments.

Reviewer #1 (Recommendations for the authors):

(1)The first couple of paragraphs make it sound like your method would exclusively benefit from sample multiplexing with MS-based proteomics. That is a bit misleading. The other stated methods use TMT. They don't use it to compare very different genomic (or compartmental) regions, but there is no reason cberst, glopro or CasID could not.

A good point and we have updated the manuscript to reflect this. While previous methods generally did not use TMT, they could be adapted to do so and, similar to OMAP, improved by the use of more replicates in their analyses.

(2) Please make the colors in 1F for the dataset overlap easier to read. 2 and 4+ are too similar.

We appreciate the comment on making the colors easier to discern. Along these lines we’ve changed the color of “2” to make it easier to distinguish from “4+”.

(3) Label as many dots as legible in your volcano plots.

We’ve labeled a number of proteins that are relevant to the discussion in this paper as well as some additional proteins. We feel that additional labeling would detract from the points that we are trying to make in individual figure panels about groups of proteins, rather than general remodeling of all proteins.

(4) Figure 2E needs a divergent color scheme since it crosses 0. And is it scaled, log-transformed, or both? And compared to what then?

Figure 2E (heatmap) is z-scaled relative protein abundance measurements based on TMTpro reporter ion signal to noise (“s/n”). We have added additional information to the legend to highlight the information that the reviewer points out here. For the color, we are unsure of what is being asked for, as above 0 is red and below 0 is blue.

(5) Unclear what you are implying with "...only 1-2 biological replicates." I would omit or clarify.

Fair point, we have updated the manuscript to omit this section to simplify the introduction.

(6) H2O2 and biotin phenols might be toxic to living organisms. But so is 4% PFA and ISH. I realize you are trying to justify your new approach but you don't need to do it with exaggerated contrasts. This O-MAP is a great approach and probably more likely for people to adopt it because it's DNA ISH based. Plus, with the clinking, you are likely not displacing proteins via Cas9 landing.

We appreciate the reviewer’s comments about adoption and lack of protein displacement. We’ve scaled back on the claims and added more about limitations owing to crosslinking and ISH.

(7) How much genome does the Cent regions take up? You state 500 kb for Telos.

In the text we delineate how large of a region the PanAlpha probes target “The genome-wide binding profile of the pan-alpha probe closely overlaps with centromeres (Figure S1) and covers approximately 35 Mb of the genome according to in silico predictions.” Additionally, we’ve added Table S4 to summarize target locus sizes for all of the included targets.

(8) You seem to be underestimating the lysine labeling. Is that after TMT labeling and analysis? If so, you're already ignoring what couldn't be seen. I don't think it's that important but you included it, so please describe clearly why it's an issue and how much of an issue it is. How does that relate to lit values? And it's not just TMTpro, it's any lysine labeler.

We appreciate the reviewers point about specifying the reasoning and the lack of clarity around overall lysine labeling. That 1.38% is the number of peptides with remainder modifications due to formaldehyde crosslinking. For overall acylation of lysines with TMT labels, we generally expect (and achieve) >97% labeling of lysines with TMT reagents as the Kuster and Carr labs nicely demonstrated across a range of labeling conditions (PMID: 30967486).

Decrosslinking is a critical step generally for proteomics workflows on fixed or FFPE tissues and thus we sought to explore whether we could achieve sufficiently low residual lysine alkylation to enable protein quantitation by TMTpro reagents (or any lysine labeler, as the reviewer notes). For TMTpro-based methods on peptides, this is less of a concern generally as protease cleavage frees new primary amines at the N-termini of peptides which can be labeled for quantitation. But in part since we are describing a proteomics method on fixed tissues we wanted to share these data and the potential inclusion of residual fixation modifications for readers to potentially take into consideration when performing this method.

Reviewer #3 (Recommendations for the authors):

Liu et al. describe an original locus labelling approach that enables the isolation of specific genomic regions and their associated proteins. I have mixed views on this work, which, in my opinion, remains preliminary at this stage. Establishing the proteome of a single chromatin region is one of the most complex challenges in chromatin biology, as extensively discussed in Gauchier et al. (2020). Any breakthrough towards this goal is of significant interest to the community, making this manuscript potentially compelling. Indeed, some data suggest that the method works for repetitive DNA to some extent. However, much of the data is not very convincing, and in the case of small DNA targets, it argues against the use of DNA-O-MAP.

In contrast to existing methods, DNA-O-MAP combines locus-specific hybridisation in situ (using affordable oligonucleotides) with proximity biotinylation. A major advantage of this strategy over other locus-specific biotinylation methods is the possibility of extensively washing excess or non-specifically hybridised probes before the biotinylation reaction, theoretically limiting biotinylation to the target region and thus significantly enhancing the signal-to-noise ratio. Other methods involving proximity biotinylation, such as targeted dCas9, do not have this capacity, meaning biotinylation occurs not only at the locus where a small fraction of dCas9 molecules is targeted but also around non-bound dCas9 molecules (representing the vast majority of dCas9 expressed in a given cell). This aspect potentially represents an interesting advance.

We thank the reviewer for their thoughts and critiques, which we hope have in part relieved concerns pertaining to limitation on repetitive elements. To the latter points, we confirmed this with new specificity analysis that showed labeling to be highly specific to a given probe locus (Figure S3).

Below, I outline the significant issues:

The manuscript implies that DNA-O-MAP has better sensitivity than earlier techniques like CAPTURE, GLOPRO, or PICh. The authors state that PICh uses one trillion cells (which I doubt is accurate), and other methods require 300 million cells, whereas DNA-O-MAP uses only 60 million cells, suggesting the latter is more feasible. However, these earlier experiments were conducted almost 15 and 6 years ago, when mass spectrometry (MS) sensitivity was considerably lower than that of current instruments. The authors cannot know whether the proteome obtained by previous methods using 60 million cells, but analysed with current MS technology, would yield results inferior to those of DNA-O-MAP. Unless the authors directly compare these methods using the same number of cells and identical MS setups, I find their argument unjustified and misleading.

Based on the instrumentation listed, we actually do have a good idea of how sensitivity changes may have affected identifications and overall sensitivity. For example, the CASPEX data was collected on an Orbitrap Fusion Lumos, while our data was collected on an Orbitrap Fusion Eclipse. From our work characterizing these two instruments during the Eclipse development (PMID: 32250601), we do actually know that the ion optics improvements boosted sensitivity of the Eclipse used in our work compared to the Lumos by ~50%, meaning if GLOPRO was run on an Eclipse it would still require >200 million cells per replicate for input.

It is suggested that DNA-O-MAP is capable of 'multiplexing', whereas previous methods are not. This statement is also misleading. As I understand it, the targeted regions do not originate from a common pool of cells. Instead, TMT multiplexing only occurs after each group of cells has been independently labelled (Telo, Centro, Mito, control). Therefore, previous methods could also perform multiplexing with TMT. Moreover, it is unclear how each proteome was compared: one would expect many more proteins from centromeres than from telomeres (I am unsure about the number of mitochondria in these cells) since these regions are significantly larger than telomeres (possibly 10 to 100 times larger?). Have the authors attempted to normalise their proteomics data to the size (concatenated) of each target? This is particularly relevant when comparing histone enrichment at chromatin regions of differing sizes.

We agree with the reviewers that this was overstated. In fact the GLOPRO paper notes that they performed a MYC analysis with a previous generation of TMT that could multiplex 10 samples. We have amended the manuscript to be more specific in those contexts. As stated in the methods section, “Samples were column normalized for total protein concentration”, to account for the amount of protein and size of the different targets.

Figure 1C shows streptavidin dots resembling telomeres. To substantiate this claim, simultaneous immunofluorescence with a telomere-specific protein (e.g., TRF1 or TRF2) is required. It is currently unknown whether all or only a subset of telomeres are targeted by DNA-O-MAP, and it is also unclear if some streptavidin foci are non-telomeric. Quantification is needed to indicate the reproducibility of the labelling (the same comment applies to the centromere probes later in the manuscript; an immunofluorescence assay with CENPB would be informative, alongside quantifications).

We understand the reviewer’s concern about specificity and reproducibility of DNA-O-MAP. To address this we have added analysis showing the efficiency and specificity of our FISH and biotin labeling for Telomere, PanAlpha, and Mitochondria targeting oligos (Figure S3). We found that biotin deposition was highly specific to the intended targets with an average across the three probes of 98% specificity.

Perhaps more importantly, the authors suggest that it may be possible to enrich proteins that are not necessarily present at the target locus but are instead in spatial proximity (e.g., RNA polymerase I subunits enriched upon centromere targeting). Does this not undermine the purpose of retrieving locus-specific proteomes?

The goal of DNA OMAP is to identify a local neighborhood of proteins around a specific genomic loci, similar to GLOPRO. As we note in the work presented in Figure 4 and 5 now, these neighborhoods are inherently interesting for comparison of quantitative changes that occur around a genomic locus.

Possibly related to the previous issue, when DNA-O-MAP is used to assess DNA-DNA interactions, probes covering regions of 20-25 kb are employed. Therefore, one would expect these regions to be significantly biotinylated compared to flanking regions. However, Genome Browser screenshots indicate extensive biotinylation signals spanning several megabases around the 20-25 kb targets. If the method were highly resolutive, the target region would be primarily enriched, with possibly discrete lower enrichment at distant interacting regions. The lack of discrete enrichment suggests poor resolution, likely due to the likely large scale of proximity biotinylation. This compromises the effectiveness of DNA-O-MAP, especially if it is intended to target small loci with complex sequences. Could the authors quantify the absolute number of reads from the target region compared to those from elsewhere in the genome (both megabases around the locus and other chromosomes, where many co-enriched regions seem to exist)? This would provide insights into both enrichment and specificity.

Thanks for this suggestion, we have included a new Figure S8 to look at normalized read depth as a function of distance from the genomic target. The resolution of DNA OMAP, like all peroxidase mediated proximity labeling methods, is not dependent on the sequence length of the DNA region, but the 30-40nm of physical space around the HRP molecule that is targeted to the genomic loci. 

Minor Issues:

(1) Page 3, second paragraph: It is unclear why probes producing a visible signal in situ necessarily translates to their ability to retrieve a specific proteome.

We have revised the manuscript to de-emphasize the visible signal aspect of probe targeting and re-emphasize our initial point that the number of probes needed to properly target unique regions makes the use of locked nucleic acid probes cost-prohibitive. The basic point though, we and others previously showed with RNA OMAP (PMID: 39468212) and Apex/proximity labeling strategies, the ability to deposit biotin and visualize generally directly translates to recovery of proximally labeled proteins (PMID: 26866790).

(2) Page 3, last paragraph: "to reach a higher degree of enrichment...": Has it been demonstrated that direct protein biotinylation provides higher enrichment of relevant proteins? Certainly, there is higher enrichment of proteins, but whether they are relevant is another matter.

Our point here was that the methods using direct protein biotinylation have higher levels of enrichment and thus require less cells than the previously mentioned PICh method, which is why we wrote the following: “In the case of GLoPro, APEX-based proximity labeling enhanced protein detection sensitivity, reducing the input required for each replicate analysis to ~300 million cells—a 10-fold reduction in cell input compared to PICh which used 3 billion cells.”

Regarding if these proteins are relevant or not, we show enrichment of known proteins that are critical to the function of their occupied genomic region at telomeres and centromeres. Additionally, we’ve made added quantitative comparisons to assess relevance in our analysis of Hox and our targeted region of the X chromosome through comparisons to ChIP data at these regions. The improved enrichment that we’ve established in our initial submission as well as in the updated version also means that we can further scale down the number of cells required.

(3) Figure 2B is misleading; it appears as though all three regions are targeted in the same cell, suggesting true multiplexing, which, I believe, is not the case.

To avoid any potential confusion about how the samples were derived we’ve updated this figure panel to show three separate cells, each with a different region being targeted.

(3) If I understand correctly, the 'no probe' control should primarily retrieve endogenously biotinylated proteins (carboxylases), which are mainly found in mitochondria. Why does the Pearson clustering in Supplementary Figure 2 not place this control proteome closer to the mitochondrial proteome?

Under the assumption that the ~10 carboxylases are biotinylated at the same levels in all cells, yet the proportion of these carboxylases compared to all enriched proteins for a given target is markedly reduced. Thus, as a proportion of the enriched proteome we note in Figure S4 that mitochondrial DNA OMAP enriches proteins besides the carboxylases. We believe this explains why the ‘no probe’ sample can be clearly separated along PC2 in Figure 2D.

(4) Was CENPA enriched in the centromere DNA-O-MAP? If not, have the authors scaled up (e.g., with ten times more cells) to see if the local proteome becomes deeper and detects relevant low-abundance proteins like CENPA or HJURP? This would be very informative.

We did not observe CENPA, and we had originally contemplated the experiment the reviewer suggested, but noted that CENPA has only two tryptic peptides (>7 AA, <35AA), and they are both in the commonly phosphorylated region of the protein. Rather than scale up these experiments, we decided to attempt DNA OMAP on the non-repetitive locus experiments.

(5) Using a few million cells, I do not see how the starting chromatin amount could range from 0.5 to 7 mg, as shown in Figures 2 and 3. How were these figures calculated? One diploid cell contains approximately 6 pg of DNA/chromatin, which means one billion cells represent about 6 mg of DNA/chromatin (a typical measurement for these methods).

Thanks to the reviewer for catching this, that should have been the total lysate amount, not chromatin mass. We have corrected Figures 2 and 3.

(6) Figure S1: There is no indication of the metrics used for the shades of red.

We have added a gradient legend to depict this.

(7) What is the purpose of HCl in the experiment?

HCl treatment was done to reduce autofluorescence for imaging (PMID: 39548245).

(8) I could not find the MS dataset on the server using the provided accession number (PDX054080).

Thank you for pointing this out, we have confirmed the dataset is public now and added the new datasets for the Xi/Xa and Hox studies. We also note that the accession should be “PXD054080”

(9) Why desthiobiotin instead of biotin?

We have tested both; desthiobiotin was helpful to reduce adsorption to surfaces. Either biotin or desthiobiotin can be used, though, for OMAP.

Author response:

The following is the authors’ response to the original reviews

General Statements

We are delighted that all reviewers found our manuscript to be a technical advance by providing a much sought after method to arrest budding yeast cells in metaphase of mitosis or both meiotic metaphases. The reviewers also valued our use of this system to make new discoveries in two areas. First, we provided evidence that the spindle checkpoint is intrinsically weaker in meiosis I and showed that this is due to PP1 phosphatase. Second, we determined how the composition and phosphorylation of the kinetochore changes during meiosis, providing key insights into kinetochore function and providing a rich dataset for future studies.

The reviewers also made some extremely helpful suggestions to improve our manuscript, which we will have now implemented:

(1) Improvements to the discussion. Following the recommendation of the reviewers recommended we have focused our discussion on the novel findings of the manuscript and drawn out some key points of interest that deserve more attention.

(2) We added a new Figure 5 to help interpret the mass spectrometry data, to address Reviewer #3, point 4.

(3) We added a new additional control experiment to address the minor point 1 from reviewer #3. Our experiment to confirm that SynSAC relies on endogenous checkpoint proteins was missing the cell cycle profile of cells where SynSAC was not induced for comparison. We have performed this experiment and the new data is show as part of a new Figure 2.

(4) We included representative images of spindle morphology as requested by Reviewer #1, point 2 in Figure1.

Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity):

These authors have developed a method to induce MI or MII arrest. While this was previously possible in MI, the advantage of the method presented here is it works for MII, and chemically inducible because it is based on a system that is sensitive to the addition of ABA. Depending on when the ABA is added, they achieve a MI or MII delay. The ABA promotes dimerizing fragments of Mps1 and Spc105 that can't bind their chromosomal sites. The evidence that the MI arrest is weaker than the MII arrest is convincing and consistent with published data and indicating the SAC in MI is less robust than MII or mitosis. The authors use this system to find evidence that the weak MI arrest is associated with PP1 binding to Spc105. This is a nice use of the system.

The remainder of the paper uses the SynSAC system to isolate populations enriched for MI or MII stages and conduct proteomics. This shows a powerful use of the system but more work is needed to validate these results, particularly in normal cells.

Overall the most significant aspect of this paper is the technical achievement, which is validated by the other experiments. They have developed a system and generated some proteomics data that maybe useful to others when analyzing kinetochore composition at each division. Overall, I have only a few minor suggestions.

We appreciate the reviewers’ support of our study.

(1) In wild-type - Pds1 levels are high during M1 and A1, but low in MII. Can the authors comment on this? In line 217, what is meant by "slightly attenuated? Can the authors comment on how anaphase occurs in presence of high Pds1? There is even a low but significant level in MII.

The higher levels of Pds1 in meiosis I compared to meiosis II has been observed previously using immunofluorescence and live imaging[1–3]. Although the reasons are not completely clear, we speculate that there is insufficient time between the two divisions to re-accumulate Pds1 prior to separase re-activation. We added the following sentence at Line 218: “ In wild-type cells, Pds1 levels are higher in meiosis I than in meiosis II, likely because the interval between the divisions is too short to allow Pds1 reaccumulation [1,2,4]. This pattern was also observed in SynSAC strains in the absence of ABA (Figure 3A).

We agree “slightly attenuated” was confusing and we have re-worded this sentence to read “However, ABA addition at the time of prophase release resulted in Pds1^securin stabilisation throughout the time course, consistent with delays in both metaphase I and II”. (Line 225).

We do not believe that either anaphase I or II occur in the presence of high Pds1. Western blotting represents the amount of Pds1 in the population of cells at a given time point. The time between meiosis I and II is very short even when treated with ABA. For example, in Figure 2B (now Figure 3B), spindle morphology counts show that at 105 minutes, 40% of cells had anaphase I spindles (and will be Pds1 negative), while ~20% had metaphase I and ~20% metaphase II spindles (and will be Pds1 positive). In contrast, due to the better efficiency of the meiosis II arrest, anaphase II hardly occurs at all in these conditions, since anaphase II spindles (and the second nuclear division) are observed at very low frequency (maximum 10%) from 165 minutes onwards. Instead, metaphase II spindles partially or fully breakdown, without undergoing anaphase extension. Taking Pds1 levels from the western blot and the spindle data together leads to the conclusion that at the end of the time-course, these cells are biochemically in metaphase II, but unable to maintain a robust spindle. Spindle collapse is also observed in other situations where meiotic exit fails, and potentially reflects an uncoupling of the cell cycle from the programme governing gamete differentiation[3,5,6]. We re-wrote this section as follows. (Line 222).

“Note that Pds1 levels do not fully decline in this population-based analysis as the short duration of meiotic stages results in a mixed-stage population. For example, at the anaphase I peak (90 minutes) around 30% of cells remain in prior stages in which Pds1 levels are expected to be high. However, ABA addition at the time of prophase release resulted in Pds1^securin stabilisation throughout the time course, consistent with delays in both metaphase I and metaphase II. (Figure 3B). Anaphase I spindles nevertheless appeared with delayed kinetics, peaking at ~40% at 105 min. Concurrently, ~40% of cells remained in metaphase I or II and were therefore Pds1-positive, accounting for the persistent Pds1 signal on the western blot. In contrast, anaphase II spindles are observed at low frequency (maximum 10%) from 165 minutes onwards because metaphase II spindles give way to post-meiotic spindles, without undergoing anaphase II extension (Figure 1D).”

(2) The figures with data characterizing the system are mostly graphs showing time course of MI and MII. There is no cytology, which is a little surprising since the stage is determined by spindle morphology. It would help to see sample sizes (ie. In the Figure legends) and also representative images. It would also be nice to see images comparing the same stage in the SynSAC cells versus normal cells. Are there any differences in the morphology of the spindles or chromosomes when in the SynSAC system?

We have now included representative images as Figure 1D along with a schematic Figure 1C. This shows that there are no differences in spindle morphology or nuclei (chromosomes cannot be observed at this resolution), except of course the number of cells with a particular spindle morphology at a given time. We added the following text confirming that there is no change in spindle morphology (Line 174). “We scored spindle morphology after anti-tubulin immunofluorescence to determine cell cycle stage (Figure 1C). Prophase, metaphase I, anaphase I, metaphase II, anaphase II and post-meiotic spindles appeared successively over the timecourse in both the absence and presence of ABA (Figure 1D). While SynSAC dimerisation did not alter characteristic spindle morphologies, it changed their distribution over time.”

The number of cells scored (at least 100 cells per timepoint) is given in the figure legends.

(3) A possible criticism of this system could be that the SAC signal promoting arrest is not coming from the kinetochore. Are there any possible consequences of this? In vertebrate cells, the RZZ complex streams off the kinetochore. Yeast don't have RZZ but this is an example of something that is SAC dependent and happens at the kinetochore. Can the authors discuss possible limitations such as this? Does the inhibition of the APC effect the native kinetochores? This could be good or bad. A bad possibility is that the cell is behaving as if it is in MII, but the kinetochores have made their microtubule attachments and behave as if in anaphase.

In our view, the fact that SynSAC does not come from kinetochores is a major advantage as this allows the study of the kinetochore in an unperturbed state. It is also important to note that the canonical checkpoint components are all still present in the SynSAC strains, and perturbations in kinetochore-microtubule interactions would be expected to mount a kinetochore-driven checkpoint response as normal. Indeed, it would be interesting in future work to understand how disrupting kinetochore-microtubule attachments alters kinetochore composition (presumably checkpoint proteins will be recruited) and phosphorylation but this is beyond the scope of this work. In terms of the state at which we are arresting cells – this is a true metaphase because cohesion has not been lost but kinetochore-microtubule attachments have been established. This is evident from the enrichment of microtubule regulators but not checkpoint proteins in the kinetochore purifications from metaphase I and II. While this state is expected to occur only transiently in yeast, since the establishment of proper kinetochore-microtubule attachments triggers anaphase onset, the ability to capture this properly bioriented state will be extremely informative for future studies. We acknowledge however that we cannot completely rule out unwanted effects of the system, as in any synchronisation system, and where possible findings with the system should be backed up with an orthogonal approach. We appreciate the reviewers’ insight in highlighting these interesting discussion points and we have re-written the relevant paragraph in the discussion, starting line 545.

Reviewer #1 (Significance):

These authors have developed a method to induce MI or MII arrest. While this was previously possible in MI, the advantage of the method presented here is it works for MII, and chemically inducible because it is based on a system that is sensitive to the addition of ABA. Depending on when the ABA is added, they achieve a MI or MII delay. The ABA promotes dimerizing fragments of Mps1 and Spc105 that can't bind their chromosomal sites. The evidence that the MI arrest is weaker than the MII arrest is convincing and consistent with published data and indicating the SAC in MI is less robust than MII or mitosis. The authors use this system to find evidence that the weak MI arrest is associated with PP1 binding to Spc105. This is a nice use of the system.

The remainder of the paper uses the SynSAC system to isolate populations enriched for MI or MII stages and conduct proteomics. This shows a powerful use of the system but more work is needed to validate these results, particularly in normal cells.

Overall the most significant aspect of this paper is the technical achievement, which is validated by the other experiments. They have developed a system and generated some proteomics data that maybe useful to others when analyzing kinetochore composition at each division.

We appreciate the reviewer’s enthusiasm for our work.

Reviewer #2 (Evidence, reproducibility and clarity):

The manuscript submitted by Koch et al. describes a novel approach to collect budding yeast cells in metaphase I or metaphase II by synthetically activating the spinde checkpoint (SAC). The arrest is transient and reversible. This synchronization strategy will be extremely useful for studying meiosis I and meiosis II, and compare the two divisions. The authors characterized this so-named syncSACapproach and could confirm previous observations that the SAC arrest is less efficient in meiosis I than in meiosis II. They found that downregulation of the SAC response through PP1 phosphatase is stronger in meiosis I than in meiosis II. The authors then went on to purify kinetochore-associated proteins from metaphase I and II extracts for proteome and phosphoproteome analysis. Their data will be of significant interest to the cell cycle community (they compared their datasets also to kinetochores purified from cells arrested in prophase I and -with SynSAC in mitosis).

I have only a couple of minor comments:

(1) I would add the Suppl Figure 1A to main Figure 1A. What is really exciting here is the arrest in metaphase II, so I don't understand why the authors characterize metaphase I in the main figure, but not metaphase II. But this is only a suggestion.

Thanks for the suggestion. We agree and have moved the data for both meiosis I and meiosis II to make a new main Figure 2.

(2) Line 197, the authors state: ...SyncSACinduced a more pronounced delay in metaphase II than in metaphase I. However, line 229 and 240 the auhtors talk about a "longer delay in metaphase <i compared to metaphase II"... this seems to be a mix-up.

Thank you for pointing this out, this is indeed a typo and we have corrected it.

(3) The authors describe striking differences for both protein abundance and phosphorylation for key kinetochore associated proteins. I found one very interesting protein that seems to be very abundant and phosphorylated in metaphase I but not metaphase II, namely Sgo1. Do the authors think that Sgo1 is not required in metaphase II anymore? (Top hit in suppl Fig 8D).

This is indeed an interesting observation, which we plan to investigate as part of another study in the future. Indeed, data from mouse indicates that shugoshin-dependent cohesin deprotection is already absent in meiosis II in mouse oocytes7, though whether this is also true in yeast is not known. Furthermore, this does not rule out other functions of Sgo1 in meiosis II (for example promoting biorientation). We have included a paragraph in the discussion in the section starting line 641.

Reviewer #2 (Significance):

The technique described here will be of great interest to the cell cycle community. Furthermore, the authors provide data sets on purified kinetochores of different meiotic stages and compare them to mitosis. This paper will thus be highly cited, for the technique, and also for the application of the technique.

Reviewer #3 (Evidence, reproducibility and clarity):

In their manuscript, Koch et al. describe a novel strategy to synchronize cells of the budding yeast Saccharomyces cerevisiae in metaphase I and metaphase II, thereby facilitating comparative analyses between these meiotic stages. This approach, termed SynSAC, adapts a method previously developed in fission yeast and human cells that enables the ectopic induction of a synthetic spindle assembly checkpoint (SAC) arrest by conditionally forcing the heterodimerization of two SAC components upon addition of the plant hormone abscisic acid (ABA). This is a valuable tool, which has the advantage that induces SAC-dependent inhibition of the anaphase promoting complex without perturbing kinetochores. Furthermore, since the same strategy and yeast strain can be also used to induce a metaphase arrest during mitosis, the methodology developed by Koch et al. enables comparative analyses between mitotic and meiotic cell divisions. To validate their strategy, the authors purified kinetochores from meiotic metaphase I and metaphase II, as well as from mitotic metaphase, and compared their protein composition and phosphorylation profiles. The results are presented clearly and in an organized manner.

We are grateful to the reviewer for their support.

Despite the relevance of both the methodology and the comparative analyses, several main issues should be addressed:

(1) In contrast to the strong metaphase arrest induced by ABA addition in mitosis (Supp. Fig. 2), the SynSAC strategy only promotes a delay in metaphase I and metaphase II as cells progress through meiosis. This delay extends the duration of both meiotic stages, but does not markedly increase the percentage of metaphase I or II cells in the population at a given timepoint of the meiotic time course (Fig. 1C). Therefore, although SynSAC broadens the time window for sample collection, it does not substantially improve differential analyses between stages compared with a standard NDT80 prophase block synchronization experiment. Could a higher ABA concentration or repeated hormone addition improve the tightness of the meiotic metaphase arrest?

For many purposes the enrichment and extended time for sample collection is sufficient, as we demonstrate here. However, as pointed out by the reviewer below, the system can be improved by use of the 4A-RASA mutations to provide a stronger arrest (see our response below). We did not experiment with higher ABA concentrations or repeated addition since the very robust arrest achieved with the 4A-RASA mutant deemed this unnecessary.

(2) Unlike the standard SynSAC strategy, introducing mutations that prevent PP1 binding to the SynSAC construct considerably extended the duration of the meiotic metaphase arrests. In particular, mutating PP1 binding sites in both the RVxF (RASA) and the SILK (4A) motifs of the Spc105(1-455)-PYL construct caused a strong metaphase I arrest that persisted until the end of the meiotic time course (Fig. 3A). This stronger and more prolonged 4A-RASA SynSAC arrest would directly address the issue raised above. It is unclear why the authors did not emphasize more this improved system. Indeed, the 4A-RASA SynSAC approach could be presented as the optimal strategy to induce a conditional metaphase arrest in budding yeast meiosis, since it not only adapts but also improves the original methods designed for fission yeast and human cells. Along the same lines, it is surprising that the authors did not exploit the stronger arrest achieved with the 4A-RASA mutant to compare kinetochore composition at meiotic metaphase I and II.

We agree that the 4A-RASA mutant is the best tool to use for the arrest and going forward this will be our approach. We collected the proteomics data and the data on the SynSAC mutant variants concurrently, so we did not know about the improved arrest at the time the proteomics experiment was done. Because very good arrest was already achieved with the unmutated SynSAC construct, we could not justify repeating the proteomics experiment which is a large amount of work using significant resources. We highlighted the potential of using the 4A-RASA variant more strongly as follows:

Line 312, Results:

“These findings also indicate that spc105^(1-455)-4A-RASA is the preferred SynSAC variant, particularly where metaphase I arrest is the goal.”

Line 598, Discussion: “Finally, the stronger and more prolonged SynSAC arrest obtained using the PP1 binding site mutant spc105^(1-455)-4A-RASA prompts its consideration as an alternative tool for future studies, particularly where meiosis I arrest is important. At the time of performing the kinetochore immunoprecipitations, these mutations were not yet available but, as we have demonstrated, wild type SynSAC protein fragments nevertheless yielded sufficiently enriched populations of metaphase I and II cells to allow reliable detection of stage-specific kinetochore proteins and phosphorylations. Going forward, however, we consider SynSAC-4A-RASA to be the optimal tool for inducing metaphase arrests.”

(3) The results shown in Supp. Fig. 4C are intriguing and merit further discussion. Mitotic growth in ABA suggest that the RASA mutation silences the SynSAC effect, yet this was not observed for the 4A or the double 4A-RASA mutants. Notably, in contrast to mitosis, the SynSAC 4A-RASA mutation leads to a more pronounced metaphase I meiotic delay (Fig. 3A). It is also noteworthy that the RVAF mutation partially restores mitotic growth in ABA. This observation supports, as previously demonstrated in human cells, that Aurora B-mediated phosphorylation of S77 within the RVSF motif is important to prevent PP1 binding to Spc105 in budding yeast as well.

We agree these are intriguing findings that highlight key differences as to the wiring of the spindle checkpoint in meiosis and mitosis and potential for future studies, however, currently we can only speculate as to the underlying cause. The effect of the RASA mutation in mitosis is unexpected and unexplained. However, the fact that the 4A-RASA mutation causes a stronger delay in meiosis I compared to mitosis can be explained by a greater prominence of PP1 phosphatase in meiosis. Indeed, our data (now Figure 7A) show that the PP1 phosphatase Glc7 and its regulatory subunit Fin1 are highly enriched on kinetochores at all meiotic stages compared to mitosis.

We agree that the improved growth of the RVAF mutant is intriguing, along with the reduced metaphase I delay, which together point to a role of Aurora B-mediated phosphorylation also in S. cerevisiae, though previous work has not supported such a role [8].

We have re-written and expanded the paragraph in the discussion related to the mutation of the RVSF motif starting line 564 to reflect these points.

(4) To demonstrate the applicability of the SynSAC approach, the authors immunoprecipitated the kinetochore protein Dsn1 from cells arrested at different meiotic or mitotic stages, and compared kinetochore composition using data independent acquisition (DIA) mass spectrometry. Quantification and comparative analyses of total and kinetochore protein levels were conducted in parallel for cells expressing either FLAG-tagged or untagged Dsn1 (Supp. Fig. 7A-B). To better detect potential changes, protein abundances were next scaled to Dsn1 levels in each sample (Supp. Fig. 7C-D). However, it is not clear why the authors did not normalize protein abundance in the immunoprecipitations from tagged samples at each stage to the corresponding untagged control, instead of performing a separate analysis. This would be particularly relevant given the high sensitivity of DIA mass spectrometry, which enabled quantification of thousands of proteins. Furthermore, the authors compared protein abundances in tagged-samples from mitotic metaphase and meiotic prophase, metaphase I and metaphase II (Supp. Fig. 7E-F). If protein amounts in each case were not normalized to the untagged controls, as inferred from the text (lines 333 to 338), the observed differences could simply reflect global changes in protein expression at different stages rather than specific differences in protein association to kinetochores.

While we agree with the reviewer that at first glance, normalising to no tag appears to be the most appropriate normalisation, in practice there is very low background signal in the no tag sample which means that any random fluctuations have a big impact on the final fold change used for normalisation. This approach therefore introduces artefacts into the data rather than improving normalisation.

To provide reassurance that our kinetochore immunoprecipitations are specific, and that the background (no tag) signal is indeed very low, we have provided a new figure showing the volcanos comparing kinetochore purifications at each stage with their corresponding no tag control (Figure 5).

It is also important to note that our experiment looks at relative changes of the same protein over time, which we expect to be relatively small in the whole cell lysate. We previously documented proteins that change in abundance in whole cell lysates throughout meiosis9. In this study, we found that relatively few proteins significantly change in abundance. We added a sentence to this effect in the discussion (Line 632). “Although some variation could reflect global changes in protein abundance during meiosis, we previously found that only a few proteins undergo dynamic abundance changes during the meiotic divisions [9], so this is unlikely to fully explain the kinetochore composition differences observed.”

Our aim in the current study was to understand how the relative composition of the kinetochore changes and for this, we believe that a direct comparison to Dsn1, a central kinetochore protein which we immunoprecipitated is the most appropriate normalisation.

(5) Despite the large amount of potentially valuable data generated, the manuscript focuses mainly on results that reinforce previously established observations (e.g., premature SAC silencing in meiosis I by PP1, changes in kinetochore composition, etc.). The discussion would benefit from a deeper analysis of novel findings that underscore the broader significance of this study.

We strongly agree with this point and we have re-framed the discussion to focus on the novel findings, as also raised by the other reviewers and noted above.

Finally, minor concerns are:

(1) Meiotic progression in SynSAC strains lacking Mad1, Mad2 or Mad3 is severely affected (Fig. 1D and Supp. Fig. 1), making it difficult to assess whether, as the authors state, the metaphase delays depend on the canonical SAC cascade. In addition, as a general note, graphs displaying meiotic time courses could be improved for clarity (e.g., thinner data lines, addition of axis gridlines and external tick marks, etc.).

We added the requested data, which is now part of Figure 2. This now clearly shows that mad2 and mad3 mutants have very similar meiotic cell cycle profiles in the SynSAC background whether or not ABA is added. Please note that we removed the mad1 mutant from this analysis as technical difficulties prevented the strain from entering meiosis well.

We have improved graphs throughout, as suggested: data lines are thinner, axis gridlines and external grid marks are included. We added an arrow to indicate the time of ethanol/ABA addition.

(2) Spore viability following SynSAC induction in meiosis was used as an indicator that this experimental approach does not disrupt kinetochore function and chromosome segregation. However, this is an indirect measure. Direct monitoring of genome distribution using GFP-tagged chromosomes would have provided more robust evidence. Notably, the SynSAC mad3Δ mutant shows a slight viability defect, which might reflect chromosome segregation defects that are more pronounced in the absence of a functional SAC.

Spore viability is a much more sensitive way of analysing segregation defects that GFP-labelled chromosomes. This is because GFP labelling allows only a single chromosome to be followed. On the other hand, if any of the 16 chromosomes mis-segregate in a given meiosis this would result in one or more aneuploid spores in the tetrad, which are typically inviable. The fact that spore viability is not significantly different from wild type in this analysis indicates that there are no major chromosome segregation defects in these strains, and we therefore we think this experiment unnecessary.

(3) It is surprising that, although SAC activity is proposed to be weaker in metaphase I, the levels of CPC/SAC proteins seem to be higher at this stage of meiosis than in metaphase II or mitotic metaphase (Fig. 4A-B).

We speculate that the challenge in biorienting homologs which are held together by chiasmata, rather than back-to-back kinetochores results in a greater requirement for dynamic error correction in meiosis I. Interestingly, the data with the RASA mutant also point to increased PP1 activity in meiosis I, and we additionally observed increased levels of PP1 (Glc7 and Fin1) on meiotic kinetochores, consistent with the idea that cycles of error correction and silencing are elevated in meiosis I. We have re-written and expanded the discussion section starting line 565 to reflect these points.

(4) Although a more detailed exploration of kinetochore composition or phosphorylation changes is beyond the scope of the manuscript, some key observations could have been validated experimentally (e.g., enrichment of proteins at kinetochores, phosphorylation events that were identified as specific or enriched at a certain meiotic stage, etc.).

We agree that this is beyond the scope of the current study but will form the start of future projects from our group, and hopefully others.

(5) Several typographical errors should be corrected (e.g., "Kinvetochores" in Fig. 4 legend, "250uM ABA" in Supp. Fig. 1 legend, etc.)

Thank you for pointing these out, they have been corrected and we have carefully proofread the manuscript.

Reviewer #3 (Significance):

Koch et al. describe a novel methodology, SynSAC, to synchronize budding yeast cells in metaphase I or metaphase II during meiosis, as well and in mitotic metaphase, thereby enabling differential analyses among these cell division stages. Their approach builds on prior strategies originally developed in fission yeast and human cells models to induce a synthetic spindle assembly checkpoint (SAC) arrest by conditionally forcing the heterodimerization of two SAC proteins upon addition of abscisic acid (ABA). The results from this manuscript are of special relevance for researchers studying meiosis and using Saccharomyces cerevisiae as a model. Moreover, the differential analysis of the composition and phosphorylation of kinetochores from meiotic metaphase I and metaphase II adds interest for the broader meiosis research community. Finally, regarding my expertise, I am a researcher specialized in the regulation of cell division.

References

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Author response:

General Statements

We thank all three reviewers for their time taken to provide valuable feedback on our manuscript, and for appreciating the quality and usefulness of our data and results presented in our study. We have improved the manuscript based on their suggestions and provide a detailed, point-by-point response below.

Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity):

The authors have a longstanding focus and reputation on single cell sequencing technology development and application. In this current study, the authors developed a novel single-cell multi-omic assay termed "T-ChIC" so that to jointly profile the histone modifications along with the full-length transcriptome from the same single cells, analyzed the dynamic relationship between chromatin state and gene expression during zebrafish development and cell fate determination. In general, the assay works well, the data look convincing and conclusions are beneficial to the community.

Thank you for your positive feedback.

There are several single-cell methodologies all claim to co-profile chromatin modifications and gene expression from the same individual cell, such as CoTECH, Paired-tag and others. Although T-ChIC employs pA-Mnase and IVT to obtain these modalities from single cells which are different, could the author provide some direct comparisons among all these technologies to see whether T-ChIC outperforms?

In a separate technical manuscript describing the application of T-ChIC in mouse cells (Zeller, Blotenburg et al 2024, (Zeller et al., 2024)), we have provided a direct comparison of data quality between T-ChIC and other single-cell methods for chromatin-RNA co-profiling (Please refer to Fig. 1C,D and Fig. S1D, E, of the preprint). We show that compared to other methods, T-ChIC is able to better preserve the expected biological relationship between the histone modifications and gene expression in single cells.

In current study, T-ChIC profiled H3K27me3 and H3K4me1 modifications, these data look great. How about other histone modifications (eg H3K9me3 and H3K36me3) and transcription factors?

While we haven’t profiled these other modifications using T-ChIC in Zebrafish, we have previously published high quality data on these histone modifications using the sortChIC method, on which T-ChIC is based (Zeller, Yeung et al 2023)(Zeller et al., 2022). In our comparison, we find that histone modification profiles between T-ChIC and sortChIC are very similar (Fig. S1C in Zeller, Blotenburg et al 2024). Therefore the method is expected to work as well for the other histone marks.

T-ChIC can detect full length transcription from the same single cells, but in FigS3, the authors still used other published single cell transcriptomics to annotate the cell types, this seems unnecessary?

We used the published scRNA-seq dataset with a larger number of cells to homogenize our cell type labels with these datasets, but we also cross-referenced our cluster-specific marker genes with ZFIN and homogenized the cell type labels with ZFIN ontology. This way our annotation is in line with previous datasets but not biased by it. Due the relatively smaller size of our data, we didn’t expect to identify unique, rare cell types, but our full-length total RNA assay helps us identify non-coding RNAs such as miRNA previously undetected in scRNA assays, which we have now highlighted in new figure S1c .

Throughout the manuscript, the authors found some interesting dynamics between chromatin state and gene expression during embryogenesis, independent approaches should be used to validate these findings, such as IHC staining or RNA ISH?

We appreciate that the ISH staining could be useful to validate the expression pattern of genes identified in this study. But to validate the relationships between the histone marks and gene expression, we need to combine these stainings with functional genomics experiments, such as PRC2-related knockouts. Due to their complexity, such experiments are beyond the scope of this manuscript (see also reply to reviewer #3, comment #4 for details).

In Fig2 and FigS4, the authors showed H3K27me3 cis spreading during development, this looks really interesting. Is this zebrafish specific? H3K27me3 ChIP-seq or CutTag data from mouse and/or human embryos should be reanalyzed and used to compare. The authors could speculate some possible mechanisms to explain this spreading pattern?

Thanks for the suggestion. In this revision, we have reanalysed a dataset of mouse ChIP-seq of H3K27me3 during mouse embryonic development by Xiang et al (Nature Genetics 2019) and find similar evidence of spreading of H3K27me3 signal from their pre-marked promoter regions at E5.5 epiblast upon differentiation (new Figure S4i). This observation, combined with the fact that the mechanism of pre-marking of promoters by PRC1-PRC2 interaction seems to be conserved between the two species (see (Hickey et al., 2022), (Mei et al., 2021) & (Chen et al., 2021)), suggests that the dynamics of H3K27me3 pattern establishment is conserved across vertebrates. But we think a high-resolution profiling via a method like T-ChIC would be more useful to demonstrate the dynamics of signal spreading during mouse embryonic development in the future. We have discussed this further in our revised manuscript.

Reviewer #1 (Significance):

The authors have a longstanding focus and reputation on single cell sequencing technology development and application. In this current study, the authors developed a novel single-cell multi-omic assay termed "T-ChIC" so that to jointly profile the histone modifications along with the full-length transcriptome from the same single cells, analyzed the dynamic relationship between chromatin state and gene expression during zebrafish development and cell fate determination. In general, the assay works well, the data look convincing and conclusions are beneficial to the community.

Thank you very much for your supportive remarks.

Reviewer #2 (Evidence, reproducibility and clarity):

Joint analysis of multiple modalities in single cells will provide a comprehensive view of cell fate states. In this manuscript, Bhardwaj et al developed a single-cell multi-omics assay, T-ChIC, to simultaneously capture histone modifications and full-length transcriptome and applied the method on early embryos of zebrafish. The authors observed a decoupled relationship between the chromatin modifications and gene expression at early developmental stages. The correlation becomes stronger as development proceeds, as genes are silenced by the cis-spreading of the repressive marker H3k27me3. Overall, the work is well performed, and the results are meaningful and interesting to readers in the epigenomic and embryonic development fields. There are some concerns before the manuscript is considered for publication.

We thank the reviewer for appreciating the quality of our study.

Major concerns:

(1) A major point of this study is to understand embryo development, especially gastrulation, with the power of scMulti-Omics assay. However, the current analysis didn't focus on deciphering the biology of gastrulation, i.e., lineage-specific pioneer factors that help to reform the chromatin landscape. The majority of the data analysis is based on the temporal dimension, but not the cell-type-specific dimension, which reduces the value of the single-cell assay.

We focussed on the lineage-specific transcription factor activity during gastrulation in Figure 4 and S8 of the manuscript and discovered several interesting regulators active at this stage. During our analysis of the temporal dimension for the rest of the manuscript, we also classified the cells by their germ layer and “latent” developmental time by taking the full advantage of the single-cell nature of our data. Additionally, we have now added the cell-type-specific H3K27me3 demethylation results for 24hpf in response to your comment below. We hope that these results, together with our openly available dataset would demonstrate the advantage of the single-cell aspect of our dataset.

(2) The cis-spreading of H3K27me3 with developmental time is interesting. Considering H3k27me3 could mark bivalent regions, especially in pluripotent cells, there must be some regions that have lost H3k27me3 signals during development. Therefore, it's confusing that the authors didn't find these regions (30% spreading, 70% stable). The authors should explain and discuss this issue.

Indeed we see that ~30% of the bins enriched in the pluripotent stage spread, while 70% do not seem to spread. In line with earlier observations(Hickey et al., 2022; Vastenhouw et al., 2010), we find that H3K27me3 is almost absent in the zygote and is still being accumulated until 24hpf and beyond. Therefore the majority of the sites in the genome still seem to be in the process of gaining H3K27me3 until 24hpf, explaining why we see mostly “spreading” and “stable” states. Considering most of these sites are at promoters and show signs of bivalency, we think that these sites are marked for activation or silencing at later stages. We have discussed this in the manuscript (“discussion”). However, in response to this and earlier comment, we went back and searched for genes that show H3K27me3 demethylation in the most mature cell types (at 24 hpf) in our data, and found a subset of genes that show K27 demethylation after acquiring them earlier. Interestingly, most of the top genes in this list are well-known as developmentally important for their corresponding cell types. We have added this new result and discussed it further in the manuscript (Fig. 2d,e, , Supplementary table 3).

Minors:

(1) The authors cited two scMulti-omics studies in the introduction, but there have been lots of single-cell multi-omics studies published recently. The authors should cite and consider them.

We have cited more single-cell chromatin and multiome studies focussed on early embryogenesis in the introduction now.

(2) bT-ChIC seems to have been presented in a previous paper (ref 15). Therefore, Fig. 1a is unnecessary to show.

Figure 1a. shows a summary of our Zebrafish TChIC workflow, which contains the unique sample multiplexing and sorting strategy to reduce batch effects, which was not applied in the original TChIC workflow. We have now clarified this in “Results”.

(3) It's better to show the percentage of cell numbers (30% vs 70%) for each heatmap in Figure 2C.

We have added the numbers to the corresponding legends.

(4) Please double-check the citation of Fig. S4C, which may not relate to the conclusion of signal differences between lineages.

The citation seems to be correct (Fig. S4C supplements Fig. 2C, but shows mesodermal lineage cells) but the description of the legend was a bit misleading. We have clarified this now.

(5) Figure 4C has not been cited or mentioned in the main text. Please check.

Thanks for pointing it out. We have cited it in Results now.

Reviewer #2 (Significance):

Strengths:

This work utilized a new single-cell multi-omics method and generated abundant epigenomics and transcriptomics datasets for cells covering multiple key developmental stages of zebrafish.

Limitations:

The data analysis was superficial and mainly focused on the correspondence between the two modalities. The discussion of developmental biology was limited.

Advance:

The zebrafish single-cell datasets are valuable. The T-ChIC method is new and interesting.

The audience will be specialized and from basic research fields, such as developmental biology, epigenomics, bioinformatics, etc.

I'm more specialized in the direction of single-cell epigenomics, gene regulation, 3D genomics, etc.

Thank you for your remarks.

Reviewer #3 (Evidence, reproducibility and clarity):

This manuscript introduces T‑ChIC, a single‑cell multi‑omics workflow that jointly profiles full‑length transcripts and histone modifications (H3K27me3 and H3K4me1) and applies it to early zebrafish embryos (4-24 hpf). The study convincingly demonstrates that chromatin-transcription coupling strengthens during gastrulation and somitogenesis, that promoter‑anchored H3K27me3 spreads in cis to enforce developmental gene silencing, and that integrating TF chromatin status with expression can predict lineage‑specific activators and repressors.

Major concerns

(1) Independent biological replicates are absent, so the authors should process at least one additional clutch of embryos for key stages (e.g., 6 hpf and 12 hpf) with T‑ChIC and demonstrate that the resulting data match the current dataset.

Thanks for pointing this out. We had, in fact, performed T-ChIC experiments in four rounds of biological replicates (independent clutch of embryos) and merged the data to create our resource. Although not all timepoints were profiled in each replicate, two timepoints (10 and 24hpf) are present in all four, and the celltype composition of these replicates from these 2 timepoints are very similar. We have added new plots in figure S2f and added (new) supplementary table (#1) to highlight the presence of biological replicates.

(2) The TF‑activity regression model uses an arbitrary R² {greater than or equal to} 0.6 threshold; cross‑validated R² distributions, permutation‑based FDR control, and effect‑size confidence intervals are needed to justify this cut‑off.

Thank you for this suggestion. We did use 10-fold cross validation during training and obtained the R²> values of TF motifs from the independent test set as an unbiased estimate. However, the cutoff of R² > 0.6 to select the TFs for classification was indeed arbitrary. In the revised version, we now report the FDR-adjusted p-values for these R² estimates based on permutation tests, and select TFs with a cutoff of padj < 0.01. We have updated our supplementary table #4 to include the p-values for all tested TFs. However, we see that our arbitrary cutoff of 0.6 was in fact, too stringent, and we can classify many more TFs based on the FDR cutoffs. We also updated our reported numbers in Fig. 4c to reflect this. Moreover, supplementary table #4 contains the complete list of TFs used in the analysis to allow others to choose their own cutoff.

(3) Predicted TF functions lack empirical support, making it essential to test representative activators (e.g., Tbx16) and repressors (e.g., Zbtb16a) via CRISPRi or morpholino knock‑down and to measure target‑gene expression and H3K4me1 changes.

We agree that independent validation of the functions of our predicted TFs on target gene activity would be important. During this revision, we analysed recently published scRNA-seq data of Saunders et al. (2023) (Saunders et al., 2023), which includes CRISPR-mediated F0 knockouts of a couple of our predicted TFs, but the scRNAseq was performed at later stages (24hpf onward) compared to our H3K4me1 analysis (which was 4-12 hpf). Therefore, we saw off-target genes being affected in lineages where these TFs are clearly not expressed (attached Fig 1). We therefore didn’t include these results in the manuscript. In future, we aim to systematically test the TFs predicted in our study with CRISPRi or similar experiments.

(4) The study does not prove that H3K27me3 spreading causes silencing; embryos treated with an Ezh2 inhibitor or prc2 mutants should be re‑profiled by T‑ChIC to show loss of spreading along with gene re‑expression.

We appreciate the suggestion that indeed PRC2-disruption followed by T-ChIC or other forms of validation would be needed to confirm whether the H3K27me3 spreading is indeed causally linked to the silencing of the identified target genes. But performing this validation is complicated because of multiple reasons: 1) due to the EZH2 contribution from maternal RNA and the contradicting effects of various EZH2 zygotic mutations (depending on where the mutation occurs), the only properly validated PRC2-related mutant seems to be the maternal-zygotic mutant MZezh2, which requires germ cell transplantation (see Rougeot et al. 2019 (Rougeot et al., 2019)) , and San et al. 2019 (San et al., 2019) for details). The use of inhibitors have been described in other studies (den Broeder et al., 2020; Huang et al., 2021), but they do not show a validation of the H3K27me3 loss or a similar phenotype as the MZezh2 mutants, and can present unwanted side effects and toxicity at a high dose, affecting gene expression results. Moreover, in an attempt to validate, we performed our own trials with the EZH2 inhibitor (GSK123) and saw that this time window might be too short to see the effect within 24hpf (attached Fig. 2). Therefore, this validation is a more complex endeavor beyond the scope of this study. Nevertheless, our further analysis of H3K27me3 de-methylation on developmentally important genes (new Fig. 2e-f, Sup. table 3) adds more confidence that the polycomb repression plays an important role, and provides enough ground for future follow up studies.

Minor concerns

(1) Repressive chromatin coverage is limited, so profiling an additional silencing mark such as H3K9me3 or DNA methylation would clarify cooperation with H3K27me3 during development.

We agree that H3K27me3 alone would not be sufficient to fully understand the repressive chromatin state. Extension to other chromatin marks and DNA methylation would be the focus of our follow up works.

(2) Computational transparency is incomplete; a supplementary table listing all trimming, mapping, and peak‑calling parameters (cutadapt, STAR/hisat2, MACS2, histoneHMM, etc.) should be provided.

As mentioned in the manuscript, we provide an open-source pre-processing pipeline “scChICflow” to perform all these steps (github.com/bhardwaj-lab/scChICflow). We have now also provided the configuration files on our zenodo repository (see below), which can simply be plugged into this pipeline together with the fastq files from GEO to obtain the processed dataset that we describe in the manuscript. Additionally, we have also clarified the peak calling and post-processing steps in the manuscript now.

(3) Data‑ and code‑availability statements lack detail; the exact GEO accession release date, loom‑file contents, and a DOI‑tagged Zenodo archive of analysis scripts should be added.

We have now publicly released the .h5ad files with raw counts, normalized counts, and complete gene and cell-level metadata, along with signal tracks (bigwigs) and peaks on GEO. Additionally, we now also released the source datasets and notebooks (Rmarkdown format) on Zenodo that can be used to replicate the figures in the manuscript, and updated our statements on “Data and code availability”.

(4) Minor editorial issues remain, such as replacing "critical" with "crucial" in the Abstract, adding software version numbers to figure legends, and correcting the SAMtools reference.

Thank you for spotting them. We have fixed these issues.

Reviewer #3 (Significance):

The method is technically innovative and the biological insights are valuable; however, several issues-mainly concerning experimental design, statistical rigor, and functional validation-must be addressed to solidify the conclusions.

Thank you for your comments. We hope to have addressed your concerns in this revised version of our manuscript.

Author response image 1.

(1) (top) expression of tbx16, which was one of the common TFs detected in our study and also targeted by Saunders et al by CRISPR. tbx16 expression is restricted to presomitic mesoderm lineage by 12hpf, and is mostly absent from 24hpf cell types. (bottom) shows DE genes detected in different cellular neighborhoods (circled) in tbx16 crispants from 24hpf subset of cells in Saunders et al. None of these DE genes were detected as “direct targets” in our analysis and therefore seem to be downstream effects. (2) Effect of 3 different concentrations of EZH2 inhibitor (GSK123) on global H3K27me3 quantified by flow cytometry using fluorescent coupled antibody (same as we used in T-ChIC) in two replicates. The cells were incubated between 3 and 10 hpf and collected afterwards for this analysis. We observed a small shift in H3K27me3 signal, but it was inconsistent between replicates.

References

Chen, Z., Djekidel, M. N., & Zhang, Y. (2021). Distinct dynamics and functions of H2AK119ub1 and H3K27me3 in mouse preimplantation embryos. Nature Genetics, 53(4), 551–563. den Broeder, M. J., Ballangby, J., Kamminga, L. M., Aleström, P., Legler, J., Lindeman, L. C., & Kamstra, J. H. (2020). Inhibition of methyltransferase activity of enhancer of zeste 2 leads to enhanced lipid accumulation and altered chromatin status in zebrafish. Epigenetics & Chromatin, 13(1), 5.

Hickey, G. J., Wike, C. L., Nie, X., Guo, Y., Tan, M., Murphy, P. J., & Cairns, B. R. (2022). Establishment of developmental gene silencing by ordered polycomb complex recruitment in early zebrafish embryos. eLife, 11, e67738.

Huang, Y., Yu, S.-H., Zhen, W.-X., Cheng, T., Wang, D., Lin, J.-B., Wu, Y.-H., Wang, Y.-F., Chen, Y., Shu, L.-P., Wang, Y., Sun, X.-J., Zhou, Y., Yang, F., Hsu, C.-H., & Xu, P.-F. (2021). Tanshinone I, a new EZH2 inhibitor restricts normal and malignant hematopoiesis through upregulation of MMP9 and ABCG2. Theranostics, 11(14), 6891–6904.

Mei, H., Kozuka, C., Hayashi, R., Kumon, M., Koseki, H., & Inoue, A. (2021). H2AK119ub1 guides maternal inheritance and zygotic deposition of H3K27me3 in mouse embryos. Nature Genetics, 53(4), 539–550.

Rougeot, J., Chrispijn, N. D., Aben, M., Elurbe, D. M., Andralojc, K. M., Murphy, P. J., Jansen, P. W. T. C., Vermeulen, M., Cairns, B. R., & Kamminga, L. M. (2019). Maintenance of spatial gene expression by Polycomb-mediated repression after formation of a vertebrate body plan. Development (Cambridge, England), 146(19), dev178590.

San, B., Rougeot, J., Voeltzke, K., van Vegchel, G., Aben, M., Andralojc, K. M., Flik, G., & Kamminga, L. M. (2019). The ezh2(sa1199) mutant zebrafish display no distinct phenotype. PloS One, 14(1), e0210217.

Saunders, L. M., Srivatsan, S. R., Duran, M., Dorrity, M. W., Ewing, B., Linbo, T. H., Shendure, J., Raible, D. W., Moens, C. B., Kimelman, D., & Trapnell, C. (2023). Embryo-scale reverse genetics at single-cell resolution. Nature, 623(7988), 782–791.

Vastenhouw, N. L., Zhang, Y., Woods, I. G., Imam, F., Regev, A., Liu, X. S., Rinn, J., & Schier, A. F. (2010). Chromatin signature of embryonic pluripotency is established during genome activation. Nature, 464(7290), 922–926.

Zeller, P., Blotenburg, M., Bhardwaj, V., de Barbanson, B. A., Salmén, F., & van Oudenaarden, A. (2024). T-ChIC: multi-omic detection of histone modifications and full-length transcriptomes in the same single cell. In bioRxiv (p. 2024.05.09.593364). https://doi.org/10.1101/2024.05.09.593364

Zeller, P., Yeung, J., Viñas Gaza, H., de Barbanson, B. A., Bhardwaj, V., Florescu, M., van der Linden, R., & van Oudenaarden, A. (2022). Single-cell sortChIC identifies hierarchical chromatin dynamics during hematopoiesis. Nature Genetics. https://doi.org/10.1038/s41588-022-01260-3

Author Response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Although the data are generally solid and well interpreted, a control showing that protein depletion works properly in cell-cycle arrested cells is lacking, both when using siRNAs and degron-based depletion.

We now demonstrate in Fig. S9 efficient degron-mediated depletion of both NUF2 and SPC24 in cell-cycle arrested cells by Western blotting. We show similar data for siRNA knockdowns. Our siRNA knockdown experiments include a “siDEATH” control that induces cytotoxicity by targeting several essential genes. In Fig. S6a we now show that siDEATH transfection results in strong cytotoxicity and cell death in cycling as well as cell cycle arrested G1/S and G2/M populations indicating efficient protein depletion. Additionally, in Fig. S6b we now show depletion NCAPH2 protein levels by siRNA knockdown in cycling as well as cell cycle arrested cell populations by Western blot analysis. We mention these results on page 11 and page 13.

Reviewer #2 (Public review):

The filtering strategy used in the screen imposes significant constraints, as it selects only for non-essential or functionally redundant genes. This is a critical point, as key regulators of chromatin organisation - such as components of the condensin and cohesin complexes-are typically essential for viability. Similarly, known effectors of centromere behaviour (e.g., work by the Fachinetti's lab) often lead to aneuploidy, micronuclei formation, and cell cycle arrest in G1. The implication of this selection criterion should be clearly discussed, as it fundamentally shapes the interpretation of the study's findings.

We discussed our hit selection criteria on page 8 and in the Methods section. Some of the concerns regarding a bias towards non-essential genes are alleviated by the fact that our screen is limited to a relative short duration of 72 hours rather than the longer timepoints that are generally used to assess essentiality in pooled CRISPR-KO screens, allowing us to identify genes that may be essential if eliminated permanently. In support of this notion, we identify subunits of the essential condensin and cohesin complexes as hits with only limited effect on cell viability. In this case, the Z-score for change in cell number upon NCAPH2 knockout was -0.26 indicating only a mild reduction compared to the average cell number across all targets.

Other confounding effects on hit selection due to micronuclei formation, cell cycle effects etc. are minimized as we closely monitor micronuclei formation and cell viability in our screen. Finally, aneuploidy is similarly not a confounding factor in hit identification since, as we previously demonstrated, the Ripley’s K-based clustering score is robust to changes in spot number (Keikhosravi, A., et al. 2025).

A major limitation of the study is the lack of connection between centromere clustering and its biological significance. It remains unclear whether this clustering is a meaningful proxy for higher-order genome organisation. Additionally, the study does not explore potential links to cell identity or transcriptional landscapes. Readers may struggle to grasp the broader relevance of the findings: if gene knockouts that alter centromere positioning do not affect cell viability or cell cycle progression, does this imply that centromere clustering - and by extension, interphase genome organisation - is not biologically significant?

We appreciate these points. Given the presence of one centromere on each chromosome, we used centromeres as surrogate landmarks of higher-order nuclear genome organization and considered centromere patterns as a general indicator of overall genome organization. While the relationship of centromere patterns to other genome features is poorly understood in mammalian cells, a link is suggested by observations in other organisms. For example, in yeast, the clustering of centromeres reflects the overall Rabl configuration of chromosomes. Having said that, we agree that our extrapolation to overall genome organization is somewhat speculative, and we have toned down these conclusions throughout the manuscript.

We agree that one of the most interesting questions emerging from our study is whether centromere clustering has a functional role. In follow-up studies we will use some of the key regulator identified in these screens to perturb the native centromere distribution and assay for various cellular responses including in gene expression and genome integrity. These studies will be the subject of future publications.

Another point requiring clarification is the conclusion that the four identified genes represent independent pathways regulating centromere clustering. In reality, all of these proteins localise to centromeres. For example, SPC24 and NUF2 are components of the NDC80 complex; Ki-67, a chromosome periphery protein, has been mapped to centromeres; and CAP-Hs, a subunit of the condensin II complex that during G1 promotes CENP-A deposition. Given their shared localisation, it would be informative to assess aneuploidy indices following depletion of each factor. Chromosome-specific probes could help determine whether centromere dysfunction leads to general mis-segregation or reflects distinct molecular mechanisms. Additionally, exploring whether Ki-67 mutants that affect its surfactant-like properties influence centromere clustering could provide a more mechanistic insight.

We thank the reviewer for this comment. We now clarify the relationship of these proteins to centromeres in more detail on page 12. While they all have some relationship to centromeres, as would be expected if they contributed to centromere clustering, they represent multiple distinct pathways and processes.

The observed effects on clustering are unlikely due to aneuploidy as only very limited aneuploidy is observed in our cells and because Ripley’s K measurement of centromere clustering is robust to change in chromosome copy number. Follow-up studies using live cell imaging approaches are currently in progress to address some of these mechanistic questions.

Finally, the additive effects observed mild mis-segregation effects are amplified when two proteins within the same pathway are depleted. This possibility should be considered in the interpretation of the data.

We rephrased the text on page 14 based on the reviewer’s recommendations.

Reviewer #3 (Public review):

Given the authors' suggestion that disorderly mitotic progression underlies the changes in centromere clustering in the subsequent interphase, I think it would be beneficial to showcase examples of disorderly mitosis in the AID samples and perhaps even quantify the misalignment on the metaphase plate.

We now include in Fig. S11 examples of disordered mitotic nuclei observed in the absence of NUF2 or SPC24.

I don't quite agree with the description that centromeres cluster into chromocenters (p4 para 2, p17 para 1, and other instances in the manuscript). To the best of my knowledge, chromocenters primarily consist of clustered pericentromeric heterochromatin, while the centromeres are studded on the chromocenter surface. This has been beautifully demonstrated in mouse cells (Guenatri et al., JCB, 2004), but it is true in other systems like flies and plants as well.

We have modified this description on page 4.

Recommendations for the authors:

Reviewing Editor Comments:

(1) Proper characterisation of the cell lines used in the manuscript. Tagged proteins have been known to affect protein levels compared to the parental cell, and where this is the case (or not), it needs to be transparently shown in the manuscript.

The cell lines to conditionally deplete NCAPH2 and KI67 have previously been published, and they have been characterized to show normal expression levels of the tagged protein (Takagi et al., 2018). We also show quantification of Western blots to compare protein level of tagged SPC24 and NUF2 to that of the untagged proteins in the parental cell line (Fig. S8e-f) and discuss these results on page 11 and page 12.

(2) Demonstration of protein depletion in the degron cell lines.

We showed efficient protein depletion in the degron cell lines (Fig. S8c and S8d). In addition, we now show in Fig. S9 depletion of SPC24 and NUF2 in cells arrested at G1/S and G2/M.

(3) The study examines centromere clustering, but not genome architecture. While it is understood that a complete investigation of genome architecture is beyond the scope of the current study, the interpretation does not match the data. The authors are suggested to pay attention to this point throughout the manuscript and consider their findings in terms of centromere clustering rather than genome architecture, including changing the title accordingly.

We have toned down our statements regarding overall genome organization throughout the manuscript. Since centromeres are a natural fiducial marker for overall genome organization and a link to overall genome organization has been suggested in some organisms such as yeast, we have retained the wording in a few select instances, including the title. We also make it clear that we do not intend to draw conclusions regarding TADs or even compartments but consider centromere patterns an indicator of overall genome organization.

Reviewer #1 (Recommendations for the authors):

(1) Controls of depletion by western blot in synchronized cells (siRNAs and degrons) are lacking.

We now show Western blots demonstrating efficient depletion of the target proteins in degron (Fig. S9) and siRNA treated cell-cycle arrested cells (Fig. S6b).

It would have been very nice to discuss the implications of these findings further. For example, do centromere clustering changes gene expression/repression of pericentromeric heterochromatin expression? Is centromere clustering associated with specific diseases? How is global chromatin organization affecting gene expression/genome stability, etc? Although some of these aspects are unknown, a discussion about them would have been nice.

We appreciate these interesting points. These questions are the subject of our ongoing follow up studies. We now discuss possible consequences of centromere re-organization on gene expression and genome stability on page 18.

Reviewer #2 (Recommendations for the authors):

Major Comments:

(1) Clarify Scope and Avoid Overinterpretation

(a) The study exclusively investigates centromere positioning, without addressing broader aspects of genome architecture.

(b) There is no established link presented between centromere positioning and higher-order genome organisation.

We have toned down our statements regarding overall genome organization throughout the manuscript. Since centromeres are a natural fiducial marker for overall genome organization and observations in yeast suggest such a link, we have retained the wording in a few select instances. We make it clear that we do not intend to draw conclusions regarding TADs or even compartments but consider centromere patterns an indicator of overall genome organization.

(c) The exclusion criteria used in the screen should be clearly explained, including the implications of selecting only non-essential or redundant genes.

We discuss on page 8 and in the Methods section the exclusion criteria used in the screen, including the implications for identifying essential genes.

(d) The authors should discuss why the identified proteins significantly affect centromere clustering but do not impact cell cycle progression.

We now discuss this topic briefly on page 9. While some hits are expected to affect both cell-cycle progression and centromere clustering (Fig. S4c), it is not a priori expected that all hits would affect both.

(2) Supplementary Figure 1

This figure appears unnecessary. The co-localisation between CENP-C and CENP-A is well established in the literature, and the scoring provided does not add essential new information.

The data was included in response to repeat questions from a centromere expert. We prefer to retain this data for completeness.

(3) Differential Hits between Cell Lines 

For hits that behave differently across cell lines, expression data should be provided. Are the genes equally expressed in both cell types? What is the level of depletion achieved?

It is possible that cell-type specific hits arise due to difference in expression. Cell-type specific hits may also arise due multiple other reason including cancer vs. non-cancer origin, hTERT-immortalization, cell growth properties, variation in underlying DNA sequences of the Cas9 target loci, initial state of centromere clustering to name a few. Each of these possibilities requires additional experiments to identify the exact reason for cell-type specificity of a given factor. A full analysis of the reason for cell-type specificity is, however, beyond the scope of current study.

(4) Efficiency of Cell Cycle-Specific Degradation

Degradation efficiency likely varies across cell cycle stages. The authors should provide Western blots showing the extent of protein depletion at each cell cycle block.

We provide Western blot data in Fig. S9 to demonstrate efficient knockdown of proteins in G1/S and G2/M arrested cells.

(5) Figure S6 - Validation of New Cell Lines

Genotyping data for the newly generated cell lines should be included, along with Western blots using protein-specific antibodies (not just the tag), compared to the parental cell line.

We provide in Fig. S7c-d genotyping data and in Fig. S8e-f Western blot data to compare levels of tagged and untagged proteins.

(6) Figure S7 - G2/M Block Efficiency

The G2/M block appears suboptimal after 20 hours in RO-3306, with only ~50% of cells in G2/M and just 21-27% for Ki-67, where most cells remain in S phase. This raises concerns about the interpretation of mitotic depletion effects. It is possible that cells never progressed from G1 or completed S phase without Ki-67. Prior studies (van Schaik et al., 2022; Stamatiou et al., 2024) have shown delayed and uneven replication of centromeric/pericentromeric regions upon Ki-67 depletion during S phase, which could affect the readout. Live-cell imaging would be a more robust approach to confirm mitotic status.

For KI67 after RO-3306 treatment, 73 and 67% cells were arrested at the G2/M boundary in the presence or absence of KI67, respectively (Fig. S10a-b). Upon release from G2/M arrest, the proportion of G1 cells increased from 6-13% to 28-60% in all four factors tested (Fig. S10b, and d). Please note that our results are not directly dependent on release efficiency, since we use single-cell staging (Fig. 3b) and selectively analyze only G1 populations (Fig. 5c).

We are currently working towards live cell imaging, but this requires development and characterization of additional cell lines which is beyond the scope of this study.

Statistical analyses of cell cycle phase distributions should also be included.

We include statistical analyses of cell cycle phase distributions in Fig. S4c and Fig. S10c-d by performing t-tests with FDR corrections to compare percentage of cells in either in G1, S or G2 in the presence and absence of each factor tested.

(7) Aneuploidy Assessment

Aneuploidy scores for the four key proteins should be provided, ideally using centromere-specific FISH probes.

While an aneuploidy score for each hit would be interesting piece of information, we showed in a previous publication that the Ripley’s K-based Clustering Score method used here is robust to aneuploidy (Keikhosravi et al., 2025) and aneuploidy would thus not lead to spurious identification of these proteins in our screen.

(8) Add-Back Experiment (Page 14)

While the add-back experiment is conceptually strong, its execution could be improved. <br /> It should be performed on synchronised cells: deplete the protein in G2/M, arrest in thymidine, then release into G1 without the protein to observe the unclustering phenotype.

Re-expression should occur during the block, followed by release and analysis in the next G1 phase. This would better demonstrate whether clustering defects from the previous division can be rescued.

We have attempted these types of long-term depletion experiments in cell-cycle arrested cells, but have observed significant viability defects, making results uninterpretable.

(9) Statistical Analyses

Several figures lack statistical analysis, which is essential for data interpretation:

(a) Figure 1B-E

(b) Figure 3I

(c) Figure 4B

(d) Figure 5B, C, G

(e) Supplementary Figures S4B and S7

Statistical analyses were performed for a) Fig. 1b-e, b) Fig. 3i, c) Fig. 4b, d) Fig. 5b-c and the details of the test are mentioned in the corresponding figure legends. We also include statistical tests for Fig. 5g, S5b and S7c-d.

Minor Comments:

(1) Page 9: "Reassuringly, in line with known centromere-nucleoli association (Bury, Moodie et al. 2020, van Schaik, Manzo et al. 2022)..."

The citation "van Schaik, Manzo et al. 2022" is incorrect and should be revised.

We have removed this reference.

(2) Page 10:

"...were grouped into six categories: regulators of chromatin structure, kinetochore proteins, nucleolar proteins, nuclear pore complex components..."

The authors should note that NUP160, listed as a nuclear pore complex hit, is also a kinetochore component during mitosis and may be linked to mitotic defects.

We now mention this on page 10.

(3) Page 12:

"Progression through S phase was equally efficient in the presence or absence of KI67."

While bulk S phase progression may appear unaffected, refined analyses (e.g., Repli-seq, EdU patterning) have shown delayed replication of centromeric/pericentromeric regions upon Ki-67 depletion. This should be acknowledged, especially given the study's focus on centromeres (see Schaik et al., 2022; Stamatiou et al., 2024).

Our statement was meant to describe the results we observed in this study. We indicate that overall progression is not affected, but subtle effects may persist, and we cite the relevant references on page 13.

(4) Page 12:

"KI67 is a well-known marker of cell proliferation..."

The first study demonstrating the dependency of chromosome periphery on Ki-67 was Booth et al., 2014, which should be cited.

This citation has been added.

Reviewer #3 (Recommendations for the authors):

(1) On page 14, paragraph 1, the authors suggest that NCAPH2 and SPC24 act independently on centromere clustering. I'm not convinced that this is the right interpretation of the data. Rather, the lack of an additive phenotype following NCAPH2 and SPC24 dual depletion suggests to me that these two proteins are acting in the same pathway.

We show that knockdown of NCAPH2 and SPC24 results in opposite effects in centromere clustering. However, knockdown of SPC24 in NCAPH2-AID cells produces an intermediate level of clustering compared to depletion of NCAPH2 or SPC24 knockdown alone. This indicates additive effects. We have modified our description of these results on p. 14.

(2) The analysis and experimental design in Figure 5g could be improved. For one, I would add statistical comparisons like the other figure panels. Second, the authors would ideally perform AID depletion in a synchronized G2 population before washout during the subsequent G1. This design might make some of the more subtle changes (e.g., KI67-AID) more obvious.

We now include statistical analysis in Fig. 5g. We have attempted long-term depletion experiments in cell-cycle arrested cells, but have observed significant viability defects, making results uninterpretable.

(3) In the discussion, the authors allude to centromere clustering data from the NDC80 complex, HMGA1, and other HMGs but fail to direct the reader to where they may find the data. If these data are in Tables S4 and S5, perhaps the authors could make these tables more reader-friendly?

For each target, the mean Z-score of two biological replicates based on Clustering Score is located in column H in Table S4 and S5.

(4) In my opinion, the term 'clustering score' comes across a bit ambiguous. In most cases, this term appears to refer to the distance between centromeric foci but is used occasionally to refer to the number of centromeric spots. For example, on page 9, paragraph 1, line 3, cluster/clustering is used three times but with slightly different meanings. Perhaps the authors can consider using the word 'clustering' to indicate the number of spots, 'dispersion' to indicate distance between centromeres, and 'radial distribution' to indicate distance from the nuclear center? Or other ways to improve the consistency of the descriptive terms.

We apologize for not being clear. The Clustering Score is a very specific parameter derived from use of a Ripley’s K clustering algorithm as described in Materials and Methods. We now ensure that the term is used correctly throughout and that the other terms are also used consistently.

Author Response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

It is well established that many potivirids (viruses in the Potiviridae family), particularly potyviruses (viruses in the Potyvirus genus), recruit (selectively) either eIF4E or eIF(iso)4E, while some others can use both of them to ensure a successful infection. CBSD caused by two potyvirids, i.e., ipomoviruses CBSV and UCBSV, severely impedes cassava production in West Africa. In a previous study (PBI, 2019), Gomez and Lin (co-first authors), et al. reported that cassava encodes five eIF4E proteins, including eIF4E, eIF(iso)4E-1, eIF(iso)4E-2, nCBP-1 and nCBP-2, and CBSV VPg interacts with all of them (Co-IP data). Simultaneous CRISPR/Cas9-mediated editing of nCBp-1 and -2 in cassava significantly mitigates CBSD symptoms and incidence. In this study, Lin et al further generated all five eIF4E family single mutants as well as both eIF(iso)4E-1/-2 and nCBP-1/-2 double mutants in a farmer-preferred casava cultivar. They found that both eIF(iso)4E and nCBP double mutants show reduced symptom severity, and the latter is of better performance. Analysis of mutant sequences revealed one important point mutation, L51F of nCBP-,2 that may be essential for the interaction with VPg. The authors suggest that the introduction of the L51F mutation into all five eIF4E family proteins may lead to strong resistance. Overall I believe this is an important study enriching knowledge about eIF4E as a host factor/susceptibility factor of potyvirids and proposing new information for the development of high CBSD resistance in cassava. I suggest the following two major comments for authors to consider for improvement:

(1) As eIF(iso)4e-1/-2 or nCBP-1/-2 double mutants show resistance, why not try to generate a quadruple mutant? I believe it is technically possible through conventional breeding.

(2) I agree that L51F mutation may be important. But more evidence is needed to support this idea. For example, the authors may conduct a quantitative Y2H assay on the binding of VPg to each of the eIF4E (L51F) mutants. Such data may add as additional evidence to support your claim.

We thank the reviewer for their overall assessment. Regarding investigating a quadruple mutant, we agree that this is a logical next step to investigate. A conventional breeding approach with existing mutant lines, however, is problematic for several reasons; 1) cassava does not flower where this work was conducted, and 2) cassava is subject to inbreeding depression, resulting in both low seed set and considerable heterogeneity among progeny that do arise. Editing existing double mutants is possible, but would require a significant, multi-year investment to produce embryogenic tissue from existing lines and generate the new lines. Cassava has practical limits as a non-model plant. Given these constraints, we conclude that investigating a quadruple mutant is beyond the scope of the current work.

For investigating the HPL to HPF mutation in other cassava eIF4E-family proteins and their interaction with VPg in yeast, we have now completed this experiment and included the data in the paper. Notably we find that generating this mutant for eIF(iso)4E-2 attenuates VPg interaction without impairing eIF(iso)4E-2 accumulation, while similarly mutating nCBP-1 and eIF(iso)4E-1 results in total and reduced protein accumulation, respectively.

Reviewer #2 (Public review):

Summary:

The authors generated single and double knockout mutants for the eIF4E family members eIF4E, iso4E1, iso4E2, nCBP1, and nCBP2 in cassava. While a single knockout of these eIF4E genes did not abolish viral infection, the nCBP1/nCBP2 double knockout mutant displayed the weakest symptoms and viral infection. Through yeast two-hybrid screening, the nCBP-2 L51F mutant was identified, and the mutant was unable to interact with VPg, yet the nCBP-2 L51F mutant could complement the eIF4E yeast mutant. This L51F is a potentially important editing site for eIF4E.

Strengths:

This study systematically generated single and double knockout mutants for the eIF4E family members and investigated their antiviral activity. It also identified a L51F site as a potentially important antiviral editing site in eIF4E, however, its antiviral genetic evidence remains to be validated.

Weaknesses:

(1) The symptoms of the iso4E1 & iso4E2 double-knockout mutant are slightly alleviated, and those of the nCBP1 & nCBP2 double-knockout mutant are alleviated the most. If the iso4E1 & iso4E2 and nCBP1 & nCBP2 mutants are crossed to obtain quadruple-knockout mutant plants, whether the resistance of the quadruple mutant will be more excellent should be further investigated.

(2) Although the yeast two-hybrid identified the nCBP-2 L51F mutant, there is no direct biological evidence demonstrating its antiviral function. While the 6-amino acid deletion mutant (including L51F) showed attenuated symptoms, this deletion might be sufficient to cause loss-of-function of nCBP-2. These indirect observations cannot definitively establish that the L51F mutation specifically confers antiviral activity.

(3) Given that nCBP-2 can rescue yeast eIF4E mutants, introducing wild type and L51F nCBP2 into the Arabidopsis iso4e mutant viral infectious clones into yeast systems could clarify whether the L51F mutation (and the same mutations in eIF4E, iso4E1, iso4E2) abrogates their roles as viral susceptibility factors - critical genetic evidence currently missing.

We sincerely thank the reviewer for their constructive feedback.

With regards to investigating a quadruple eIF4E mutant, please see our response to reviewer 1.

The reviewer makes a salient point regarding the nCBP-2 L51F and K45_L51del mutations. Ideally, complementation of the ncbp double mutant with nCBP-2 L51F, followed by viral challenge, would address this question. However, the practical limitations, as noted in our response to reviewer 1, make this difficult within the context of this manuscript. We acknowledge that this is a limitation of our study and have been cautious in not overstating our conclusions.

Reviewer #3 (Public review):

In the manuscript, the authors generated several mutant plants defective in the eIF4E family proteins and detected cassava brown streak viruses (CBSVs) infection in these mutant plants. They found that CBSVs induced significantly lower disease scores and virus accumulation in the double mutant plants. Furthermore, they identified important conserved amino acid for the interaction between eIF4E protein and the VPg of CBSVs by yeast two hybrid screening. The experiments are well designed, however, some points need to be clarified:

(1) The authors reported that the ncbp1 ncbp2 double mutant plants were less sensitive to CBSVs infection in their previous study, and all the eIF4E family proteins interact with VPg. In order to identify the redundancy function of eIF4E family proteins, they generated mutants for all eIF4E family genes, however, these mutants are defective in different eIF4E genes, they did not generate multiple mutants (such as triple, quadruple mutants or else) except several double mutant plants, it is hard to identify the redundant function eIF4E family genes.

(2) The authors identified some key amino acids for the interaction between eIF4E and VPg such as the L51, it is interesting to complement ncbp1 ncbp2 double mutant plants with L51F form of eIF4E and double check the infection by CBSVs.

We thank the reviewer for their assessment and feedback.

Regarding analysis of higher-order mutants, please see our response to Reviewer #1’s public review.

For investigation of nCBP-2 L51F in planta, please see our response to Reviewer #2’s public review.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Since nCBP2 can complement a yeast mutant, it indicates that nCBP2 can also complement Arabidopsis. Wild-type nCBP2 should be introduced into the Arabidopsis iso4e mutant to determine whether it can complement Arabidopsis iso4e and whether the virus can re-establish the infection. The nCBP2 L51F mutant should also be introduced into the Arabidopsis iso4e mutant to see if this mutant fails to re-establish the virus infection. Similarly, eIF4E, iso4E1, iso4E2, nCBP1, etc., should be introduced into the Arabidopsis iso4e mutant to determine whether they can truly complement the virus-infected mutant Arabidopsis, while the L51F mutants cannot.

Arabidopsis encodes multiple eIF4E proteins, an nCBP protein, and an eIF(iso)4E protein, and knocking out the eIF(iso)4e gene specifically confers resistance to TuMV. Introducing cassava nCBP-2 into arabidopsis eif(iso)4e mutants is unlikely to restore TuMV susceptibility. Because TuMV belongs to a different genus than CBSV, we used the TuMV VPg interaction with arabidopsis eIF(iso)4E to test the generality of mutating the eIF4E HPL motif to HPF potyvirid VPg-eIF4E interaction. However, since this mutation disrupts arabidopsis eIF(iso)4E’s endogenous translation initiation activity in yeast, this mutant protein is not worth pursuing further. In contrast, cassava eIF(iso)4E-2 L27F retains translation initiation activity and has reduced interaction with CBSV VPg by quantitative yeast two-hybrid. It would be interesting to see if this particular mutant protein could interact with TuMV VPg, and if not, would then be worth testing for the ability to restore TuMV susceptibility in Arabidopsis eif(iso)4e. Unfortunately, we are unable to pursue these experiments at this time.

(2) Given that nCBP-2 can complement yeast eIF4E mutants, the authors may introduce viral infectious clones into yeast systems expressing nCBP-2 variants to determine whether nCBP-2 supports viral translation. This approach could further clarify whether the L51F mutation (and mutations in eIF4E, iso4E1, so4E2) abolishes their roles as viral susceptibility factors.

This is an intriguing suggestion, but challenging for a few reasons. First, an infectious clone of CBSV Naliendele isolate does not exist, although we have tried to construct one, without success. There is also no guarantee such a clone could infect yeast. We are aware of yeast being used as a surrogate host for a few plant viruses, such as Tomato bushy stunt virus and Brome mosaic virus but are unaware of a similar system for any potyvirid. Developing such a system would undoubtedly require a significant investmentbeyond the scope of this manuscript.

(3) Phenotypes of all mutant lines with and without virus inoculation in Table 1 should be presented.

Photos of un-challenged mutants are included in supplemental figures. Representative storage root symptoms for all lines have now been included in the supplemental figures as well.

(4) In Figure 1c, the results of viral accumulation assays should be presented for additional mutant lines beyond ncbp-1, ncbp-2, ncbp-1 nCBP-2 K45_L51del, and ncbp-1 ncbp-2, particularly eif(iso)4e-1 & eif(iso)4e-2#172 and eif(iso)4e-1 & eif(iso)4e-2#92.

We have previously found that subtle reductions in visible disease do not always translate to clear differences in viral titer when analyzed by qPCR (Gomez et al., 2018). As such, we focused on lines with the strongest phenotypes in viral titer experiments.

(5) Inconsistently, the ncbp-1 nCBP-2 K45_L51del line showed reduced symptoms compared to wild-type in Figures 1a and 1b, yet viral accumulation levels were comparable to wild-type in Figure 1c. The explanations for this discrepancy are required.

Please see our response to (4).

(6) Root phenotypic data for all mutant lines shown in Figure 1d should be presented.

Please see our response to (3).

(7) In Figure 2b, GST control pulldowns showed detectable proteins. This background signal requires explanation.

It is not uncommon to see weak signal in bead or tag-only negative control pulldown and IP reactions. Importantly, we see strong enrichment of VPg relative to these controls in our experimental samples.

(8) Contrary to the abstract's implication, Figure 5c indicates that the L51F mutation impacts yeast growth, suggesting potential pleiotropic effects of this mutant.

We interpret the results to be that nCBP2 L51F does not fully complement the yeast eif4e mutation, rather than nCBP2 L51F impacts yeast growth.

(9) In vivo protein-protein interaction assays (e.g., co-immunoprecipitation) should be performed to complement the in vitro GST pull-down data in Figure 6.

We appreciate the desire for these experiments and agree that they would bolster our Y2H and pulldown data. Unfortunately, we are not able to complete these experiments at this time, so have been careful not to over interpret the data.

(10) Since the AteIF(iso)4E L28F mutant fails to complement yeast, the authors should test whether introducing the L51F mutation into other family members (eIF4E, iso4E1, iso4E2, nCBP1) preserves their yeast complementation capacity.

This has now been done for additional cassava eIF4E-family proteins.

(11) Indicate molecular weight sizes in all Western blots.

This was done. As differences in buffer formulations between gel types can affect the mobility and thus apparent molecular weight of markers, we have provided in the methods section SDS-PAGE gel chemistries and specific protein ladders used in this study. Importantly we note in our experience that certain markers, in relation to proteins of interest, can vary up to 15 kDa between gel chemistries.

(12) Figures 4d,e are not provided in the paper. Based on the content of the paper, the description in the paper likely corresponds to Figures 5c, d.

Thank you for catching this error, this has now been corrected.

Congratulations. You've joined an exclusive club that includes writers like: Edward Abbey John Ashbery, Saul Below, Johnny Carson, Joan Didion, Bernard Kalb, Elia Kazan, Helen Keller, Grace Metalious, Arthur Miller, Carl Reiner, Fred Rogers, Rod Sterling, George Sheehan, and Wallace Stegner.

I've got over 60 typewriters in my collection and the KMG is my favorite, especially when it's clean and properly adjusted. I've got one each in Royal Elite and Royal Pica typefaces they're so nice.

KMG controls diagram: https://site.xavier.edu/polt/typewriters/RoyalKMGdiagram.jpg<br /> Richard Polt's site doesn't have a manual (yet) for the KMG, so pull the manual for the Royal KMM instead. It was the model made just before the KMG and should be functionally identical. The Royal HH which followed it was also broadly similar. https://site.xavier.edu/polt/typewriters/tw-manuals.html

The spools for the standard Royal typewriters (Ten, H, KH, KHM, KMM, KMG, RP, HH, FP, Empress, 440, 660, etc.) have a custom metal mechanism for their auto-reverse. The spools are known as the T1 (which is the same as General Ribbon part # T1-77B , T1-77BR, and Nu-Kote B64.) If winding on universal 1/2 inch wide ribbon onto them, remove any eyeletes which aren't needed and may interfere with the auto reverse. https://www.youtube.com/watch?v=TMDfGkKqbgE

Incidentally when browsing YouTube for repair videos, the mechanics of all the Royal standards (listed above) are all incredibly similar if not exactly the same, so search beyond KMG to find solutions.

For cleaning:<br /> - https://www.youtube.com/watch?v=xjumGF9NFE8&list=PLJtHauPh529XYHI5QNj5w9PUdi89pOXsS&index=5<br /> - https://boffosocko.com/2024/08/09/on-colloquial-advice-for-degreasing-cleaning-and-oiling-manual-typewriters/ - The tombstone "glass" (acetate) keys are metal rings that hold a piece of acetate over a paper legend (with the key letter printed on it) onto a metal platform. Don't get liquids or water on these as it will seep inside and discolor or damage the paper legends. They're replaceable, but it requires a special tool and/or lots of patience. Incidentally, these were the last US manufactured typewriters with glass keys.

Use and maintenance: https://boffosocko.com/2025/06/06/typewriter-use-and-maintenance-for-beginning-to-intermediate-typists/

If it helps, here's a link to all my posts about the purchase, history, use and some restoration pieces I've written about mine (start at the oldest and work your way forward): https://boffosocko.com/tag/royal-kmg/

Other resources as you may need them: https://boffosocko.com/research/typewriter-collection/

Good luck!

reply to u/Saltiend at https://reddit.com/r/typewriters/comments/1rwsfxp/just_bought_a_royal_kmg_any_tips/

Reviewer #1 (Public review):

Summary:

Severe childhood malaria is associated with three main overlapping syndromes: impaired consciousness (IC), respiratory distress (RD), and severe malaria anaemia (SMA). One central feature of severe malaria, driven by host and parasite factors, is the sequestration of parasitized red blood cells in vascular beds, leading to impaired tissue perfusion and lactic acidosis. The causing agent, the parasite ligand PfEMP1, is expressed on the surface of infected red blood cells, where it binds to a broad range of different endothelial receptors. Accumulation of parasite-infected erythrocytes in the host's microvasculature has been repeatedly confirmed for cerebral malaria, but there are scarce data on the extent of sequestration in the other severe malaria syndromes. However, the absence of effective adjunctive therapies for severe malaria implies that our understanding of its pathogenesis remains incomplete. Thus, by comparing var gene expression from a large Kenyan cohort (n=372 severe cases; n=340 non-severe cases), this study addresses a critical knowledge gap regarding the role of PfEMP1 across distinct severe malaria syndromes. The substantial sample size, phenotypic stratification, and use of two complementary methods (DBLa-tag sequencing and RT-qPCR), along with data about the parasite's ability to form rosettes and antibody level assessments, provide a strong setup. Var gene expression data - either proportions of different DBLa-tags classified by the number of cysteine residues and presence of particular motifs or relative expression RT-qPCR data from a set of primer pairs targeting conserved regions of var groups or particular domains - is associated with (a) severe malaria syndromes, (b) variant expression homogeneity, (c) rosetting ability, and (d) mortality using independent linear regression models, spearman ranks correlations, or logistic regression models. In summary, the study confirms that A-type and DC8-containing gene expression correlate with IC, that RD is associated with rosetting, and that SMA is linked to a high variant expression homogeneity (VEH) of var-A expression, which may indicate a longer infection duration. However, some findings remain inconclusive. For example, when analyzing pure syndromes, several associations changed: DC8 expression was also found to be significantly enriched in SMA (with multiple primer pairs) and RD, not exclusively with IC. Additionally, rosetting was associated with DC8 expression but not with IC, even though IC itself is linked to DC8 expression. Overall, the findings are significant and supported by a large dataset, though the reported evidence remains largely associative rather than mechanistic.

Strengths:

As the authors stated themselves, one of the key unresolved questions is whether severity-causing parasites are biologically different from parasites responsible for asymptomatic infections. This study is among the first to address this question using data from a large, phenotypically stratified cohort. The use of two complementary methods (DBLa-tag sequencing and RT-qPCR), together with data on the parasites' ability to form rosettes and assessments of antibody levels, provides an excellent experimental framework.

Weaknesses:

Even when assessing var gene expression using two different approaches - DBLα-tag sequencing and RT-qPCR targeting pre-defined variants - only a glimpse of the parasites' actual biology is captured. Moreover, a well-known confounder in gene expression studies of P. falciparum field isolates is variation in parasite age (hours post-invasion) or synchronicity, both of which significantly influence var gene expression. The methods employed in this study, unfortunately, do not allow for controlling or correcting for these factors. Then, the old classification system of DBLa-tag data developed by Bull et al is certainly still valid; however, more recent advances in bioinformatic tool development now allow for a more in-depth exploration of DBLa-tag datasets. Tools such as Varia (doi: 10.1186/s12859-022-04573-6), cUPS (https://doi.org/10.1371/journal.ppat.1012813), and upsML (doi: https://doi.org/10.1101/2025.05.19.654848) enable the prediction of DBLa-tag-connected PfEMP1 domains and the var group affiliations.

As A-type var gene expression has already been associated with severity, most expression studies (including this one) have a selection bias towards A- and B/A-type var genes. Here, A- and B/A-types are covered by 8 primer pairs (gpA1, gpA2, 4x DC8, DC13, DC4), whereas high polymorphic B-types are targeted by only 2 primer pairs (b1, DC9) and C-types only by a single primer (c2). Thus, any association with A-type expression is more likely to be observed, although evidence is accumulating that parasites are preferably expressing B-type var genes at the onset of blood stage infection in naïve/less immune individuals; this is also consistent with the observation of the authors that VEH is positively associated with immunity (measured as anti-IE) and negatively associated with temperature.<br /> I am not an expert in biostatistics, but to my understanding, independently performed regressions should be corrected for multiple testing.

Overall, the authors largely achieved their aims, identifying specific var groups associated with different severity syndromes. However, due to the complexity of var gene data and the interdependence of parameters, the resulting picture is not entirely clear. Some opposite results between different analyses may also be difficult for the reader to interpret. Nevertheless, this study can be considered a pioneering effort, providing valuable insights into the complex interplay of var gene expression across different severity syndromes and offering useful data for the field. Follow-up studies will be important to validate these findings and further dissect the mechanisms linking parasites gene expression to clinical outcomes.

Comment by Janneke_Adema: Comment by onewheeljoe:

For example, we might simply ask that each participant refrain from using hashtags as a final thought because that is a form of sarcasm or punchline that can be misconstrued or shut down honest debate or agreeable disagreement.

We could ask respondents to reply to any comment that they read twice because of tone to use "ouch" as a tag or a textual response. The offending respondent could respond with "oops" in order to preserve good will in an exchange of ideas.

Finally, the first part of a flash mob might occur here, in the page notes, where norms could be quickly negotiated and agreed upon with a form of protocol.

Unclear + error

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Zeng et al. have investigated the impact of inhibiting lactate dehydrogenase (LDH) on glycolysis and the tricarboxylic acid cycle. LDH is the terminal enzyme of aerobic glycolysis or fermentation that converts pyruvate and NADH to lactate and NAD+ and is essential for the fermentation pathway as it recycles NAD+ needed by upstream glyceraldehyde-3-phosphate dehydrogenase. As the authors point out in the introduction, multiple published reports have shown that inhibition of LDH in cancer cells typically leads to a switch from fermentative ATP production to respiratory ATP production (i.e., glucose uptake and lactate secretion are decreased, and oxygen consumption is increased). The presumed logic of this metabolic rearrangement is that when glycolytic ATP production is inhibited due to LDH inhibition, the cell switches to producing more ATP using respiration. This observation is similar to the well-established Crabtree and Pasteur effects, where cells switch between fermentation and respiration due to the availability of glucose and oxygen. Unexpectedly, the authors observed that inhibition of LDH led to inhibition of respiration and not activation as previously observed. The authors perform rigorous measurements of glycolysis and TCA cycle activity, demonstrating that under their experimental conditions, respiration is indeed inhibited. Given the large body of work reporting the opposite result, it is difficult to reconcile the reasons for the discrepancy. In this reviewer's opinion, a reason for the discrepancy may be that the authors performed their measurements 6 hours after inhibiting LDH. Six hours is a very long time for assessing the direct impact of a perturbation on metabolic pathway activity, which is regulated on a timescale of seconds to minutes. The observed effects are likely the result of a combination of many downstream responses that happen within 6 hours of inhibiting LDH that causes a large decrease in ATP production, inhibition of cell proliferation, and likely a range of stress responses, including gene expression changes.

Strengths:

The regulation of metabolic pathways is incompletely understood, and more research is needed, such as the one conducted here. The authors performed an impressive set of measurements of metabolite levels in response to inhibition of LDH using a combination of rigorous approaches.

Weaknesses:

Glycolysis, TCA cycle, and respiration are regulated on a timescale of seconds to minutes. The main weakness of this study is the long drug treatment time of 6 hours, which was chosen for all the experiments. In this reviewer's opinion, if the goal was to investigate the direct impact of LDH inhibition on glycolysis and the TCA cycle, most of the experiments should have been performed immediately after or within minutes of LDH inhibition. After 6 hours of inhibiting LDH and ATP production, cells undergo a whole range of responses, and most of the observed effects are likely indirect due to the many downstream effects of LDH and ATP production inhibition, such as decreased cell proliferation, decreased energy demand, activation of stress response pathways, etc.

We thank reviewer for the careful reading of our manuscript, the accurate summary of the prevailing model, and the positive assessment of the rigor of our measurements. We agree that much prior literature reports increased oxygen consumption following LDH inhibition, and we recognize that our finding—coordinated suppression of glycolysis, the TCA cycle, and OXPHOS—differs from this prevailing interpretation. We address below the reviewer’s main concern regarding the 6-hour time point and clarify the conceptual scope of our study.

(1) Scope: steady-state metabolic regulation versus immediate transient effects

The reviewer raises an important point that many metabolic perturbations can trigger rapid, transient responses within seconds to minutes, whereas our measurements were performed after sustained LDH inhibition. We agree that very early time points would be required if the primary goal were to isolate the most immediate, proximal consequence of LDH inhibition before downstream propagation. However, the objective of our study is different: we aim to characterize the metabolic steady state re-established after sustained inhibition of LDH activity, because this adapted steady state is more relevant for understanding long-term metabolic consequences and therapeutic outcomes of LDH inhibition in cancer cells.

(2) Genetic LDHA/LDHB knockout: comparison of two steady states

A related point applies to the LDHA/LDHB knockout models. We fully agree that the knockout process necessarily involves a temporal perturbation during cell line generation and adaptation. Nevertheless, the experimental comparison in our study is explicitly between two steady states: the baseline steady state of control cells and the steady state achieved after stable genetic disruption of LDHA or LDHB. The observation that LDHA or LDHB knockout alone had minimal effects on glycolysis and respiration indicates that partial reduction of LDH activity can be compensated in a steady-state manner, consistent with the exceptionally high catalytic capacity of LDH in cancer cells relative to upstream rate-limiting enzymes.

(3) LDH-activity-dependent quantitative relationships support stable metabolic states

Importantly, our conclusions do not rely on a single inhibitor condition at a single time point. Rather, we established quantitative steady-state relationships between residual LDH activity and pathway behavior across a wide range of LDH inhibition. These LDH-activity-dependent data strongly support that the system resides in stable metabolic states at different degrees of LDH activity, rather than reflecting non-specific collapse due to prolonged stress.

Specifically, we observed that when LDH activity was reduced from 100% to approximately ~9% (e.g., by genetic perturbation and partial pharmacologic inhibition), glucose consumption and lactate production remained essentially unchanged, indicating maintenance of a steady-state glycolytic flux despite substantial LDH inhibition. Only when LDH activity was further reduced below this threshold did glycolytic flux decrease in a graded manner, consistent with a nonlinear control structure (Figure 8 A & B)).

Likewise, the isotope tracing results showed distinct LDH-activity-dependent transitions in TCA cycle labeling patterns. Over the range in which LDH activity decreased from 100% to ~9%, the [¹³C₆]glucose-derived labeling pattern of citrate remained largely unchanged, whereas deeper inhibition led to a decrease in m2 citrate with a compensatory rise in higher-order citrate isotopologues, consistent with altered flux entry versus cycling/retention in the TCA cycle (Figure 8C). Similarly, [¹³C₅]glutamine tracing revealed that deeper LDH inhibition reduced the direct m5 contribution, accompanied by corresponding shifts in other isotopologues (Figure 8D). These graded, quantitative transitions—rather than an abrupt global failure—support the interpretation of distinct metabolic steady states across LDH activity levels, linking LDH inhibition to changes in both glycolysis and mitochondrial metabolism.

(4) Reconciling discrepancies with prior studies

We agree that multiple prior studies have reported increased oxygen consumption or enhanced oxidative metabolism following LDH inhibition in cancer cells. However, we note that this prevailing notion often persists because LDH inhibition is frequently discussed by analogy to the classical Pasteur and Crabtree effects, in which cells toggle between fermentation and respiration depending on oxygen and glucose availability. We believe this analogy can be misleading.

In the Pasteur effect, the metabolic shift is primarily driven by oxygen limitation, i.e., restriction of the terminal electron acceptor for the mitochondrial electron transport chain, which enforces reliance on fermentation. In the Crabtree effect, high glucose availability suppresses respiration through regulatory mechanisms while glycolysis is strongly activated. Both phenomena are fundamentally controlled by oxygen availability and respiratory capacity, rather than by inhibition of a specific cytosolic enzyme.

By contrast, LDH inhibition is mechanistically distinct: it directly perturbs cytosolic redox recycling by limiting NADH-to-NAD⁺ regeneration and can therefore constrain upstream glycolytic flux (particularly at GAPDH) and reshape pathway thermodynamics. Under conditions where LDH inhibition sufficiently limits effective NAD⁺ availability and reduces glycolytic flux into pyruvate, the downstream consequence is reduced carbon input into the TCA cycle and suppressed OXPHOS—consistent with our experimental measurements. We therefore suggest that divergent outcomes reported across studies likely reflect differences in residual LDH activity, cell-type–specific metabolic wiring, and the extent to which glycolytic flux remains sustained versus becoming redox-limited upstream, rather than a universal Pasteur/Crabtree-like “switch” from fermentation to respiration. Accordingly, interpreting LDH inhibition as a Pasteur/Crabtree-like toggle may oversimplify the biochemical consequences of disrupting cytosolic NAD⁺ regeneration.

We have revised the Discussion to clarify this conceptual distinction and to avoid relying on comparisons that are not mechanistically equivalent to LDH inhibition.

Reviewer #2 (Public Review):

Summary:

Zeng et al. investigated the role of LDH in determining the metabolic fate of pyruvate in HeLa and 4T1 cells. To do this, three broad perturbations were applied: knockout of two LDH isoforms (LDH-A and LDH-B), titration with a non-competitive LDH inhibitor (GNE-140), and exposure to either normoxic (21% O2) or hypoxic (1% O2) conditions. They show that knockout of either LDH isoform alone, though reducing both protein level and enzyme activity, has virtually no effect on either the incorporation of a stable 13C-label from a 13C6-glucose into any glycolytic or TCA cycle intermediate, nor on the measured intracellular concentrations of any glycolytic intermediate (Figure 2). The only apparent exception to this was the NADH/NAD+ ratio, measured as the ratio of F420/F480 emitted from a fluorescent tag (SoNar).

The addition of a chemical inhibitor, on the other hand, did lead to changes in glycolytic flux, the concentrations of glycolytic intermediates, and in the NADH/NAD+ ratio (Figure 3). Notably, this was most evident in the LDH-B-knockout, in agreement with the increased sensitivity of LDH-A to GNE-140 (Figure 2). In the LDH-B-knockout, increasing concentrations of GNE-140 increased the NADH/NAD+ ratio, reduced glucose uptake, and lactate production, and led to an accumulation of glycolytic intermediates immediately upstream of GAPDH (GA3P, DHAP, and FBP) and a decrease in the product of GAPDH (3PG). They continue to show that this effect is even stronger in cells exposed to hypoxic conditions (Figure 4). They propose that a shift to thermodynamic unfavourability, initiated by an increased NADH/NAD+ ratio inhibiting GAPDH explains the cascade, calculating ΔG values that become progressively more endergonic at increasing inhibitor concentrations.

Then - in two separate experiments - the authors track the incorporation of 13C into the intermediates of the TCA cycle from a 13C6-glucose and a 13C5-glutamine. They use the proportion of labelled intermediates as a proxy for how much pyruvate enters the TCA cycle (Figure 5). They conclude that the inhibition of LDH decreases fermentation, but also the TCA cycle and OXPHOS flux - and hence the flux of pyruvate to all of those pathways. Finally, they characterise the production of ATP from respiratory or fermentative routes, the concentration of a number of cofactors (ATP, ADP, AMP, NAD(P)H, NAD(P)+, and GSH/GSSG), the cell count, and cell viability under four conditions: with and without the highest inhibitor concentration, and at norm- and hypoxia. From this, they conclude that the inhibition of LDH inhibits the glycolysis, the TCA cycle, and OXPHOS simultaneously (Figure 7).

Strengths:

The authors present an impressively detailed set of measurements under a variety of conditions. It is clear that a huge effort was made to characterise the steady-state properties (metabolite concentrations, fluxes) as well as the partitioning of pyruvate between fermentation as opposed to the TCA cycle and OXPHOS.

A couple of intermediary conclusions are well supported, with the hypothesis underlying the next measurement clearly following. For instance, the authors refer to literature reports that LDH activity is highly redundant in cancer cells (lines 108 - 144). They prove this point convincingly in Figure 1, showing that both the A- and B-isoforms of LDH can be knocked out without any noticeable changes in specific glucose consumption or lactate production flux, or, for that matter, in the rate at which any of the pathway intermediates are produced. Pyruvate incorporation into the TCA cycle and the oxygen consumption rate are also shown to be unaffected.

They checked the specificity of the inhibitor and found good agreement between the inhibitory capacity of GNE-140 on the two isoforms of LDH and the glycolytic flux (lines 229 - 243). The authors also provide a logical interpretation of the first couple of consequences following LDH inhibition: an increased NADH/NAD+ ratio leading to the inhibition of GAPDH, causing upstream accumulations and downstream metabolite decreases (lines 348 - 355).

Weaknesses:

Despite the inarguable comprehensiveness of the data set, a number of conceptual shortcomings afflict the manuscript. First and foremost, reasoning is often not pursued to a logical conclusion. For instance, the accumulation of intermediates upstream of GAPDH is proffered as an explanation for the decreased flux through glycolysis. However, in Figure 3C it is clear that there is no accumulation of the intermediates upstream of PFK. It is unclear, therefore, how this traffic jam is propagated back to a decrease in glucose uptake. A possible explanation might lie with hexokinase and the decrease in ATP (and constant ADP) demonstrated in Figure 6B, but this link is not made.

We appreciate the reviewer's critical comment. In Figure 3C, there is no accumulation of F6P or G6P, which are upstream of PFK1. This is because the PFK1-catalyzed reaction sets a significant thermodynamic barrier. Even with treatment using 30 μM GNE-140, the ∆G_PFK1 (Gibbs free energy of the PFK1-catalyzed reaction) remains -9.455 kJ/mol (Figure 3D), indicating that the reaction is still far from thermodynamic equilibrium, thereby preventing the accumulation of F6P and G6P.

We agree with the reviewer that hexokinase inhibition may play a role, this requires further investigation.

The obvious link between the NADH/NAD+ ratio and pyruvate dehydrogenase (PDH) is also never addressed, a mechanism that might explain how the pyruvate incorporation into the TCA cycle is impaired by the inhibition of LDH (the observation with which they start their discussion, lines 511 - 514).

We agree with the reviewer’s comment. In this study, we did not explore how the inhibition of LDH affects pyruvate incorporation into the TCA cycle. As this mechanism was not investigated, we have titled the study:

"Elucidating the Kinetic and Thermodynamic Insights into the Regulation of Glycolysis by Lactate Dehydrogenase and Its Impact on the Tricarboxylic Acid Cycle and Oxidative Phosphorylation in Cancer Cells."

It was furthermore puzzling how the ΔG, calculated with intracellular metabolite concentrations (Figures 3 and 4) could be endergonic (positive) for PGAM at all conditions (also normoxic and without inhibitor). This would mean that under the conditions assayed, glycolysis would never flow completely forward. How any lactate or pyruvate is produced from glucose, is then unexplained.

This issue also concerned me during the study. However, given the high reproducibility of the data, we consider it is true, but requires explanation. The PGAM-catalyzed reaction is tightly linked to both upstream and downstream reactions in the glycolytic pathway. In glycolysis, three key reactions catalyzed by HK2, PFK1, and PK are highly exergonic, providing the driving force for the conversion of glucose to pyruvate. The other reactions, including the one catalyzed by PGAM, operate near thermodynamic equilibrium and primarily serve to equilibrate glycolytic intermediates rather than control the overall direction of glycolysis, as previously described by us (J Biol Chem. 2024 Aug8;300(9):107648).

The endergonic nature of the PGAM-catalyzed reaction does not prevent it from proceeding in the forward direction. Instead, the directionality of the pathway is dictated by the exergonic reaction of PFK1 upstream, which pushes the flux forward, and by PK downstream, which pulls the flux through the pathway. The combined effects of PFK1 and PK may account for the observed endergonic state of the PGAM reaction.

However, if the PGAM-catalyzed reaction were isolated from the glycolytic pathway, it would tend toward equilibrium and never surpass it, as there would be no driving force to move the reaction forward.

Finally, the interpretation of the label incorporation data is rather unconvincing. The authors observe an increasing labelled fraction of TCA cycle intermediates as a function of increasing inhibitor concentration. Strangely, they conclude that less labelled pyruvate enters the TCA cycle while simultaneously less labelled intermediates exit the TCA cycle pool, leading to increased labelling of this pool. The reasoning that they present for this (decreased m2 fraction as a function of DHE-140 concentration) is by no means a consistent or striking feature of their titration data and comes across as rather unconvincing. Yet they treat this anomaly as resolved in the discussion that follows.

GNE-140 treatment increased the labeling of TCA cycle intermediates by [¹³C₆]glucose but decreased the OXPHOS rate, we consider the conflicting results as an 'anomaly' that warrants further explanation. To address this, we analyzed the labeling pattern of TCA cycle intermediates using both [¹³C₆]glucose and [¹³C₅]glutamine. Tracing the incorporation of glucose- and glutamine-derived carbons into the TCA cycle suggests that LDH inhibition leads to a reduced flux of glucose-derived acetyl-CoA into the TCA cycle, coupled with a decreased flux of glutamine-derived α-KG, and a reduction in the efflux of intermediates from the cycle. These results align with theoretical predictions. Under any condition, the reactions that distribute TCA cycle intermediates to other pathways must be balanced by those that replenish them. In the GNE-140 treatment group, the entry of glutamine-derived carbon into the TCA cycle was reduced, implying that glucose-derived carbon (as acetyl-CoA) entering the TCA cycle must also be reduced, or vice versa.

This step-by-step investigation is detailed under the subheading "The Effect of LDHB KO and GNE-140 on the Contribution of Glucose Carbon to the TCA Cycle and OXPHOS" in the Results section in the manuscript.

In the Discussion, we emphasize that caution should be exercised when interpreting isotope tracing data. In this study, treatment of cells with GNE-140 led to an increase labeling percentage of TCA cycle intermediates by [¹³C₆]glucose (Figure 5A-E). However, this does not necessarily imply an increase in glucose carbon flux into TCA cycle; rather, it indicates a reduction in both the flux of glucose carbon into TCA cycle and the flux of intermediates leaving TCA cycle. When interpreting the data, multiple factors must be considered, including the carbon-13 labeling pattern of the intermediates (m1, m2, m3, ---) (Figure 5G-K), replenishment of intermediates by glutamine (Figure 5M-V), and mitochondrial oxygen consumption rate (Figure 5W). All these factors should be taken into account to derive a proper interpretation of the data.

Reviewer #3 (Public Review):

Hu et al in their manuscript attempt to interrogate the interplay between glycolysis, TCA activity, and OXPHOS using LDHA/B knockouts as well as LDH-specific inhibitors. Before I discuss the specifics, I have a few issues with the overall manuscript. First of all, based on numerous previous studies it is well established that glycolysis inhibition or forcing pyruvate into the TCA cycle (studies with PDKs inhibitors) leads to upregulation of TCA cycle activity, and OXPHOS, activation of glutaminolysis, etc (in this work authors claim that lowered glycolysis leads to lower levels of TCA activity/OXPHOS). The authors in the current work completely ignore recent studies that suggest that lactate itself is an important signaling metabolite that can modulate metabolism (actual mechanistic insights were recently presented by at least two groups (Thompson, Chouchani labs). In addition, extensive effort was dedicated to understanding the crosstalk between glycolysis/TCA cycle/OXPHOS using metabolic models (Titov, Rabinowitz labs). I have several comments on how experiments were performed. In the Methods section, it is stated that both HeLa and 4T1 cells were grown in RPMI-1640 medium with regular serum - but under these conditions, pyruvate is certainly present in the medium - this can easily complicate/invalidate some findings presented in this manuscript. In LDH enzymatic assays as described with cell homogenates controls were not explained or presented (a lot of enzymes in the homogenate can react with NADH!). One of the major issues I have is that glycolytic intermediates were measured in multiple enzyme-coupled assays. Although one might think it is a good approach to have quantitative numbers for each metabolite, the way it was done is that cell homogenates (potentially with still traces of activity of multiple glycolytic enzymes) were incubated with various combinations of the SAME enzymes and substrates they were supposed to measure as a part of the enzyme-based cycling reaction. I would prefer to see a comparison between numbers obtained in enzyme-based assays with GC-MS/LC-MS experiments (using calibration curves for respective metabolites, of course). Correct measurements of these metabolites are crucial especially when thermodynamic parameters for respective reactions are calculated. Concentrations of multiple graphs (Figure 1g etc.) are in "mM", I do not think that this is correct.

We thank the reviewer’s comment and the following are clarification of the conceptual framework, the quantitative methodology, and the experimental basis supporting our conclusions.

(1) “It is well established that glycolysis inhibition or forcing pyruvate into the TCA cycle… leads to upregulation of TCA/OXPHOS… (authors claim lowered glycolysis leads to lower TCA/OXPHOS)”

This framing is not accurate in the context of our study. PDK inhibition and LDH inhibition are fundamentally different perturbations. PDK inhibition directly promotes mitochondrial pyruvate oxidation by enabling PDH flux, whereas LDH inhibition primarily perturbs cytosolic redox balance (free NADH/NAD⁺) and thereby constrains upstream glycolytic reactions, particularly the GAPDH step. Therefore, the metabolic outcomes of these interventions are not expected to be identical and should not be treated as interchangeable.

Importantly, we do not “ignore” prior studies proposing increased OXPHOS after LDH inhibition; we explicitly cite and summarize this prevailing interpretation in the Introduction. Our study was motivated precisely because this interpretation does not resolve key quantitative inconsistencies, including (i) the large mismatch between glycolytic flux and mitochondrial oxidative capacity, and (ii) the exceptionally high catalytic capacity of LDH relative to upstream rate-limiting glycolytic enzymes. These constraints raise a mechanistic question: how does LDH inhibition actually suppress glycolytic flux in intact cancer cells, and what are the consequences for TCA cycle and OXPHOS?

Our central contribution is the identification of a biochemical mechanism supported by integrated measurements of fluxes, metabolite concentrations, redox state, and reaction thermodynamics: LDH inhibition increases free NADH/NAD⁺, decreases free NAD⁺ availability, inhibits GAPDH, drives accumulation/depletion patterns in glycolytic intermediates, shifts Gibbs free energies of near-equilibrium reactions (PFK1–PGAM segment), suppresses pyruvate production, and consequently reduces carbon input into TCA cycle and OXPHOS. These analyses are not provided by most prior work and directly address the mechanistic gap.

(2) Lactate signaling (Thompson/Chouchani) and metabolic modeling (Titov/Rabinowitz)

These research directions are valuable, but they address questions that are different from the one investigated here. Our manuscript focuses on steady-state biochemical control of metabolic flux by LDH inhibition through redox-linked kinetics and pathway thermodynamics.

(3) Pyruvate in RPMI

Pyruvate in standard medium does not invalidate our conclusions. All experimental comparisons were performed under identical conditions across groups, and the major conclusions rely on orthogonal measurements including glycolytic flux (glucose consumption/lactate production), OCR profiling, and isotope tracing with [¹³C₆]glucose and [¹³C₅] glutamine, which directly quantify carbon entry into lactate and TCA cycle intermediates. These tracer-based results are not confounded by unlabeled extracellular pyruvate in a way that would reverse the mechanistic conclusions.

(4) LDH activity assay in homogenates and “many enzymes can react with NADH”

This concern is overstated. In the LDH assay, substrates are pyruvate + NADH, and the measured signal reflects NADH oxidation coupled to pyruvate reduction. In cell lysates, LDH is uniquely abundant and catalytically efficient for this reaction pair, and the inhibitor-response behavior matches the known LDHA/LDHB selectivity of GNE-140 and the cellular phenotypes. Thus, the assay is mechanistically specific in this context.

(5) Enzyme-coupled metabolite assays and request for LC–MS validation

The reviewer’s implication that enzyme-coupled assays are intrinsically unreliable is incorrect. Enzymatic cycling assays are a widely used quantitative approach when performed with proper specificity and calibration, and they are particularly useful for labile glycolytic intermediates that are challenging to quantify reproducibly by MS without specialized quenching, derivatization, and isotope dilution standards.

We agree that MS-based quantification is valuable, and we have developed LC–MS methods for selected metabolites. However, absolute quantification of these intermediates remains technically difficult due to the inherent limitation of this method and, in our hands, did not provide uniformly robust performance for all intermediates required for thermodynamic analysis.

(6) Units (“mM”)

The metabolite concentration units are correct.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

If the goal is to investigate the direct impact of LDH inhibition, then in my opinion, most of these experiments need to be repeated at a very early time point immediately after or a few minutes after LDH inhibition. I understand that this is a tremendous amount of work that the authors might not want to pursue. I do want to highlight that the quality of the experiments performed in this work is impressive. I hope the authors continue investigating this subject and look forward to reading their future manuscripts on this topic.

We thank the reviewer for this thoughtful and constructive comment and for the positive assessment of the experimental quality of our work.

We fully agree that measurements at very early time points after LDH inhibition would be required if the goal were to isolate an immediate, proximal molecular event occurring before downstream propagation. However, the primary objective of our study is not to dissect a single instantaneous biochemical consequence of LDH inhibition, but rather to characterize the metabolic steady state that is re-established after sustained suppression of LDH activity, which we believe is more relevant for understanding the long-term metabolic and therapeutic consequences of LDH inhibition in cancer cells.

(1) Scope: steady-state metabolic regulation versus immediate transient effects

The reviewer raises an important point that many metabolic perturbations can trigger rapid, transient responses within seconds to minutes, whereas our measurements were performed after sustained LDH inhibition. We agree that very early time points would be required if the primary goal were to isolate the most immediate, proximal consequence of LDH inhibition before downstream propagation. However, the objective of our study is different: we aim to characterize the metabolic steady state re-established after sustained inhibition of LDH activity, because this adapted steady state is more relevant for understanding long-term metabolic consequences and therapeutic outcomes of LDH inhibition in cancer cells.

(2) Genetic LDHA/LDHB knockout: comparison of two steady states

A related point applies to the LDHA/LDHB knockout models. We fully agree that the knockout process necessarily involves a temporal perturbation during cell line generation and adaptation. Nevertheless, the experimental comparison in our study is explicitly between two steady states: the baseline steady state of control cells and the steady state achieved after stable genetic disruption of LDHA or LDHB. The observation that LDHA or LDHB knockout alone had minimal effects on glycolysis and respiration indicates that partial reduction of LDH activity can be compensated in a steady-state manner, consistent with the exceptionally high catalytic capacity of LDH in cancer cells relative to upstream rate-limiting enzymes.

(3) LDH-activity-dependent quantitative relationships support stable metabolic states

Importantly, our conclusions do not rely on a single inhibitor condition at a single time point. Rather, we established quantitative steady-state relationships between residual LDH activity and pathway behavior across a wide range of LDH inhibition. These LDH-activity-dependent data strongly support that the system resides in stable metabolic states at different degrees of LDH activity, rather than reflecting non-specific collapse due to prolonged stress.

Specifically, we observed that when LDH activity was reduced from 100% to approximately ~9% (e.g., by genetic perturbation and partial pharmacologic inhibition), glucose consumption and lactate production remained essentially unchanged, indicating maintenance of a steady-state glycolytic flux despite substantial LDH inhibition. Only when LDH activity was further reduced below this threshold did glycolytic flux decrease in a graded manner, consistent with a nonlinear control structure.

Likewise, the isotope tracing results showed distinct LDH-activity-dependent transitions in TCA cycle labeling patterns. Over the range in which LDH activity decreased from 100% to ~9%, the [¹³C₆]glucose-derived labeling pattern of citrate remained largely unchanged, whereas deeper inhibition led to a decrease in m2 citrate with a compensatory rise in higher-order citrate isotopologues, consistent with altered flux entry versus cycling/retention in the TCA cycle. Similarly, [¹³C₅]glutamine tracing revealed that deeper LDH inhibition reduced the direct m5 contribution, accompanied by corresponding shifts in other isotopologues. These graded, quantitative transitions—rather than an abrupt global failure—support the interpretation of distinct metabolic steady states across LDH activity levels, linking LDH inhibition to changes in both glycolysis and mitochondrial metabolism.

Reviewer #2 (Recommendations For The Authors):

All in all, the authors would benefit from collaboration with a group more well-versed in quantitative aspects of metabolism (such as Metabolic Control Analysis) and modelling methods (such as flux analysis) to boost the interpretation and impact of their really nice data set.

We sincerely thank the reviewer for this insightful and constructive suggestion. We fully agree that collaboration with groups specializing in quantitative metabolic analysis, such as Metabolic Control Analysis and flux modeling, would further expand the interpretative depth and broader impact of this work.

The primary objective of the present work, however, was not to construct a global mathematical model, but to experimentally dissect the biochemical mechanism by which LDH inhibition coordinately suppresses glycolysis, the TCA cycle, and OXPHOS, integrating enzyme kinetics with thermodynamic constraints at steady state. Within this scope, we focused on experimentally demonstrable relationships between LDH activity, redox balance, GAPDH perturbation, thermodynamic shifts in near-equilibrium reactions, and emergent flux suppression.

We fully recognize the power of MCA and related modeling approaches in formalizing control coefficients and system-level sensitivities, and we view our dataset as particularly well suited to support such future analyses. We therefore see this work as providing a robust experimental platform upon which more comprehensive quantitative modeling can be built, either in future studies or through collaboration with specialists in metabolic modeling.

Reviewer #3 (Recommendations For The Authors):

We sincerely thank the reviewer for the important suggestions.

(1) I strongly disagree that "regulation of glycolytic flux".. "remained largely unexplored.”

Our original wording was meant to emphasize not the absence of prior work on glycolytic flux regulation, but rather that the specific biochemical mechanism by which LDH regulates glycolytic flux—particularly through the integrated effects of enzyme kinetics, redox balance, and thermodynamic constraints within the pathway—has not been fully elucidated.

To avoid any ambiguity or overstatement, we have revised the relevant text to more precisely reflect this intent. The revised wording now reads:

“This study elucidates a biochemical mechanism by which lactate dehydrogenase influences glycolytic flux in cancer cells, revealing a kinetic–thermodynamic interplay that contributes to metabolic regulation.”

We believe this revised phrasing more accurately acknowledges prior work while clearly defining the specific mechanistic contribution of the present study.

(2) Very confusing in the Introduction section: "If LDH is inhibited at the LDH step..”

We sincerely thank the reviewer for pointing out the potential confusion caused by the phrase “If LDH is inhibited at the LDH step” in the Introduction.

Our intention was to contrast two conceptual models of LDH inhibition. The first is the conventional view, in which the effect of LDH inhibition is assumed to be confined to the LDH-catalyzed reaction itself, leading primarily to local accumulation of pyruvate and its redirection toward mitochondrial metabolism. The second, which is supported by our data, is that LDH inhibition initiates a system-wide biochemical response, perturbing redox balance, upstream enzyme kinetics, and the thermodynamic state of the glycolytic pathway, ultimately resulting in coordinated suppression of glycolysis, the TCA cycle, and OXPHOS.

We agree that the original phrasing was ambiguous and potentially misleading. To improve clarity, we have revised the text as follows:

“If the effect of LDH inhibition were confined solely to its catalytic step…”

(3) The entire introduction part when the authors attempt to explain how decreased glycolysis will lead to decreased mitochondrial respiration is confusing.

We would like to clarify that the Introduction does not attempt to explain how decreased glycolysis leads to decreased mitochondrial respiration. Rather, the final paragraph of the Introduction is intended to highlight an unresolved conceptual inconsistency in the existing literature and to motivate the central question addressed in this study.

Specifically, we summarize the prevailing view that LDH inhibition redirects pyruvate toward mitochondrial metabolism and enhances oxidative phosphorylation, and then point out that this interpretation is difficult to reconcile with quantitative considerations, such as the large disparity between glycolytic and mitochondrial flux capacities and the excess catalytic activity of LDH relative to upstream glycolytic enzymes. These observations are presented to emphasize that the biochemical mechanism linking LDH inhibition to changes in glycolysis and mitochondrial respiration has not been fully resolved.

Importantly, the Introduction does not propose a mechanistic explanation for the observed suppression of mitochondrial respiration; rather, it poses this as an open question, which is then systematically addressed through experimental analysis in the Results section.

(4) Line 144: "which is 81(HeLa-LDHAKO) -297(HeLa-Ctrl) times"- here and in many other places wording is confusing to the reader.

Our intention was to emphasize the significant redundancy of LDH activity relative to hexokinase (HK), the first rate-limiting enzyme in the glycolysis pathway, in cancer cells.

Specifically, we wanted to express that in HeLa-Ctrl cells, the total LDH activity is 297 times that of HK activity; while in HeLa-LDHAKO cells, although the total LDH activity decreased, it was still 81 times that of HK activity. This data comes from supplement Table 1 in the paper and aims to provide quantitative evidence for "why knocking out LDHA or LDHB alone is insufficient to significantly affect glycolysis flux," because the remaining LDH activity is still far higher than the HK activity at the pathway entrance, sufficient to maintain flux.

Based on your suggestion, we rewrite it in the revised draft with a more specific statement: "...the total activity of LDH in HeLa cells is very high, which is 297-fold higher than the first rate-limiting enzyme HK activity in HeLa-Ctrl cells and 81-fold higher in HeLa-LDHAKO cells.”

(5) Line 153: "in the following four aspects:"- but what are these aspects, the text below has no corresponding subtitles, etc.

Our intention was to indicate that after LDHA or LDHB knockout alone failed to affect the glycolysis rate, we further explored its potential impact on the glycolytic pathway from four deeper perspectives: the glucose carbon to pyruvate and lactate, the glucose carbon to subsidiary branches of glycolysis, the concentration of glycolytic intermediates and the thermodynamic state of the pathway, and the redox state of cytosolic free NADH/NAD⁺.

Following your valuable suggestion, we have now added the aforementioned clear subtitles to these four aspects in the revised manuscript.

(6) Lines 193, another example of the very confusing statement: "The results suggested that the loss of total LDH concentration was compensated.."

The actual catalytic activity (reaction rate) of LDH is determined by both its enzyme concentration and substrate concentration (pyruvate and NADH). When the total LDH protein concentration (enzyme amount) in the cell is reduced through gene knockout, the reaction equilibrium is disrupted. To maintain sufficient lactate production flux to support a high glycolysis rate, the cell compensates by increasing the concentration of one of the substrates—free NADH (as shown in Figure 1I). This results in an increased substrate concentration, despite a reduction in the amount of enzyme, thus partially maintaining the overall reaction rate.

We have revised the original statement to more accurately describe this kinetic equilibrium process: "The decrease in total LDH concentration was counterbalanced by a concomitant increase in the concentration of its substrate, free NADH, thereby maintaining the reaction velocity.”

(7) Line 222-223: "did not or marginally significantly affect....”

Our intention is to reflect the complexity of the data in Figure 1. Specifically: Regarding "did not affect": This means that there were no statistically significant differences in most key parameters, such as glycolytic flux (glucose consumption rate, lactate production rate). Regarding "or marginally significantly affected": This means that in a few indicators, although statistical calculations showed p-values less than 0.05, the absolute value of the difference was very small, with limited biological significance.

To clarify this, we rewrite it as: "...did not significantly affect glucose-derived pyruvate entering into TCA cycle, neither significantly affect mitochondrial respiration, although statistically significant but minimal changes were observed in a few specific parameters (e.g., m3-pyruvate% in medium).”

(8) It is very confusing to use the same colors for three GNE-140 drug concentrations (Figure 2a-b) and for 3 different cell lines right next to each other (Figure 2c-d).

The figures have been revised accordingly.

(9) Lines 263-273: nothing is new here as oxidized NAD+ is required for run glycolysis and LDH inhibition/KO leads to a high NADH/NAD+ ratio; Also below it is well known that reductive stress blocks serine biosynthesis;

It is well established that oxidized NAD⁺ is required for glycolysis, that LDH inhibition or knockout increases the NADH/NAD⁺ ratio, and that reductive stress can suppress serine biosynthesis. We did not intend to present these observations as novel.

The key point of this section is not the qualitative requirement of NAD⁺ for GAPDH, but rather the mechanistic alignment between LDH inhibition, changes in free NAD⁺ availability, and the emergence of GAPDH as a flux-controlling step within the glycolytic pathway under steady-state conditions. Previous studies have largely treated the increase in NADH/NAD⁺ following LDH inhibition as a correlative or downstream effect, without directly demonstrating how this redox shift quantitatively propagates upstream to reorganize glycolytic flux distribution and thermodynamic driving forces.

In our study, we explicitly link LDH inhibition to (i) an increase in free NADH/NAD⁺ ratio, (ii) inhibition of GAPDH activity in intact cells, (iii) accumulation of upstream glycolytic intermediates, (iv) suppression of serine biosynthesis from 3-phosphoglycerate, and critically, (v) coordinated shifts in the Gibbs free energies of reactions between PFK1 and PGAM. This integrated kinetic–thermodynamic framework goes beyond the established qualitative understanding of NAD⁺ dependence and provides a pathway-level mechanism by which LDH activity controls glycolytic flux.

(10) Lines 368-370: "... we reached an alternative interpretation of the data.."- does not provide much confidence.

Our intention was to prudently emphasize that we proposed a new interpretation based on detailed data, differing from conventional views. Our interpretation is grounded in key and consistent evidence from dual isotope tracing experiments using [¹³C₆]glucose and [¹³C₅]glutamine: The [¹³C₆]glucose tracing data: the labeling pattern of citrate, the starting product of TCA cycle, showed a significant decrease in m+2 %. This directly reflects a reduction in the flux of newly generated acetyl-CoA from glucose entering the TCA cycle. Simultaneously, the sum of other isotopologues % (m+1/ m+3/ m+4/m+5/m+6) increased, indicating a longer retention time of the labeled carbon in the cycle, implying a simultaneous decrease in the flux of cycle intermediates effluxed for biosynthesis. [¹³C₅]Glutamine tracing data: the labeling pattern of α-ketoglutarate showed a decrease in m+5 %, indicating a reduction in glutamine replenishment flux. The pattern of change in the total percentage of other isotopologues % (m+1/ m+2/ m+3/m+4) also supports the conclusion of reduced intermediate product efflux.

These two sets of data corroborate each other, pointing to a unified conclusion: LDH inhibition not only reduces carbon source inflow into the TCA cycle but also decreases intermediate product efflux, leading to a decrease in overall cycle activity. Therefore, our "alternative interpretation" is a well-supported and more consistent explanation of our overall experimental results. We revise the original wording to: "Integrated analysis of dual isotope tracing data demonstrates that LDH inhibition reduces both influx and efflux of the TCA cycle..."

(11) Lines 418-421: This entire discussion on how TCA cycle activity is decreased upon LDH inhibition is very confusing. I also would like to see these tracer studies when ETC is inhibited with different inhibitors.

We would like to clarify that the mitochondrial respiration rate data presented in Figure 5W are based on studies using different ETC inhibitors, and the cell treatment conditions (including culture time, etc.) for these oxygen consumption measurements are consistent with the conditions for the [¹³C₆]glucose and [¹³C₅]glutamine isotope tracing experiments (Figure 5A-V). Therefore, the changes in TCA cycle flux revealed by the tracing data and the inhibition of OXPHOS rate shown by the respiration measurements are mutually corroborating evidence from the same experimental conditions.

(12) Figure 6F, G - very limited representation of growth curves, why not perform these experiments with all corresponding cell lines and over multiple days. Especially since proliferation arrest vs cell death was implicated.

We have provided the growth curves of the HeLa-Ctrl and HeLa-LDHAKO cell lines under the corresponding treatments in Figure 6—figure supplement 1, as a supplement to Figure 6F, G (HeLa-LDHBKO cells). The choice of 48 hours as the cutoff observation point is based on clear biological evidence: under the stress of hypoxia (1% O₂) combined with GNE-140 treatment, HeLa-LDHBKO cells experienced substantial death within 24 to 48 hours, at which point the differences in the growth curves were already very significant.

(13) Move most of the Supplementary tables into an Excel file - so values can be easily accessed.

We have compiled the tables into an Excel file and submitted it along with the revised manuscript as supplementary material.

(14) Consider changing colors to more appealing- especially jarring is a bright blue, red, black combination on many bar graphs.

We have adjusted the color scheme of the figures (especially the bar graphs) in the paper, and have submitted them with the revised manuscript.

(15) Double check y-axis on multiple graphs it says "mM".

We have checked y-axis, the unit (mM) is correct.

(16) Instead TCA cycle use the TCA cycle.

In the revised manuscript, TCA cycle is used.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study by Xu et al. focuses on the impact of clathrin-independent endocytosis in cancer cells on T cell activation. In particular, by using a combination of biochemical approaches and imaging, the authors identify ICAM1, the ligand for T cell-expressed integrin LFA-1, as a novel cargo for EndoA3-mediated endocytosis. Subsequently, the authors aim to identify functional implications for T cell activation, using a combination of cytokine assays and imaging experiments.

They find that the absence of EndoA3 leads to a reduction in T cell-produced cytokine levels. Additionally, they observe slightly reduced levels of ICAM1 at the immunological synapse and an enlarged contact area between T cells and cancer cells. Taken together, the authors propose a mechanism where EndoA3-mediated endocytosis of ICAM1, followed by retrograde transport, supplies the immunological synapse with ICAM1. In the absence of EndoA3, T cells attempt to compensate for suboptimal ICAM1 levels at the synapse by enlarging their contact area, which proves insufficient and leads to lower levels of T cell activation.

Strengths:

The authors utilize a rigorous and innovative experimental approach that convincingly identifies ICAM1 as a novel cargo for Endo3A-mediated endocytosis.

Weaknesses:

The characterization of the effects of Endo3A absence on T cell activation appears incomplete. Key aspects, such as surface marker upregulation, T cell proliferation, integrin signalling and most importantly, the killing of cancer cells, are not comprehensively investigated.

We agree with the reviewer that the effects of EndoA3 depletion on T cell activation were not characterized enough. In new data presented in Fig.S4G-J, we explored additional activation markers and proliferation parameters. We didn’t observe any difference for the surface markers PD-1, CD137 and Tim-3 between LB33-MEL EndoA3+ cells treated with control and EndoA3 siRNAs. Regarding proliferation (Fig. S4J), although the proliferation index seems slightly lower upon EndoA3 depletion, we didn’t observe any significant difference either. Degranulation has also been monitored (Fig. S4K), but we didn’t observe any significant differences. In the new Fig. 3F however, we performed chromium release assays to assess the killing of cancer cells. Very interestingly, we observed an ~15% higher lysis of LB33-MEL EndoA3+ cells after EndoA3 depletion, when compared to the control condition at a ratio of 3:1 T cells:target cells (where the maximal effect is observed). These data are further discussed in the discussion section (new §6-9).

As Endo- and exocytosis are intricately linked with the biophysical properties of the cellular membrane (e.g. membrane tension), which can significantly impact T-cell activation and cytotoxicity, the authors should address this possibility and ideally address it experimentally to some degree.

Evaluating changes in the biophysical properties of cancer cell plasma membrane upon EndoA3 depletion is not trivial. An indirect way to address this question is by observing the area and shape of cells after siRNA treatment. In the new data added in the new Fig. S4B-D, we compared the area, aspect ratio and roundness of LB33-MEL EndoA3+ cells treated with negative control or EndoA3 siRNAs. While we observed a slight cell area reduction upon EndoA3 depletion, no significant changes were observed regarding the aspect ratio and the roundness. Hence, we think that the biophysical properties of cancer cells are not drastically modified by EndoA3 depletion.

Crucially, key literature relevant to this research, addressing the role of ICAM1 endocytosis in antigen-presenting cells, has not been taken into consideration.

We thank the reviewer for this important point. We have now considered and cited the relevant literature (Discussion, Page no.9).

Reviewer #2 (Public review):

Summary:

The manuscript by Xu et al. studies the relevance of endophilin A3-dependent endocytosis and retrograde transport of immune synapse components and in the activation of cytotoxic CD8 T cells. First, the authors show that ICAM1 and ALCAM, known components of immune synapses, are endocytosed via endoA3-dependent endocytosis and retrogradely transported to the Golgi. The authors then show that blocking internalization or retrograde trafficking reduces the activation of CD8 T cells. Moreover, this diminished CD8 T cell activation resulted in the formation of an enlarged immune synapse with reduced ICAM1 recruitment.

Strengths:

The authors show a novel EndoA3-dependent endocytic cargo and provide strong evidence linking EndoA3 endocytosis to the retrograde transport of ALCAM and ICAM1.

Weaknesses:

The role of EndoA3 in the process of T cell activation is shown in a cell that requires exogenous expression of this gene. Moreover, the authors claim that their findings are important for polarized redistribution of cargoes, but failed to show convincingly that the cargoes they are studying are polarized in their experimental system. The statistics of the manuscript also require some refinement.

We fully acknowledge that the requirement for exogenous expression of EndoA3 in our immunological model represents a limitation of our study. Unfortunately, it remains challenging to identify cancer cell lines for which autologous CD8 T cells are available and that endogenously express all molecular players investigated (in particular EndoA3). At this stage, we do not have access to any other cancer cell line/autologous CD8⁺ T cell pairs that are sufficiently well characterized. In future studies, it would be valuable to investigate tumor types with high endogenous EndoA3 expression (such as glioblastomas, gliomas, and head and neck cancers) for which autologous CD8 T cells could be obtained, but this remains technically challenging.

To address the reviewer’s second point regarding polarized redistribution of cargoes, we have added new data in the new Figure 4 and Movies S8-9. Using high-speed spinningdisk live-cell confocal microscopy, we captured the movement of ICAM1-positive tubulovesicular carriers in cancer cells at the moment of contact with CD8 T cells. Capturing such events is technically challenging, as T cell–cancer cell contacts form randomly and transiently. Successful imaging requires that the cancer cell be well spread and express ICAM1–GFP at an optimal level (as it is transiently expressed as a GFP-tagged construct), while acquisition must occur precisely at the moment when the T cell initiates contact. Despite these technical constraints, we successfully imaged early stages of immune synapse formation, enabling visualization of ICAM1 vesicular transport.

The data reveal a flux of ICAM1-positive carriers emerging from the perinuclear region (corresponding to the Golgi area) and moving toward the contact site with the CD8 T cell, with fusion events of vesicles occurring at the developing immune synapse. AI-based segmentation and tracking analyses showed that ICAM1-positive carrier trajectories were predominantly oriented toward the forming immune synapse, whereas carriers moving toward other cellular regions were markedly less frequent. These results provide direct evidence for polarized ICAM1 transport via vesicular trafficking toward the immune synapse.

Reviewer #3 (Public review):

Summary:

Shiqiang Xu and colleagues have examined the importance of ICAM-1 and ALCAM internalization and retrograde transport in cancer cells on the formation of a polarized immunological synapse with cytotoxic CD8+ T cells. They find that internalization is mediated by Endophilin A3 (EndoA3) while retrograde transport to the Golgi apparatus is mediated by the retromer complex. The paper is building on previous findings from corresponding author Henri-François Renard showing that ALCAM is an EndoA3dependent cargo in clathrin-independent endocytosis.

Strengths:

The work is interesting as it describes a novel mechanism by which cancer cells might influence CD8+ T cell activation and immunological synapse formation, and the authors have used a variety of cell biology and immunology methods to study this. However, there are some aspects of the paper that should be addressed more thoroughly to substantiate the conclusions made by the authors.

Weaknesses:

In Figure 2A-B, the authors show micrographs from live TIRF movies of HeLa and LB33MEL cells stably expressing EndoA3-GFP and transiently expressing ICAM-1-mScarlet. The ICAM-1 signal appears diffuse across the plasma membrane while the EndoA3 signal is partially punctate and partially lining the edge of membrane patches. Previous studies of EndoA3-mediated endocytosis have indicated that this can be observed as transient cargo-enriched puncta on the cell surface. In the present study, there is only one example of such an ICAM-1 and EndoA3 positive punctate event. Other examples of overlapping signals between ICAM-1 and EndoA3 are shown, but these either show retracting ICAM1 positive membrane protrusions or large membrane patches encircled by EndoA3. While these might represent different modes of EndoA3-mediated ICAM-1 internalization, any conclusion on this would require further investigation.

We agree with the reviewer that the pattern of cargoes during endocytosis (puncta vs large patches) as observed by live-cell TIRF microscopy may be confusing. Actually, a punctate pattern has been observed quasi systematically when we monitored the uptake of endogenous cargoes via antibody uptake assays (whatever the imaging approach: TIRF, spinning-disk, classical confocal or lattice light-sheet microscopy). For example:

- ALCAM: Fig.1e-h, Supplementary Figure 5 and Supplementary Movies 1-3 and 6 in Renard et al. 2020, https://doi.org/10.1038/s41467-020-15303-y; Fig.1D and Movie 2 in Tyckaert et al. 2022, https://doi.org/10.1242/jcs.259623.

- L1CAM: Fig.2 and 3D, Movies S1-4 in Lemaigre et al. 2023, https://doi.org/10.1111/tra.12883.

In rare examples, bigger clusters of antibodies were observed, where EndoA3 was observed to surround them, delineate them in a “lasso-like” pattern, and the clusters were progressively taken up:

- ALCAM: Supplementary Movie 4 in Renard et al. 2020, https://doi.org/10.1038/s41467-020-15303-y.

However, bigger patches of cargoes were more often observed when uptake was observed using transient expression of GFP-/mCherry-tagged versions of cargoes. In these cases, EndoA3 was predominantly observed to delineate cargo patches as a “lasso-like” pattern, progressively triming those patches leading to endocytosis. For example:

- L1CAM: Fig.3E, Movie S5-7 in Lemaigre et al. 2023, https://doi.org/10.1111/tra.12883.

- We also observed this pattern with CD166-GFP (unpublished).

The fact that we observed rather patches than punctate patterns upon transient expression of fluorescently-tagged constructs of cargoes is likely due to the elevated expression level of the cargoes.

Therefore, the patchy pattern observed for ICAM1 and ALCAM, transiently expressed in fusion with fluorescent proteins, and surrounded by EndoA3 in Fig.2A-B and old Movies S1-3, is not surprising. Of note, upon anti-ALCAM antibody uptake, we observed a more punctate pattern (Fig.2C), as previously described. Unfortunately, the lower quality of commercial anti-ICAM1 antibody did not allow us to proceed to uptake assays as for ALCAM.

Regarding Fig.S2 and old Movies S4-5, we agree with the reviewer that these data may be misleading, as they represent phenomena happening at protrusions and contact zones between two adjacent cells. We have now replaced these images with other examples where we avoid contact zones (Fig.S2 and new Movies S5-7).

These different patterns (patches vs dots) are still unexplained at the current stage, and may indeed represent different modes of endocytosis. We think these various patterns may depend on the abundance/expression level of cargoes and their degree of clustering. This will be investigated in future studies. Still, whatever the pattern, these data demonstrate and confirm the association between EndoA3 and cargoes (such as ICAM1 or ALCAM), even in the absence of antibodies.

Moreover, in Figure 2C-E, uptake of the previously established EndoA3 endocytic cargo ALCAM is analyzed by quantifying total internal fluorescence in LB33-MEL cells of antibody labelled ALCAM following both overexpression and siRNA-mediated knockdown of EndoA3, showing increased and decreased uptake respectively. Why has not the same quantification been done for the proposed novel EndoA3 endocytic cargo ICAM-1? Furthermore, if endocytosis of ICAM-1 and ALCAM is diminished following EndoA3 knockdown, the expression level on the cell surface would presumably increase accordingly. This has been shown for ALCAM previously and should also be quantified for ICAM-1.

As correctly pointed by the reviewer, anti-ICAM1 antibody uptake assays would have been great. We have tried to do them many times. Unfortunately, all commercial antibodies we tested did not yield satisfying results in uptake experiments. Either the labeling was too week/non-specific, or the antibody was not effectively stripped from the cell surface by acid washes, i.e. the acid-wash conditions required for efficient stripping were too harsh for the cells to tolerate. We have tried other approaches using the same commercial antibody which do not require acid washes (loss of surface assays by FACS, or uptake assays using surface protein biotinylation) or based on insertion of an Alfa-tag in the extracellular part of ICAM1 by CRISPR-Cas9 and detection of ICAM1 with an antiAlfa-tag nanobody (unpublished approach; collaboration with the lab of Prof. Leonardo Almeida-Souza, University of Helsinki, who developed the approach), but without success. However, we were more successful with the SNAP-tag-based approach to follow retrograde transport, for which the commercial anti-ICAM1 antibody worked properly. In Fig. 1F, we could show that retrograde transport of ICAM1 (and thus most likely its endocytosis step) was significantly decreased upon EndoA3 depletion in HeLa cells, indirectly demonstrating that ICAM1 is effectively an EndoA3-dependent cargo.

Regarding the fact that surface level of ICAM1 should increase upon perturbation of EndoA3-mediated endocytosis, we agree with the reviewer that this could be an expected result. However, this is not necessarily systematic, as the surface level of a protein cargo is always the result of a balance between its endocytosis, recycling to plasma membrane, and lysosomal degradation. We also have to take into account the neosynthesized protein flux. One must also consider that multiple endocytic mechanisms exist in parallel, and that the perturbation of one mechanism (EndoA3-mediated CIE, here) may be partially compensated by others, as cargoes can often be taken up via multiple endocytic doors. Hence, an increased abundance at the cell surface is not always guaranteed upon endocytosis perturbation. Anyway, we measured the cell surface level of both ICAM1 and ALCAM in LB33-MEL EndoA3+ cells treated with negative control or EndoA3 siRNAs (Fig. S4E-F). Only minor differences were observed.

In Figure 4A the authors show micrographs from a live-cell Airyscan movie (Movie S6) of a CD8+ T cell incubated with HeLa cells stably expressing HLA-A*68012 and transiently expressing ICAM1-EGFP. From the movie, it seems that some ICAM-1 positive vesicles in one of the HeLa cells are moving towards the T cell. However, it does not appear like the T cell has formed a stable immunological synapse but rather perhaps a motile kinapse. Furthermore, to conclude that the ICAM-1 positive vesicles are transported toward the T cell in a polarized manner, vesicles from multiple cells should be tracked and their overall directionality should be analyzed. It would also strengthen the paper if the authors could show additional evidence for polarization of the cancer cells in response to T-cell interaction.

A similar point was raised by reviewer #2. We have revised this section accordingly. In the new Fig. 4 and Movies S8-9, we replaced the live-cell Airyscan confocal data with highspeed spinning-disk confocal imaging data, enabling a more accurate analysis of cargo polarized redistribution and at a higher time resolution.

Using this approach, we captured the movement of ICAM1-positive tubulo-vesicular carriers in cancer cells at the moment of contact with CD8 T cells. Capturing such events is technically challenging, as T cell–cancer cell contacts form randomly and transiently. Successful imaging requires that the cancer cell be well spread and express ICAM1–GFP at an optimal level (as it is transiently expressed as a GFP-tagged construct), while acquisition must occur precisely at the moment when the T cell initiates contact. Despite these technical constraints, we successfully imaged early stages of immune synapse formation, enabling visualization of ICAM1 vesicular transport.

The data reveal a flux of ICAM1-positive carriers emerging from the perinuclear region (corresponding to the Golgi area) and moving toward the contact site with the CD8 T cell, with fusion events of carriers occurring at the developing immune synapse.

AI-based segmentation and tracking analyses showed that ICAM1-positive carrier trajectories were predominantly oriented toward the forming immune synapse, whereas carriers moving toward other cellular regions were markedly less frequent. These results provide direct evidence for polarized ICAM1 transport via vesicular trafficking toward the immune synapse.

Finally, in Figures 4D-G, the authors show that the contact area between CD8+ T cells and LB33-MEL cells is increased in response to siRNA-mediated knockdown of EndoA3 and VPS26A. While this could be caused by reduced polarized delivery of ICAM-1 and ALCAM to the interface between the cells, it could also be caused by other factors such as increased cell surface expression of these proteins due to diminished endocytosis, and/or morphological changes in the cancer cells resulting from disrupted membrane traffic. More experimental evidence is needed to support the working model in Figure 4H.

Regarding the cell surface expression of both ICAM1 and ALCAM, as already explained above, only minor differences were observed (Fig. S4E-F). Regarding morphological changes of cancer cells upon EndoA3 depletion (Fig. S4B-D), we compared the area, aspect ratio and roundness of LB33-MEL EndoA3+ cells treated with negative control or EndoA3 siRNAs. While we observed a slight cell area reduction upon EndoA3 depletion, no significant changes were observed regarding the aspect ratio and the roundness. Cancer cell morphology is thus not drastically modified by EndoA3 depletion. All these new data are now discussed in the manuscript.

Recommendations for the authors:

Reviewing Editor Comments:

The reviewers discussed the paper and all agreed it was incomplete in supporting the conclusions. Additional data needed to support the conclusions were:

(1) Better characterisation of Endo3A-expressing and knock-down cells such as morphology, ICAM-1, and ALCAM surface levels to name two parameters.

As discussed above, we have now added new data addressing these points:

- Morphology: Fig. S4B-D

- ICAM1 and ALCAM surface levels: Fig. S4E-F These new data are discussed in the main text.

(2) Better characterisation of the ICAM-1 polarisation process. Does this require interaction with LFA-1 can ICAM-1 be delivered to the synapse without this?

As discussed above, we have now added new data better addressing the characterization of ICAM1 polarized trafficking to the immune synapse, that can be found in the new Fig. 4 (high-speed spinning-disk confocal imaging of ICAM1 trafficking upon conjugate formation between CD8 T cell and cancer cell). The text has been modified accordingly. The dependency on LFA-1 has not been addressed directly, but we may suppose it is indeed important as (i) it has already been addressed in other cellular systems by previous studies (Jo et al. 2010), and (ii) we observed a denser flux of ICAM1-positive carriers in the cancer cell toward regions involved in immune synapses with CD8 T cells, than other regions. As we didn’t address this question more directly in our study, we briefly mentioned this point in the Discussion section.

(3) Better characterisation of T cell response- activation markers, cytotoxicity assays.

As discussed above, we have now added new data addressing these points:

- Cell surface activation markers: Fig. S4G-I

- Proliferation: Fig. S4J

- Degranulation: Fig. S4K

- Cytotoxic activity: Fig. 3F

These new data are discussed in the main text.

(4) Citing relevant literature.

The relevant literature (in particular the paper by Jo et al. 2010) is now cited and discussed.

(5) Number of donors evaluated - is it true there was only one blood donor? For human studies better to have key results on >4 donors.

Our immunological working model indeed originates from a single patient (Baurain et al., 2000), from whom both a cancer cell line (LB33-MEL) and autologous CD8 T cells were derived. These CD8 T cells specifically recognize an HLA molecule presenting a defined antigenic peptide (MUM-3) on the surface of the cancer cells. This provides us with a unique and fully natural experimental system that allows us to faithfully reconstitute cytotoxic T lymphocyte (CTL)-mediated killing of cancer cells in vitro.

Using CD8 T cells from other donors would not be meaningful in this context, as they would not recognize the LB33-MEL cells. Conversely, testing the same CD8 T cells on other cancer cell lines requires engineering these lines to express the appropriate HLA molecule and to be exogenously pulsed with the correct antigenic peptide – which is precisely what we did with the HeLa cell line.

Therefore, increasing the number of donors would require obtaining both cancer cell lines and CD8 T cells from each donor, ideally with evidence that the donor’s T cells recognize their own tumor cells. This is technically challenging and not trivial, although it would indeed be highly valuable to diversify immunological models in future studies.

Importantly, the high specificity of our autologous co-culture system, where cancer cells interact with their naturally matched CD8 T cells, offers clear advantages over commonly used in vitro models such as Jurkat (T) and Raji (B) cell lines, which rely on artificial stimulation with a superantigen to enforce immunological synapse formation and T cell activation.

(6) How does the binding of antibodies to ICAM-1 and ALCAM impact their trafficking?

As IgG antibodies are bivalent and can bind two target antigens, they may induce clustering, which could in turn affect endocytosis. To address this concern, we performed an uptake assay based on surface protein biotinylation using a cleavable biotin reagent (with a reducible linker). Briefly, after allowing endocytosis for different time intervals, cell surface–exposed biotins were removed by treatment with the cellimpermeable reducing agent MESNA, while internalized (endocytosed) biotinylated proteins remained protected. These internalized proteins were then recovered by affinity purification on streptavidin resin and analyzed by Western blot to detect the protein of interest.

Importantly, this uptake assay can be performed in the absence or presence of an anticargo antibody, allowing assessment of its potential influence on endocytosis. Author response image 1 shows the results for ALCAM uptake in HeLa cells, with and without anti-ALCAM antibody:

Author response image 1.

Antibody binding to an extracellular epitope of ALCAM increases its endocytosis. HeLa cellsurface proteins were biotinylated on ice using EZ-Link Sulfo-NHS-SS-Biotin (Pierce) and then incubated at 37 °C for the indicated times to allow endocytosis. Internalization was assessed in the absence or presence of an anti-ALCAM antibody (Ab) added to the extracellular medium. Endocytosis was stopped by returning the cells to ice, and surface-exposed biotin was removed by treatment with the cell-impermeable reducing agent MESNA. Internalized, MESNA-resistant biotinylated proteins were affinity-purified on streptavidin resin and analyzed by Western blot to detect ALCAM. The “unstripped” condition shows the total amount of ALCAM at the cell surface at the beginning of the experiment (signal at ~95 kDa). Quantification of the time course (normalized to the no-antibody condition) shows increased ALCAM endocytosis in the presence of antibody at 15 and 30 min. Blot is representative of two independent experiments; quantifications include data from both experiments.

We observed that the anti-ALCAM antibody slightly enhanced ALCAM uptake. A similar experiment was attempted for ICAM1, but we were unable to detect the protein by Western blot using the available commercial antibody.

Although this outcome was expected, it highlights a potential caveat in using antibodies to monitor endocytosis. Alternative tools such as nanobodies, while monovalent and theoretically less perturbing, are not yet available for many cargo proteins and may still influence cargo conformation or dynamics. Therefore, antibodies remain the current gold standard in endocytosis studies. Nevertheless, data obtained with antibodies should always be validated by complementary approaches that do not rely on antibody binding, as we have done in this study (e.g. live-cell imaging of fluorescently tagged proteins).

The work is of interest and we look forward to your response/revision.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Thank you for submitting your manuscript which I had the pleasure to review. While I enjoyed your work, I feel that it would strongly benefit by addressing the following points:

(1) In-depth characterization of T cell responses upon Endo3A depletion: The characterization should be expanded to include surface marker upregulation, T cell proliferation, and, most importantly, tumor cell cytotoxicity. I was wondering if the incomplete characterization of T-cell responses is due to limited supplies of antigenspecific T-cells? My understanding is that these cells have been derived from a single patient. This also raises concerns in terms of reproducibility as all data are practically from a single biological replicate. My suggestion would be to use an additional system of specific cell-cell contacts to complement the current findings. For instance, HeLa cells could be transfected to express CD19 or EpCAM, for both of which bispecific T cell engagers (Invivogen) exist that would allow specific contact formation, thereby allowing the study of the effect of Endo3A depletion across T cells from different donors and through a more complete set of assays.

We refer the reviewer to our responses above, where these points have been addressed in detail. We sincerely thank the reviewer for the excellent suggestion of transfecting HeLa cells with CD19 or EpCAM and using bispecific T-cell engagers. However, after careful consideration, we concluded that this approach falls outside the scope of the present study, which was specifically designed to investigate the most natural system, cancer cells and their autologous CD8 T cells. We nevertheless appreciate this insightful suggestion and will certainly consider it for future studies.

(2) Alterations in membrane tension as an alternative explanation: Endo- and exocytosis have been found to influence the biophysical properties of cells, such as membrane tension (e.g., Djakbaravo et al., 2021, PMID: 33788963), which in turn influences their susceptibility to cytotoxic T cells with lower tension corresponding to reduced cytotoxicity (e.g., Basu & Whitlock, 2016, PMID: 26924577). Thus, interference with endocytic pathways could arguably lead to changes in membrane tension that could contribute to the observed effects. These possible effects should be discussed and addressed experimentally to a degree. While measuring membrane tension directly requires specialized expertise (e.g., tether pulling experiments) and is not within the scope of this study, membrane tension affects cell spreading and actin organization. Thus, I would suggest conducting a thorough comparative phenotypical and morphological characterization of the Endo3A+ and Endo3A- cancer cells to estimate the possible effect of changes in membrane tension (if any) on the results.

We refer the reviewer to our responses above, where these points have been addressed in detail. New data have been added and the text of our manuscript has been modified accordingly.

(3) Citation and consideration of earlier work: Jo & Kwon et al., 2010 (PMID: 20681010) have previously shown that ICAM1 undergoes clathrin-independent recycling and repolarization to the immunological synapse in APCs. Furthermore, they provided evidence that actin-based transport, but not lateral diffusion, together with recycling is crucial for the repolarization of ICAM1 to the immunological synapse. This important earlier work has to be cited. Actin-based transport on the cell surface has not been considered in the current manuscript. In light of these earlier findings, it is unclear in Figure 4A if ICAM1 is delivered to the T cell from within- or from the surface of the cancer cell. I would suggest changing the imaging modalities in this experiment to be able to differentiate cell surface from internal ICAM1, e.g., by detaching the cancer cells from the surface as has been done in Fig. 4B, E, and F.

We refer the reviewer to our responses above, where these points have been addressed in detail. New data have been added and the text of our manuscript has been modified accordingly.

Reviewer #2 (Recommendations for the authors):

Major comments:

(1) The authors should be more careful with their claims about the importance of their results for cell polarity as their evidence for this is scarce (i.e. The live-cell imaging in Figure 4A is not quantified and the ICAM1 polarization effect shown in figure 4B-C is, albeit significant, small and not very convincing).

We refer the reviewer to our responses above, where these points have been addressed in detail. New data have been added and the text of our manuscript has been modified accordingly.

(2) The absence (or very low expression) of EndoA3 on the LB33-MEL cell suggests that EndoA3-mediated recycling of immune synaptic components is not required for T-cell activation. The fact that EndoA3 exogenous expression in LB33-MEL cells leads to increased cytokine production in T cells is, however, interesting.

We fully agree with the reviewer’s observation. Although EndoA3 is not expressed in some cellular contexts, its cargoes may still be present. It is therefore reasonable to assume that alternative endocytic mechanisms can compensate for its absence. It is now widely accepted that many cargoes can be internalized through multiple endocytic routes, and that the relative contribution of each pathway depends strongly on the cellular and physiological context.

For example, we have shown that ALCAM and L1CAM, although primarily internalized via clathrin-independent pathways, present a minor fraction (< 25%) undergoing clathrinmediated endocytosis (Renard et al., 2020; Lemaigre et al., 2023). Moreover, we observed that inhibition of macropinocytosis enhances EndoA3-mediated endocytosis of ALCAM, indicating a crosstalk between specific EndoA3-mediated clathrin-independent endocytosis (CIE) and non-specific macropinocytosis (Tyckaert et al., 2022).

Thus, even in the absence of EndoA3, its cargoes are likely internalized through alternative endocytic routes. Nonetheless, our data clearly demonstrate that EndoA3 expression markedly enhances the endocytosis and intracellular trafficking of its cargoes, ultimately leading to modified CD8 T cell responses.

(3) For the statistics in bar graphs (graphs 1C, D, E &F; 3E, 3F, S1C-I, and S3C), one cannot have all values for controls simply normalized to 1. This procedure hides the variance for the controls between each replicate and makes any statistics meaningless.

We thank the reviewer for this important remark. Regarding Figures 1C–F, S1C–I, and S3C, which correspond to quantifications from Western blots, it is standard practice to normalize the quantification to a control condition set to 1 (or 100%). Absolute signal intensities cannot be directly compared across different blots due to the variability inherent to this semi-quantitative technique. For this reason, we chose to keep the data presented in normalized form. However, we agree that this type of data require the careful choice of a convenient statistical analysis approach. Here, we choose one-sample T tests, allowing to test the hypothesis that the various siRNA conditions are different from 100% (the normalized value of the siCtrl condition). We adapted the statistical analysis accordingly in the different figures mentioned.

Regarding old Figures 3E–F (now Fig. 3E and 3G), which correspond to IFNγ secretion assays, we agree that representing IFNγ secretion as a fold change relative to a control condition may obscure inter-experimental variability. However, this format was intentionally chosen to facilitate data interpretation, as IFNγ secretion was quantified by ELISA and also displayed inter-experimental variability. For completeness, we now provide below the corresponding graphs showing absolute IFNγ concentrations, which retain the information on inter-experimental variability (Author response image 2). As you can see, the overall conclusions remain unchanged.

Author response image 2.

IFNg secretion data corresponding to Fig. 3E and 3G, expressed in absolute values (pg/mL)

Minor comments:

(1) What happens to surface and total levels of ICAM1 and ALCAM in the retromer or EndoA3 knockdown/overexpression conditions? This information would put the effects described into context.

We refer the reviewer to our responses above, where these points have been addressed in detail. New data have been added and the text of our manuscript has been modified accordingly.

(2) The authors should clearly indicate that BFA means bafilomycin A in the figure legend or methods.

BFA corresponds to Brefeldin A. We have now clarified this information in legends and methods.

(3) In the sentence: "These data demonstrate that retromer-mediated retrograde transport is critical for trafficking ALCAM and ICAM1 to the Golgi and that this process requires the full secretory capacity of the TGN." What do the authors mean by full secretory capacity?

We have modified the sentence: “Together, these data demonstrate that retromermediated retrograde transport is critical for trafficking ALCAM and ICAM1 to the Golgi and that this process requires efficient secretion from the TGN (as evidenced by the involvement of Rab6).”

(4) The method used for retrograde transport seems to be a variation of the original protocol (reference 43). The manuscript would benefit from a thorough explanation of this assay, rather than citing the original protocol.

We did not modify the original SNAP-tag–based protocol used to monitor retrograde transport. A comprehensive methodological paper has been published (ref. 44), and we have followed it strictly. Additionally, we briefly summarized the rationale of the approach in Figure 1A and in the first paragraph of the Results section.

Reviewer #2 (Public review):

Summary:

During vertebrate gastrulation, the mesoderm and endoderm arise from a common population of precursor cells and are specified by similar signaling events, raising questions as to how these two germ layers are distinguished. Here, Cheng and colleagues use zebrafish gastrulation as a model for mesoderm and endoderm segregation. By reanalyzing published single cell sequencing data, they identify a common progenitor population for anterior endoderm and the mesodermal prechordal plate (PP). They find that expression levels of PP genes gsc and ripply are among the earliest differences between these populations, and that their increased expression suppresses the expression of endoderm markers. Further analysis of chromatin accessibility and Ripply CUT-and-TAG is consistent with direct repression of endoderm by this PP marker. This study demonstrates roles for Gsc and Ripply in suppressing anterior endoderm fate, but this role for Gsc was already known and the effect of Ripply is limited to a small population of anterior endoderm.

Strengths:

Integrated single cell ATAC- and RNA-seq convincingly demonstrate changes in chromatin accessibility that may underlie segregation of mesoderm and endoderm lineages, including gsc and ripply. Identification of Ripply-occupied genomic regions augments this analysis. The genetic mutants for both genes provide strong evidence for their function anterior mesendoderm development, although these phenotypes are subtle.

Weaknesses:

The use of zebrafish embryonic explants for cell fate trajectory analysis (rather than intact embryos) is not justified. Much of the work is focused on the role of Nodal in the mesoderm/endoderm fate decision, but the results largely confirm previous studies and again provide few new insights. The authors similarly confirm previous findings that FGF signaling likely plays a larger role in this fate decision, but these results are largely overlooked by the authors.

Reviewer #3 (Public review):

Summary of work:

Cheng, Liu, Dong, et al. demonstrate that anterior endoderm cells can arise from prechordal plate progenitors, which is suggested by pseudotime reanalysis of published scRNAseq data, pseudotime analysis of new scRNAseq data generated from Nodal-stimulated explants, live imaging from sox17:DsRed and gsc:eGFP transgenics, fluorescent in situ hybridization, and a Cre/Lox system. Early fate mapping studies already suggested that progenitors at the dorsal margin give rise to both of these cell types (Warga), and live imaging from the Heisenberg lab (Sako 2016, Barone 2017) convincingly showed this previously. However, the data presented for this point are very nice and further cement this result. Though better demonstrated by previous work (Alexander 1999, Gritsman 1999, Gritsman 2000, Sako 2016, Rogers 2017, others), the manuscript presents confirmatory data that high Nodal signaling is required for both cell types. The manuscript generates new single-cell RNAseq data from Nodal-stimulated explants with increased (lft1 KO) or decreased (ndr1 KD) Nodal signaling and multi-omic ATAC+scRNAseq data from wild-type 6 hpf embryos, which can be used as a resource, though few new conclusions are drawn from it in this manuscript. Lastly, the manuscript presents suggests that SWI/SNF remodelers and Ripply1 may be involved in the anterior endoderm - prechordal plate decision, but these data are less convincing. The SWI/SNF remodeler experiments are unconvincing because the demonstration that these factors are differentially expressed or active between the two cell types are weak. The Ripply1 gain-of function experiments are unconvincing because they are based on incredibly high overexpression of ripply1 (500 pg or 1000 pg) that generates a phenotype that is not in line with previously demonstrated overexpression studies (with phenotypes from 10-20x lower expression). Similarly, the cut-and-tag data seems low quality and is based on high overexpression, so may not support direct binding of ripply1 to these loci.

During revision, the authors addressed some comments, including eliminating references to "lineage" when referring to pseudotime trajectories, eliminating conclusions drawn from locations of cells on UMAP plots, and reducing use of the term "cooperative" which may have been confusing in this context, as well as increasing the number of embryos analyzed for some experiments. The authors also point out that whole-embryo transcriptional trajectories typically do not associate endodermal cells with prechordal plate cells, despite classical evidence that they are related. This is most likely because endodermal cells arise from several different previous transcriptional states in different regions of the embryonic margin and are, as the authors point out, difficult to computationally sort into dorsal, lateral, and ventral populations. Thus, there is value in generating data to more specifically look at the relationship between dorsal mesodermal and endodermal populations. However, the decision to use an artificial Nodal-treated explant system, rather than isolating the relevant population from whole embryos (such as by dissection prior to dissociation) remains a weakness of the manuscript, since it is unclear whether endodermal specification has been altered in this system (there seem to be few endodermal cells produced and the system involves manipulating one of the signals under study in this work). Concerns about the rigor of experiments concerning ripply1 and SWI/SNF experiments remains. While the authors improved peak calling in their ripply1 cut-and-tag, it is still based on massive overexpression of ripply1 that may drive binding outside of its endogenous loci.

In the end, this study provides some additional details in the cell fate decision between the prechordal plate and anterior endoderm and generates new data that may be useful for reanalysis by other experts in the field. However, this work does not make clear how Nodal signaling, FGF signaling, and elements of the gene regulatory network (including gsc, possibly ripply1, and other factors) interact to make the decision. I suggest that this manuscript is of interest to Nodal signaling or zebrafish germ layer patterning afficionados, but may not be of interest to a broad audience. While it provides new datasets and observations, it does not weave these into a convincing story that advances our understanding of the specification of these cell types.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This study provides a useful analysis of the changes in chromatin organization and gene expression that occur during the differentiation of two cell types (anterior endoderm and prechordal plate) from a common progenitor in zebrafish. Although the findings are consistent with previous work, the evidence presented in the study appears to be incomplete and would benefit from more rigorous interpretation of single-cell data, more in-depth lineage tracing, overexpression experiments with physiological levels of Ripply, and a clearer justification for using an explant system. With these modifications, this paper will be of interest to zebrafish developmental biologists investigating mechanisms underlying differentiation.

We sincerely thank the editor and the reviewers for their valuable time and efforts. Their insightful comments were greatly appreciated and have been largely addressed in the revised manuscript. We are confident that these revisions have enhanced the overall quality and clarity of our paper.

Reviewer #1 (Public review):

Summary:

During vertebrate gastrulation, mesendoderm cells are initially specified by morphogens (e.g. Nodal) and segregate into endoderm and mesoderm in part based on Nodal concentrations. Using zebrafish genetics, live imaging, and single-cell multi-omics, the manuscript by Cheng et al presents evidence to support a claim that anterior endoderm progenitors derive primarily from prechordal plate progenitors, with transcriptional regulators goosecoid (Gsc) and ripply1 playing key roles in this cell fate determination. Such a finding would represent a significant advance in our understanding of how anterior endoderm is specified in vertebrate embryos.

We would like to thank reviewer #1 for his/her comments and positive feedbacks about our manuscript.

Strengths:

Live imaging-based tracking of PP and endo reporters (Figure 2) is well executed and convincing, though a larger number of individual cell tracks will be needed. Currently, only a single cell track (n=1) is provided.

We thank the reviewer for the positive comments and the valuable suggestion. As the reviewer suggested, we re-performed live imaging analyses on the embryos of Tg(gsc:EGFP;sox17:DsRed). We tracked dozens of cells during their transformation from gsc-positive to sox17-positive. Furthermore, we performed quantification of the RFP/GFP signal intensity ratio in these cells over the course of development (Please see the revised Figure 2D and MovieS4).

Weaknesses:

(1) The central claim of the paper - that the anterior endoderm progenitors arise directly from prechordal plate progenitors - is not adequately supported by the evidence presented. This is a claim about cell lineage, which the authors are attempting to support with data from single-cell profiling and genetic manipulations in embryos and explants. The construction of gene expression (pseudo-time) trajectories, while a modern and powerful approach for hypothesis generation, should not be used as a substitute for bona fide lineage tracing methods. If the authors' central hypothesis is correct, a CRE-based lineage tracing experiment (e.g. driving CRE using a PP marker such as Gsc) should be able to label PP progenitor cells that ultimately contribute to anterior endoderm-derived tissues. Such an experiment would also allow the authors to quantify the relative contribution of PP (vs non-PP) cells to the anterior endoderm, which is not possible to estimate from the indirect data currently provided. Note: while the present version of the manuscript does describe a sox17:CRE lineage tracing experiment, this actually goes in the opposite direction that would be informative (sox:17:CRE-marked descendants will be a mixture of PP-derived and non-PP derived cells, and the Gsc-based reporter does not allow for long-term tracking the fates of these cells).

We sincerely thank the reviewer for the professional comments and the constructive suggestions. As the reviewer indicated, utilizing the single-cell transcriptomic trajectory analyses on zebrafish embryos and Nodal-injected explants system, along with the live imaging analyses on Tg(gsc:EGFP;sox17:DsRed) embryos, we revealed that anterior endoderm progenitors arise from prechordal plate progenitors. To further verify this observation, we conducted two sets of lineage-tracing assays. Initial evidence came from the results of co-injecting sox17:Cre and gsc:loxp-STOP-loxp-mcherry plasmids. We observed RFP-positive cells at 8 hpf, demonstrating the presence of cells that had expressed both genes. To explicitly follow the proposed lineage, we then implemented a reciprocal strategy, as suggested by the reviewer, that constructed and co-injected sox17:loxp-STOP-loxp-mcherry and gsc:Cre plasmids. The appearance of RFP-positive cells in the anterior dorsal region at 8 hpf provides direct evidence for a transition from gsc-positive to sox17-positive identity. These results are now included in the revised manuscript (Please see Author response image 1 and Figure S4E). However, in accordance with the reviewer's caution, we acknowledge that this does not prove this is the sole origin of anterior endoderm. Consequently, we have revised the text to clarify that our findings demonstrate that anterior endoderm can be specified from prechordal plate progenitors, without claiming that it is the only source.

Author response image 1.

Characterization of anterior endoderm lineage by Cre-Lox recombination system.

(2) The authors' descriptions of gene expression patterns in the single-cell trajectory analyses do not always match the data. For example, it is stated that goosecoid expression marks progenitor cells that exist prior to a PP vs endo fate bifurcation (e.g. lines 124-130). Yet, in Figure 1C it appears that in fact goosecoid expression largely does not precede (but actually follows) the split and is predominantly expressed in cells that have already been specified into the PP branch. Likewise, most of the cells in the endo branch (or prior) appear to never express Gsc. While these trends do indeed appear to be more muddled in the explant data (Figure 1H), it still seems quite far-fetched to claim that Gsc expression is a hallmark of endoderm-PP progenitors.

We thank the reviewer for pointing out this issue. Our initial analysis proposed that the precursors of the prechordal plate (PP) and anterior endoderm (endo) more closely resemble a PP cell fate, as their progenitor populations highly express PP marker genes, such as gsc. The gsc gene is widely recognized as a PP marker[1]. The reviewer pointed out that in our analysis, these precursor cells do not initially exhibit high gsc expression; rather, gsc expression gradually increases as PP fate is specified.

The reason for this observation is as follows: First, for the in vivo data, we used the URD algorithm to trace back all possible progenitor cells for both the PP and anterior endo trajectory. As mentioned in the manuscript, the PP and anterior endo are relatively distant in the trajectory tree of the zebrafish embryonic data. Consequently, this approach likely included other, confounding progenitor cells that do not express gsc (like ventral epiblast, Author response image 2). However, we further investigated the expression of gsc and sox17 along these two trajectories. The conclusion remains that gsc expression is indeed higher than sox17 in the progenitor cells common to both trajectories (Author response image 2). Combined with the live imaging analysis presented in this study, which shows that gsc expression increases progressively in the PP, this supports the notion that the progenitor cells for both PP and anterior endoderm initially bias towards a PP cell fate.

On the other hand, in our previously published work using the Nodal-injected explant system, which specifically induces anterior endo and PP, the cellular trajectory analysis also revealed that the specifications of PP and anterior endo follow very similar paths. Therefore, we proceeded to analyze the Nodal explant data. Similarly, when using URD to trace the differentiation trajectories of PP and anterior endo cells, a small number of other progenitor cells were also captured. This explains why a minority of cells do not express gsc—these are likely ventral epiblast cells (Author response image 2). However, based on the Nodal explant data, gsc is specifically highly expressed in the progenitor cells of the PP and anterior endo. Its expression remains high in the PP trajectory but gradually decreases in the endoderm trajectory (Figure 1H).

Author response image 2.

(A) The expression of ventral epiblast markers in PP and anterior Endo URD trajectory. (B) The expression of gsc, sox32 and sox17 in the progenitors of PP and anterior endo in embryos and Nodal explants.

(3) The study seems to refer to "endoderm" and "anterior endoderm" somewhat interchangeably, and this is potentially problematic. Most single-cell-based analyses appearing in the study rely on global endoderm markers (sox17, sox32) which are expressed in endodermal precursors along the entire ventrolateral margin. Some of these cells are adjacent to the prechordal plate on the dorsal side of the gastrula, but many (most in fact) are quite some distance away. The microscopy-based evidence presented in Figure 2 and elsewhere, however, focuses on a small number of sox17-expressing cells that are directly adjacent to, or intermingled with, the prechordal plate. It, therefore, seems problematic for the authors to generalize potential overlaps with the PP lineage to the entire endoderm, which includes cells in ventral locations. It would be helpful if the authors could search for additional markers that might stratify and/or mark the anterior endoderm and perform their trajectory analysis specifically on these cells.

We thank the reviewer for these comments and suggestions. We fully agree with the reviewer's point that the expression of sox32 and sox17 cannot be used to distinguish dorsal endoderm from ventral-lateral endoderm cells. However, during the gastrulation stage, all endodermal cells express sox32 and sox17, and there are currently no specific marker genes available to distinguish between them.

After gastrulation ends, the dorsal endoderm (i.e., the anterior endoderm) begins to express pharyngeal endoderm marker genes, such as pax1b. Therefore, in the analysis of embryonic data in vivo, when studying the segregation of the anterior endoderm and PP trajectory, we specifically used the pharyngeal endoderm as the subject to trace its developmental trajectory.

In the case of Nodal explants, Nodal specifically induces the fate of the dorsal mesendoderm, which includes both the PP and pharyngeal endoderm (anterior endoderm). Precisely for this reason, we consider the Nodal explant system as a highly suitable model for investigating the mechanisms underlying the cell fate separation between anterior endoderm and PP. Thus, in the Nodal explant data, we included all endodermal cells for downstream analysis.

To avoid any potential confusion for readers, we have revised the term "endoderm" in the manuscript to "anterior endoderm" as suggested by the reviewer.

(4) It is not clear that the use of the nodal explant system is allowing for rigorous assessment of endoderm specification. Why are the numbers of endoderm cells so vanishingly few in the nodal explant experiments (Figure 1H, 3H), especially when compared to the embryo itself (e.g. Figures 1C-D)? It seems difficult to perform a rigorous analysis of endoderm specification using this particular model which seems inherently more biased towards PP vs. endoderm than the embryo itself. Why not simply perform nodal pathway manipulations in embryos?

We sincerely thank the reviewer for raising this important question. In our study of the fate separation between the PP and anterior endoderm, we initially analyzed zebrafish embryonic data. However, when reconstructing the transcriptional lineage tree using URD, we observed that these two cell trajectories were positioned relatively far apart on the tree. Yet, existing studies have shown that the anterior endoderm and PP are not only spatially adjacent but also both originate from mesendodermal progenitor cells[2-4], and they share transcriptional similarities[5]. Therefore, as the reviewer pointed out, when tracing all progenitor cells of these two trajectories using the URD algorithm, it is easy to include other cell types, such as ventral epiblast cells (Author response image 2). For this reason, we concluded that directly using embryonic data to dissect the mechanism of fate separation between PP and anterior endoderm might not yield highly accurate results.

In contrast, our group’s previous work, published in Cell Reports, demonstrated that the Nodal-induced explant system specifically enriches dorsal mesendodermal cells, including anterior endoderm, PP, and notochord[5]. Thus, we considered the Nodal explant system to be a highly suitable model for investigating the mechanism of fate separation between PP and anterior endoderm. Ultimately, by analyzing both in vivo embryonic data and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitor cells—a conclusion further validated by live imaging experiments.

Regarding the reviewer’s concern about the relatively low number of endodermal cells in the Nodal explant system, we speculate that this is because the explants predominantly induce anterior endoderm. Since endodermal cells constitute only a small proportion of cells during gastrulation, and anterior endoderm represents an even smaller subset, the absolute number is naturally limited. Nevertheless, the anterior endodermal cells captured in our Nodal explants were sufficient to support our analysis of the fate separation mechanism between anterior endoderm and PP. Finally, to further strengthen the findings from scRNA-seq analyses, we subsequently performed live imaging validation experiments using both zebrafish embryos and the explant system.

(5) The authors should not claim that proximity in UMAP space is an indication of transcriptional similarity (lines 207-208), especially for well-separated clusters. This is a serious misrepresentation of the proper usage of the UMAP algorithm. The authors make a similar claim later on (lines 272-274).

We would like to extend our gratitude to the reviewer for their insightful comments. We have revised the descriptions regarding UMAP throughout the manuscript as suggested (Please see the main text in revised manuscript).

Reviewer # 1 (Recommendations For The Authors):

- Pseudotime trajectories constructed from single-cell snapshots are not true "lineage" measurements. Authors should refrain from referring to such data as lineage data (e.g. lines 99, 100, 103, 109, 112, 127, etc). Such models should be referred to as "trajectories", "hypothetical lineages", or something else.

We are grateful to the reviewer for this comment. Following their recommendation, we have revised the terminology from "transcriptional lineage tree" to "trajectory" across the entire manuscript (Please see main text in revised manuscript).

- The live imaging data presented in Figure 2 (and supplemental figures) are compelling and do seem to show that some cells can switch between PP and endo states. However, the number of cells reported is still too low to be able to ascertain whether or not this is just a rare/edge-case phenomenon. Tracks for just a single cell are reported in Figure 2C-D. This is insufficient. Tracks for many more cells should be collected and reported alongside this current sole (n=1) example. The choice of time window for these live imaging experiments should also be better explained. These live imaging experiments are being performed at or after 6hpf, but authors claim in the text that "... the segregation between PP and Endo has already occurred by 6hpf." (lines 126-127). Why not perform these live imaging experiments earlier, when the initial fate decision between PP and endo is supposedly occurring?

We sincerely appreciate the reviewer’s insightful questions and constructive feedback. In response, we have made several important revisions. First, the reviewer noted that our original manuscript tracked only a single cell and suggested increasing the number of tracked cells. Following this recommendation, we repeated the live-imaging experiments and expanded the number of tracked endodermal cells (Please see the revised Movie S4 and Figure 2D). The experimental conditions were kept identical to the previous setup, and these cells consistently exhibited a gradual transition from a gsc+ fate to a sox17+ endodermal fate. In addition, the reviewer recommended performing live imaging at an earlier time point (Movie S5). Accordingly, we conducted additional experiments initiating live imaging at around 5.7 hours and observed the onset of a sox17 expression in gsc+ cells at approximately 6 hpf, which is consistent with our single-cell transcriptomic analysis.

- The sections devoted to lengthy descriptions of GO terms (lines 131-146, 239-254) and receptor-ligand predictions (lines 170-185) are largely speculative. Consider streamlining.

Thanks for the reviewer's comment. We have streamlined the content related to the GO analysis as suggested (Please see Lines 128-132, 157-167, 221-225).

- The use of a "Nodal Activity Score" (lines 212-226) is clever but might actually be less informative than showing contributions from individual nodal target genes. The combining of counts data from 29 predicted nodal targets means that the contribution (or lack of contribution) from each gene becomes masked. The authors should include supplementary dot plots that break down the score across all 29 genes, allowing the reader to assess overall contributions and/or sub-clusters of gene co-expression patterns, if present.

Thank you very much for the reviewer's positive feedback on our use of the "Nodal Activity Score" and the valuable suggestions provided. Following the recommendation, we analyzed the expression of the 29 Nodal direct targets used in our study across the WT, ndr1 knockdown (kd), and lft1 knockout (ko) groups. We found that the known axial mesoderm genes, such as chrd, tbxta, noto, and gsc, contributed significantly to the Nodal score. The newly conducted analysis has been included in the Supplementary Information (Please see Figure S7L).

- The differential expression trends being reported for srcap (line 251) do not appear to be significant. Are details and P-values for these DEG tests reported somewhere in the manuscript?

We thank the reviewer for raising this question. Based on the reviewer's comment, we performed statistical tests (Wilcoxon test) to compare the expression of srcap in PP and Endo. Our analysis revealed that while srcap expression is slightly higher in PP than in Endo, this difference is not statistically significant. The specific p-value and fold change have been indicated in the revised figure (Please see Figure 4J and S7H). Based on this analysis, we revised our description to state that srcap expression is slightly higher in the PP compared to in the anterior endoderm.

- Following the drug experiments with the drug AU15330 (lines 254-263), authors have only reported #s of endodermal cells, which seem to have increased, which the authors suggest indicates a fate switch from PP to endo. However, the authors have not reported whether the numbers of PP cells decreased or stayed the same in these embryos. This would be helpful information to include, as it is very difficult to discern quantitative trends from the images presented in Fig 4H and 4L.

Thank the reviewer for his/her comments and suggestions. Following the reviewer's suggestions, we performed Imaris analysis on the HCR staining results from the DMSO (control), 1μM AU15330-treated, and 5μM AU15330-treated groups. Our analysis focused on the number of frzb-positive cells (PP), and the comparison revealed that treatment with AU15330 significantly reduces the PP cell number. These findings have been incorporated into the revised manuscript and supplementary information (Please see Figures S7J and S7K).

Reviewer #2 (Public review):

Summary:

During vertebrate gastrulation, the mesoderm and endoderm arise from a common population of precursor cells and are specified by similar signaling events, raising questions as to how these two germ layers are distinguished. Here, Cheng and colleagues use zebrafish gastrulation as a model for mesoderm and endoderm segregation. By reanalyzing published single-cell sequencing data, they identify a common progenitor population for the anterior endoderm and the mesodermal prechordal plate (PP). They find that expression levels of PP genes Gsc and ripply are among the earliest differences between these populations and that their increased expression suppresses the expression of endoderm markers. Further analysis of chromatin accessibility and Ripply cut-and-tag is consistent with direct repression of endoderm by this PP marker. This study demonstrates the roles of Gsc and Ripply in suppressing anterior endoderm fate, but this role for Gsc was already known and the effect of Ripply is limited to a small population of anterior endoderm. The manuscript also focuses extensively on the function of Nodal in specifying and patterning the mesoderm and endoderm, a role that is already well known and to which the current analysis adds little new insight.

We would like to thank the reviewer #2 for the constructive comments and positive feedback regarding our manuscript.

Strengths:

Integrated single-cell ATAC- and RNA-seq convincingly demonstrate changes in chromatin accessibility that may underlie the segregation of mesoderm and endoderm lineages, including Gsc and ripply. Identification of Ripply-occupied genomic regions augments this analysis. The genetic mutants for both genes provide strong evidence for their function in anterior mesendoderm development, although these phenotypes are subtle.

We thank the reviewer for recognizing our work, and we greatly appreciate the constructive suggestions from the reviewer.

Weaknesses:

The use of zebrafish embryonic explants for cell fate trajectory analysis (rather than intact embryos) is not justified. In both transcriptomic comparisons between the two fate trajectories of interest and Ripply cut-and-tag analysis, the authors rely too heavily on gene ontology which adds little to our functional understanding. Much of the work is focused on the role of Nodal in the mesoderm/endoderm fate decision, but the results largely confirm previous studies and again provide few new insights. Some experiments were designed to test the relationship between the mesoderm and endoderm lineages and the role of epigenetic regulators therein, but these experiments were not properly controlled and therefore difficult to interpret.

We sincerely thank the reviewer for the comments. As we previously answered, in our study of the fate differentiation between the PP and the anterior endoderm, we initially analyzed zebrafish embryonic data. However, when we used URD to reconstruct the transcriptional trajectory tree, we found that these two cell trajectories were distantly located on the tree. Existing studies have shown that the anterior endoderm and the PP are not only spatially adjacent but also both originate from mesendodermal progenitor cells and share transcriptional similarities[2-4]. Therefore, when tracing all progenitor cells of these two trajectories using the URD algorithm, it is easy to include other cell types, such as ventral mesendodermal cells (Please see Author response image 2A). Based on this, we believe that directly using embryonic data to decipher the mechanism of fate differentiation between the PP and the anterior endoderm may not yield sufficiently precise results. In contrast, our group’s previous study published in Cell Reports demonstrated that the Nodal-induced explant system can specifically enrich dorsal mesendodermal cells, including the anterior endoderm, PP, and notochord[5]. Thus, we consider the Nodal explant system as an ideal model for studying the fate differentiation mechanism between the PP and the anterior endoderm. Ultimately, through comprehensive analysis of in vivo embryonic data and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitor cells—a conclusion further validated by live imaging experiments.

Regarding the GO analysis, we have streamlined it as suggested by the reviewers. In the revised manuscript, we analyzed the expression of specific genes contributing to key GO functions. Additionally, in the revised version, we conducted more live imaging experiments and quantitative cell assays. We designed gRNA for srcap using the CRISPR CAS13 system to knock down srcap, which further corroborated the morpholino knockdown results, showing consistency with the morpholino data. We also performed Western blot validation of the SWI/SNF complex's response to the drug AU15330, confirming the drug's effectiveness. We hope these additional experiments adequately address the reviewers' concerns.

Reviewer #2 (Recommendations For The Authors):

(1) In the introduction, the authors state that mesendoderm segregates into mesoderm and endoderm in a Nodal-concentration dependent manner. While it is true that higher Nodal signaling levels are required for endoderm specification, A) this is also true for some mesoderm populations, and B) Work from Caroline Hill's lab has shown that Nodal activity alone is not determinative of endoderm fate. Although the authors cite this work, it is conclusions are not reflected in this over-simplified explanation of mesendoderm development. The authors also state that it is not clear when PP and endoderm can be distinguished transcriptionally, but this was also addressed in Economou et al, 2022, which found that they can be distinguished at 60% epiboly but not 50% epiboly.

We sincerely thank the reviewer for raising this question and reminding us of the conclusions drawn from that excellent study. As the reviewer pointed out, Economou et al. demonstrated that Nodal signaling alone is insufficient to determine the cell fate segregation of mesendoderm[6]. However, their study primarily focused on the fate segregation of the ventral-lateral mesendoderm lineage. In contrast, we believe that the mechanisms underlying dorsal mesendoderm specification may differ.

First, it is well-studied that in zebrafish embryos, the most dorsal mesendoderm is initially specified by the activity of the dorsal organizer. Notably, the Nodal signaling ligands ndr1 and ndr2 begin to be expressed in the dorsal organizer as early as the sphere stage[7]. In our study, through single-cell transcriptomic trajectory analysis and live imaging analysis, we observed that the cell fate segregation of the dorsal mesendoderm can be traced back to the shield stage.

Second, the regulatory mechanisms governing dorsal mesendoderm fate differentiation may differ from those of the ventral-lateral mesendoderm. For instance, the gsc gene is exclusively expressed in the dorsal mesendoderm and is absent in the ventral-lateral mesendoderm. Given that gsc is a critical master gene, its overexpression in the ventral side can induce a complete secondary body axis. Similarly, ripply1, identified in our study, is also expressed early and specifically in the dorsal mesendoderm. Overexpression of ripply1 in the ventral side similarly induces a secondary body axis, albeit with the absence of the forebrain[5]. In this study, we found that gsc and ripply1 as the repressor, collectively inhibited dorsal (anterior) endoderm specified from PP progenitors.

In summary, our study focuses on the regulatory mechanisms of fate segregation in the dorsal (anterior) mesendoderm, which differs from the mechanisms of ventral-lateral mesendoderm lineage segregation reported by Economou et al. We believe that this distinction represents a key novelty of our work.

(2) As noted in the manuscript, Warga and Nusslein-Volhard determined long ago that PP and anterior endoderm share a common precursor. It is surprising that this close relationship is not apparent from the lineage trees in whole embryos but is apparent in lineage trees from explants. The authors speculate that the resolution of the whole embryo dataset is insufficient to detect this branch point and propose explants as the solution, but it is not clear why the explant dataset is higher resolution and/or more appropriate to address this question.

We sincerely thank the reviewer for their thoughtful comments. As we mentioned previously, our investigation of fate differentiation between the PP and the anterior endoderm initially involved the analysis of zebrafish embryonic data. However, when we used URD to reconstruct the transcriptional trajectory tree, we observed that these two cell trajectories were located far apart. Previous elegant studies, as the reviewer mentioned, have shown that the anterior endoderm and the PP are not only spatially adjacent but also both originate from mesendodermal progenitor cells and share transcriptional similarities[2,3,8]. Consequently, when tracing all progenitor cells of these two trajectories using the URD algorithm, other cell types—such as ventral mesendodermal cells—are easily included. Based on this, we believe that directly using embryonic data to elucidate the mechanism of fate differentiation between the PP and the anterior endoderm may lack sufficient precision.

In contrast, our group’s previous study published in Cell Reports demonstrated that the Nodal-induced explant system specifically enriches dorsal mesendodermal cells, including the anterior endoderm, PP, and notochord[5]. Therefore, we consider the Nodal explant system as an ideal model for studying the mechanism underlying fate differentiation between the PP and the anterior endoderm. Through comprehensive analyses of both in vivo embryonic and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitor cells—a conclusion further supported by live imaging experiments.

(3) Much of the analysis of DEGs between the lineages of interest is focused on GO term enrichment. But this logic is circular. The endoderm lineage is defined as such because it expresses endoderm-enriched genes, therefore the finding that the endoderm lineage is enriched for endoderm-related GO terms adds no new insights.

We thank the reviewer for these comments. As the reviewers suggested, in the revised manuscript, we indicated specific genes associated with key GO terms (Please see Figure 4B). Additionally, we have streamlined the content related to the GO analysis as suggested.

(4) The authors describe the experiment in Figure S4 as key evidence that Gsc+ cells can give rise to endoderm, but no controls are presented. Only a few cells are shown that express mCherry upon injection of sox17:cre constructs. Is mCherry also expressed in the occasional cell injected with Gsc:lox-stop-lox-mCherry in the absence of cre? Although they report 3 independent replicates, it appears that only 2 individual embryos express mCherry. This very small number is not convincing, especially in the absence of appropriate controls.

We thank the reviewer for raising this question. Following the reviewer's suggestion, we injected gsc:loxp-stop-loxp-mCherry into zebrafish embryos at the 1-cell stage as a control. After performing at least three independent replicates and analyzing no fewer than 100 embryos, we did not observe any mCherry-positive cells. Additionally, we co-injected gsc:loxp-stop-loxp-mCherry with sox17:cre and increased the sample size. Furthermore, we constructed plasmids of sox17:loxp-stop-loxp-mCherry and gsc:cre, and upon injection at the 1-cell stage, we observed RFP-positive cells at 8 hpf (Please see Author response image 1 and Figure S4E). Together with our live imaging data, these experiments collectively demonstrate that anterior endodermal cells can originate from PP progenitors.

(5) The authors spend a lot of effort demonstrating that PP and anterior endoderm are Nodal dependent. First, these data (especially Figures 3E and 3I) are not very convincing, as the differences shown are very small or not apparent. Second, this is already well-known and adds nothing to our understanding of mesoderm-endoderm segregation.

We sincerely thank the reviewer for their insightful questions. First, the reviewer mentioned that in the initial version of our manuscript, the effects of ndr1 knockdown and lefty1 knockout on Nodal signaling and cell fate—particularly prechordal plate (PP) and anterior endoderm (endo)—in Nodal-induced explants were not very pronounced. We recognize that the negative feedback mechanism between Nodal and Lefty signaling may explain why Nodal acts as a morphogen, regulating pattern formation through a Turing-like model[9]. Therefore, knocking down a Nodal ligand gene, such as ndr1 in this study, or knocking out a Nodal inhibitor, such as lft1, may only have a subtle impact on Nodal signaling[10].

Accordingly, in this study, we performed extensive pSmad2 immunofluorescence analysis and observed that although the overall intensity of Nodal activity did not change dramatically, there was a statistically significant difference. Importantly, this subtle variation in Nodal signaling strength is precisely what we intended to capture, since PP and anterior endoderm are highly sensitive to Nodal signaling[11], and even minor differences may bias their fate segregation.

This leads directly to the reviewer’s second concern. While numerous studies suggest that the strength of Nodal signaling influences mesendodermal fate—with high Nodal promoting endoderm and lower concentrations inducing mesoderm—most of these studies focus on ventral-lateral mesendoderm development[4,6,10]. In contrast, the mechanisms underlying dorsal mesendoderm fate specification differ, which is a key innovation of our study.

Previous work by Bernard Thisse and colleagues demonstrated that even a slight reduction in Nodal signaling, achieved by overexpressing a Nodal inhibitor, is sufficient to cause defects in the specification of PP and endoderm[11]. This indicates that PP and endoderm require the highest levels of Nodal signaling for proper specification. Moreover, the most dorsal mesendoderm, PP and anterior endoderm are not only spatially adjacent but also share similar transcriptional states, making the regulation of their fate separation particularly challenging to study.

The Dr. C.P. lab made important contributions to this issue, showing that the duration of Nodal exposure is critical for segregating PP and anterior endoderm fates: prolonged Nodal signaling promotes expression of the transcriptional repressor Gsc, which directly suppresses the key endodermal transcription factor Sox17, thereby inhibiting anterior endoderm specification[3]. They also found that tight junctions among PP cells facilitate Nodal signal propagation[8]. However, their studies revealed that Gsc mutants do not exhibit endodermal phenotypes, suggesting that additional factors or mechanisms regulate PP versus anterior endoderm fate separation[3].

In our study, we first observed that subtle differences in Nodal concentration may bias the fate choice between PP and anterior endoderm. Given that ndr1 knockdown and lft1 knockout mildly reduce or enhance Nodal signaling, respectively, we reasoned that using these two perturbations in a Nodal-induced explant system combined with single-cell RNA sequencing could generate transcriptomic profiles under slightly reduced and enhanced Nodal signaling. This approach may help identify key decision points and transcriptional differences during PP and anterior endoderm segregation, ultimately uncovering the molecular mechanisms downstream of Nodal that govern their fate separation.

(6) The authors claim that scrap expression differs between the 2 lineages of interest, but this is not apparent from Figure 4J-K. Experiments testing the role of SWI/SNF and scrap also require additional controls. Can scrap MO phenotypes be rescued by scrap RNA? Is there validation that SWI/SNF components are degraded upon treatment with AU15330?

We are very grateful for the reviewers' questions. Using single-cell data from zebrafish embryos and Nodal explants, we compared the expression of srcap in the PP and anterior Endo cell populations. We found that srcap expression showed a slight increase in PP compared to anterior Endo, but the difference was not statistically significant (Please see Figure 4J and S7H). Therefore, we modified our description in the revised manuscript. However, we speculate that this slight difference might influence the distinct cell fate specification between PP and anterior endo. In the original version of the manuscript, we reported that either treatment with AU15330, an inhibitor of the SWI/SNF complex, or injection of morpholino targeting srcap—a key component of the SWI/SNF complex—enhanced anterior endo fate while reducing PP cell specification. During this round of revision, we initially attempted to follow the reviewer’s suggestion to co-inject srcap mRNA along with srcap morpholino to rescue the phenotype. However, we found that the length of srcap mRNA exceeds 10,000 bp, and despite multiple attempts, we were unable to successfully obtain the srcap mRNA. Therefore, we were unable to perform the rescue experiment and instead adopted an alternative approach to validate the function of srcap. We aimed to use anthor knockdown approach (CRISPR/Cas system) to determine whether a phenotype similar to that observed with morpholino knockdown could be achieved. Using the CRISPR/Cas13 system, we designed gRNA targeting srcap, knocked down srcap, and examined the cell specification of PP and anterior endo. We found that, consistent with our previous results, knocking down srcap obviously reduced PP cell fate while increasing anterior endo cell fate (Author response image 3). Additionally, the reviewer raised the question of whether the SWI/SNF complex is degraded after AU15330 treatment. Following the reviewer’s suggestion, we attempted to perform Western blot analysis on BRG1, one of the components of the SWI/SNF complex. However, despite multiple attempts, we were unable to achieve successful detection of the BRG1 protein by the antibody in zebrafish. Several studies have reported that knockdown or knockout of brg1 leads to defects in neural crest cell specification in zebrafish[12,13]. Therefore, alternatively, we treated zebrafish embryos at the one-cell stage with 0 μM (DMSO), 1 μM, and 5 μM AU15330, and examined the expression of sox10 and pigment development around 48 h. We found that treatment with 1 μM AU15330 reduced sox10 expression and pigment production, though not significantly, whereas treatment with 5 μM AU15330 significantly disrupted neural crest cell development. Thus, this experiment demonstrates that AU15330 is functional in zebrafish. (Author response image 3).

Author response image 3.

(A) Characterization of anterior endoderm and PP cells following CRISPR-Cas13d-mediated srcap knockdown. (B) Validation of srcap mRNA expression by RT‑qPCR following CRISPR‑Cas13d knockdown. (C) RT‑qPCR shows the expression of sox10 after treatment with increasing concentrations of AU15300. (D) Morphology of zebrafish embryos at 48 hpf after treatment with increasing concentrations of AU15300.

(7) The authors conclude from their chromatin accessibility analysis that variations in Nodal signaling are responsible for expression levels of PP and endoderm genes, but they do not consider the alternative explanation that FGF signaling is playing this role. Such a function for FGF was established by Caroline Hill's lab, and the authors also show in Figure S5G that FGF signaling in enriched between these cell populations.

Thank you very much for raising this issue. As the reviewer pointed out, Caroline Hill's lab has conducted elegant work demonstrating that FGF signaling plays a crucial role in the separation of ventral-lateral mesendoderm cell fates[4,6]. In contrast, our study primarily focuses on studying the mechanisms underlying the separation of dorsal mesendoderm cell fates. However, our research also reveals that FGF signaling significantly regulates the fate separation of the dorsal mesendoderm, as inhibiting FGF signaling suppresses PP cell specification while promoting anterior Endo fate. In our previously published work, we found that Nodal signaling can directly activate the expression of FGF ligand genes[5]. Therefore, we hypothesize that Nodal signaling, acting as a master regulator, activates various downstream target genes—including FGF—and how FGF signaling regulates the cell fate separation of the dorsal mesendoderm warrants further investigation in our further studies.

(8) When interpreting the results of their Ripply cut-and-run experiment, the authors again rely heavily on GO term analysis and claim that this supports a role for Ripply as a transcriptional repressor. GO term enrichment does not equal functional analysis. It would be more convincing to intersect DEGs between WT and ripply-/- embryos with Ripply-enriched loci.

Thanks for raising this important issue and the constructive suggestion. In response to the reviewer's valid concern regarding the GO term analyses from our CUT&Tag data, we implemented a more stringent filtering strategy. We identified peaks enriched in the treatment group and applied differential analysis, selecting genes with a log₂FoldChange > 3, padj < 0.05, and baseMean > 30 as high-confidence Ripply1 binding targets. A GO enrichment analysis of these genes revealed significant terms related to muscle development, consistent with Ripply1's established role in somite development, thereby validating our approach. We supplemented the related gene list in the revised manuscript. Moreover, within this refined analysis, we found that sox32 met our binding threshold, while sox17 did not. Furthermore, as suggested, we examined mespbb—a known Ripply1-repressed gene—which was present, and gsc, a Nodal target used as a negative control, which was absent. This confirms the specificity of our analysis (Figure 6 and Figure S11). Consequently, our revised analyses support a model in which Ripply1 directly binds the sox32 promoter. Given that Sox32 is a known upstream regulator of sox17, this binding provides a plausible direct mechanism for the observed regulation of sox17 expression. We have updated the figures and text accordingly. We attempted to generate ripply1^-/- mutants but found that homozygous loss results in embryonic lethality.

(9) The way N's are reported is unconventional. N= number of embryos used in the experiment, n= number of embryos imaged. If an embryo was not imaged or analyzed in any way, it cannot be considered among the embryos in an experiment. If only 4 embryos were imaged, the N for that experiment is 4 regardless of how many embryos were stained. Authors should also report not only the number of embryos examined but also the number of independent trials performed for all experiments.

Thank you very much for the reviewer's suggestion. As suggested, we have revised the description regarding the number of embryos and experimental replicates in the figure legends.

(10) The authors should avoid the use of red-green color schemes in figures to ensure accessibility for color-blind readers.

Thanks for the suggestions. We have updated the figures in our revised manuscript and adjusted the color schemes to avoid red-green combinations.

Reviewer #3 (Public Review):

Summary:

Cheng, Liu, Dong, et al. demonstrate that anterior endoderm cells can arise from prechordal plate progenitors, which is suggested by pseudo time reanalysis of published scRNAseq data, pseudo time analysis of new scRNAseq data generated from Nodal-stimulated explants, live imaging from sox17:DsRed and Gsc:eGFP transgenics, fluorescent in situ hybridization, and a Cre/Lox system. Early fate mapping studies already suggested that progenitors at the dorsal margin give rise to both of these cell types (Warga) and live imaging from the Heisenberg lab (Sako 2016, Barone 2017) also pretty convincingly showed this. However, the data presented for this point are very nice, and the additional experiments in this manuscript, however, further cement this result. Though better demonstrated by previous work (Alexander 1999, Gritsman 1999, Gritsman 2000, Sako 2016, Rogers 2017, others), the manuscript suggests that high Nodal signaling is required for both cell types, and shows preliminary data that suggests that FGF signaling may also be important in their segregation. The manuscript also presents new single-cell RNAseq data from Nodal-stimulated explants with increased (lft1 KO) or decreased (ndr1 KD) Nodal signaling and multi-omic ATAC+scRNAseq data from wild-type 6 hpf embryos but draws relatively few conclusions from these data. Lastly, the manuscript presents data that SWI/SNF remodelers and Ripply1 may be involved in the anterior endoderm - prechordal plate decision, but these data are less convincing. The SWI/SNF remodeler experiments are unconvincing because the demonstration that these factors are differentially expressed or active between the two cell types is weak. The Ripply1 gain-of-function experiments are unconvincing because they are based on incredibly high overexpression of ripply1 (500 pg or 1000 pg) that generates a phenotype that is not in line with previously demonstrated overexpression studies (with phenotypes from 10-20x lower expression). Similarly, the cut-and-tag data seems low quality and like it doesn't support direct binding of ripply1 to these loci.

In the end, this study provides new details that are likely important in the cell fate decision between the prechordal plate and anterior endoderm; however, it is unclear how Nodal signaling, FGF signaling, and elements of the gene regulatory network (including Gsc, possibly ripply1, and other factors) interact to make the decision. I suggest that this manuscript is of most interest to Nodal signaling or zebrafish germ layer patterning afficionados. While it provides new datasets and observations, it does not weave these into a convincing story to provide a major advance in our understanding of the specification of these cell types.

We sincerely thank the reviewer for their thorough and thoughtful assessment of our work. The reviewer acknowledged several strengths of our study, such as the use of multiple technical approaches to demonstrate that anterior endoderm differentiates from PP progenitor cells, and recognized the value of the newly added single-cell omics data. The reviewer also raised some concerns regarding the initial version of our work, including the SWI/SNF remodeler experiments and the Ripply1 gain-of-function experiment. In the revised manuscript, we have supplemented these parts with additional control experiments to better support our conclusions. We hope that our updated manuscript adequately addresses the points raised by the reviewer.

Major issues:

(1) UMAPs: There are several instances in the manuscript where UMAPs are used incorrectly as support for statements about how transcriptionally similar two populations are. UMAP is a stochastic, non-linear projection for visualization - distances in UMAP cannot be used to determine how transcriptionally similar or dissimilar two groups are. In order to make conclusions about how transcriptionally similar two populations are requires performing calculations either in the gene expression space, or in a linear dimensional reduction space (e.g. PCA, keeping in mind that this will only consider the subset of genes used as input into the PCA). Please correct or remove these instances, which include (but are not limited to):

p.4 107-110

p.4 112

p.8 207-208

p.10 273-275

We would like to thank the reviewer for raising this question. The descriptions of UMAP have been revised throughout the manuscript in accordance with the reviewer's suggestion (Please see the main text in the revised manuscript).

(2) Nodal and lefty manipulations: The section "Nodal-Lefty regulatory loop is needed for PP and anterior Endo fate specification" and Figure 3 do not draw any significant conclusions. This section presents a LIANA analysis to determine the signals that might be important between prechordal plate and endoderm, but despite the fact that it suggests that BMP, Nodal, FGF, and Wnt signaling might be important, the manuscript just concludes that Nodal signaling is important. Perhaps this is because the conclusion that Nodal signaling is required for the specification of these cell types has been demonstrated in zebrafish in several other studies with more convincing experiments (Alexander 1999, Gritsman 1999, Gritsman 2000, Rogers 2017, Sako 2016). While FGF has recently been demonstrated to be a key player in the stochastic decision to adopt endodermal fate in lateral endoderm (Economou 2022), the idea that FGF signaling may be a key player in the differentiation of these two cell types has strangely been relegated to the discussion and supplement. Lastly, the manuscript does not make clear the advantage of performing experiments to explore the PP-Endo decision in Nodal-stimulated explants compared to data from intact embryos. What would be learned from this and not from an embryo? Since Nodal signaling stimulates the expression of Wnts and FGFs, these data do not test Nodal signaling independent of the other pathways. It is unclear why this artificial system that has some disadvantages is used since the manuscript does not make clear any advantages that it might have had.

We sincerely thank the reviewers for their valuable comments. As mentioned in our manuscript, although a substantial number of studies have reported on the mechanisms governing the segregation of mesendoderm fate in zebrafish embryos—including the Dr. Hill laboratory’s work cited by the reviewers, which demonstrated the involvement of FGF signaling in the ventral mesendoderm fate specification—research on the regulatory mechanisms underlying anterior mesendoderm differentiation remains relatively limited. This is largely due to the challenges posed by the close physical proximity and similar transcriptional states of anterior mesendoderm cells, as well as their shared dependence on high levels of Nodal signaling for specification.

Several studies from the Dr. C.P. Heisenberg’s laboratory have attempted to elucidate the fate segregation between anterior mesendoderm cells, namely the prechordal plate (PP) and anterior endoderm (endo) cells. They found that PP cells are tightly connected, facilitating the propagation of Nodal signaling[8]. Prolonged exposure to Nodal activates the expression of Gsc, which acts as a transcriptional repressor to inhibit sox17 expression, thereby suppressing endodermal fate[3]. However, they also noted that Gsc mutants do not exhibit endoderm developmental defects, suggesting the involvement of additional factors in this process.

The reviewer inquired about our rationale for using the Nodal-injected explant system. In our investigation of the fate separation between the PP and the anterior endo, we initially analyzed zebrafish embryonic data. Using URD to reconstruct the transcriptional lineage tree, we found that these two cell types were positioned distantly from each other. However, existing literature indicates that the anterior endoderm and PP are not only spatially adjacent but also derive from common mesendodermal progenitors and exhibit transcriptional similarities[2,8]. As the reviewer noted, when tracing all progenitor cells of these two lineages using URD, it is easy to inadvertently include other cell types—such as ventral epiblast cells—which may compromise the accuracy of the analysis. We therefore concluded that directly using embryonic data to dissect the mechanism of fate separation between PP and anterior endoderm might not yield highly precise results.

By contrast, our group’s earlier study published in Cell Reports demonstrated that the Nodal-induced explant system specifically enriches dorsal mesendodermal cells, including anterior endo, PP, and notochord[5]. This makes the Nodal explant system a highly suitable model for studying the fate separation between PP and anterior endo. Ultimately, by analysing in vivo embryonic data and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitors—a conclusion further supported by live imaging experiments.

As we answered above, we first used the analyses of single-cell RNA sequencing and live imaging to demonstrate that anterior endoderm can originate from PP progenitor cells. Understanding the mechanism underlying the fate segregation between these two cell populations became a key focus of our research. We began by applying cell communication analysis to our single-cell data to identify signaling pathways that may be involved. This analysis specifically highlighted the Nodal-Lefty signaling pathway. Since Lefty acts as an inhibitor of Nodal signaling, we hypothesized that differences in Nodal signaling strength might regulate the fate of these two cell populations. By overexpressing different concentrations of Nodal mRNA and examining the fates of PP and anterior Endo cells, we confirmed this hypothesis.

Thus, we propose that even subtle differences in Nodal signaling levels may influence anterior mesendoderm fate decisions. To test this, we generated systems with slightly reduced Nodal signaling (via ndr1 knockdown) and slightly elevated Nodal signaling (via lft1 knockout). Using these models, we precisely captured the critical stage of fate segregation between PP and anterior endo cells and identified a novel transcriptional repressor, Ripply1, which works in concert with Gsc to suppress anterior endoderm differentiation.

(3) ripply1 mRNA injection phenotype inconsistent with previous literature: The phenotype presented in this manuscript from overexpressing ripply1 mRNA (Fig S11) is inconsistent with previous observations. This study shows a much more dramatic phenotype, suggesting that the overexpression may be to a non-physiological level that makes it difficult to interpret the gain-of-function experiments. For instance, Kawamura et al 2005 perform this experiment but do not trigger loss of head and eye structures or loss of tail structures. Similarly, Kawamura et al 2008 repeat the experiment, triggering a mildly more dramatic shortening of the tail and complete removal of the notochord, but again no disturbance of head structures as displayed here. These previous studies injected 25 - 100 pg of ripply1 mRNA with dramatic phenotypes, whereas this study uses 500 - 1000 pg. The phenotype is so much more dramatic than previously presented that it suggests that the level of ripply1 overexpression is sufficiently high that it may no longer be regulating only its endogenous targets, making the results drawn from ripply1 overexpression difficult to trust.

We sincerely thank the reviewer for raising this question. First, we apologize for not providing a detailed description of the amount of HA-ripply1 mRNA injected in our previous manuscript. We injected 500 pg of HA-ripply1 mRNA at the 1-cell stage and allowed the embryos to develop until 6 hpf for the CUT&Tag experiment. In the supplementary materials, we included a bright-field image of an 18 hpf-embryo injected with HA-ripply1 mRNA, which morphologically exhibited severe developmental abnormalities. The reviewer pointed out that the amount of ripply1 mRNA we injected might be excessive, potentially leading to non-specific gain-of-function effects. The injection dose of 500 pg was determined based on conclusions from our previous study. In that study, injecting 24 pg of ripply1 mRNA into one cell of zebrafish embryos at the 16–32 cell stage was sufficient to induce a secondary axis lacking the forebrain[5]. From this, we estimated that an injection concentration of approximately 500–1000 pg would be appropriate at the 1-cell stage, so that after several rounds of cell division, each cell gained 20-30 pg mRNA at 32 cell stage. Additionally, we conducted supplementary experiments injecting 100 pg, 250 pg, and 500 pg of ripply1 mRNA, and observed 500 pg of ripply1 mRNA led to a dramatic suppression of endoderm formation (Author response image 4).

Finally, our study focuses on the mechanism of cell fate segregation in the anterior mesendoderm, primarily during gastrulation. The embryos injected with ripply1 mRNA underwent normal gastrulation, and our CUT&Tag experiment was performed at 6 hpf. Therefore, we believe that the amount of ripply1 mRNA injected in this study is appropriate for addressing our research question.

Author response image 4.

Different concentrations of ripply1 mRNA were injected into zebrafish embryos at the one-cell stage, with RFP fluorescence labeling sox17-positive cells.

(4) Ripply1 binding to sox17 and sox32 regulatory regions not convincing: The Cut and Tag data presented in Fig 6J-K does not seem to be high quality and does not seem to provide strong support that Ripply 1 binds to the regulatory regions of these genes. The signal-to-noise ratio is very poor, and the 'binding' near sox17 that is identified seems to be even coverage over a 14 kb region, which is not consistent with site-specific recruitment of this factor, and the 'peaks' highlighted with yellow boxes do not appear to be peaks at all. To me, it seems this probably represents either: (1) overtagmentation of these samples or (2) an overexpression artifact from injection of too high concentration of ripply1-HA mRNA. In general, Cut and Tag is only recommended for histone modifications, and Cut and Run would be recommended for transcriptional regulators like these (see Epicypher's literature). Given this and the previous point about Ripply1 overexpression, I am not convinced that Ripply1 regulates endodermal genes. The existing data could be made somewhat more convincing by showing the tracks for other genes as positive and negative controls, given that Ripply1 has known muscle targets (how does its binding look at those targets in comparison) and there should be a number of Nodal target genes that Ripply1 does not bind to that could be used as negative controls. Overall this experiment doesn't seem to be of high enough quality to drive the conclusion that Ripply1 directly binds near sox17 and sox32 and from the data presented in the manuscript looks as if it failed technically.

We sincerely thank the reviewer for raising this question. We apologize that the binding regions of sox17 marked in our previous analysis were incorrect, and we have made the corresponding revisions in the latest version of the manuscript.

The reviewer noted that our CUT&Tag data contain considerable noise. To address this, we further refined our data processing: we annotated all peaks enriched in the treatment group and performed differential analysis, selecting genes with log₂FoldChange > 3, padj < 0.5, and baseMean > 30 as candidate targets of Ripply1 binding. Subsequent GO enrichment analysis of these genes revealed significant enrichment of muscle development-related GO terms, which is consistent with previously reported roles of Ripply1 in regulating somite development. Therefore, we believe our filtering method effectively removes a large number of noise peaks and their associated genes.

Under these screening criteria, we found that sox32 meets the threshold, while sox17 does not. In addition, following the reviewer’s suggestion, we examined mespbb—a known gene repressed by Ripply1—and gsc, a Nodal target gene, as a negative control.

Based on these new analyses, we have revised our figures and text accordingly. Our data now support the possibility that Ripply1 may directly bind to the promoter region of sox32. Since sox32 acts as a direct upstream regulator of sox17, this binding could influence sox17 expression (Figure 6 and Figure S11).

Finally, we would like to note that studies have reported Ripply1 as a transcriptional repressor, which may function by recruiting other co-factors, such as Groucho, to form a complex[14,15]. This might explain why our CUT&Tag data detected Ripply1 binding to a broad set of genes.

(5) "Cooperatively Gsc and ripply1 regulate": I suggest avoiding the term "cooperative," when describing the relationship between Ripply1 and Gsc regulation of PP and anterior endoderm - it evokes the concept of cooperative gene regulation, which implies that these factors interact with each biochemically in order to bind to the DNA. This is not supported by the data in this manuscript, and is especially confusing since Ripply1 is thought to require cooperative binding with a T-box family transcription factor to direct its binding to the DNA.

We sincerely thank the reviewer for raising this important issue. The reviewer pointed out that the term "Cooperatively" may not be entirely appropriate in the context of our study. In accordance with the reviewer's suggestion, we have replaced "Cooperatively" with "Collectively" in the relevant sections.

(6) SWI/SNF: The differential expression of srcap doesn't seem very remarkable. The dot plots in the supplement S7H don't help - they seem to show no expression at all in the endoderm, which is clearly a distortion of the data, since from the violin plots it's obviously expressed and the dot-size scale only ranges from ~30-38%. Please add to the figure information about fold-change and p-value for the differential expression. Publicly available scRNAseq databases show scrap is expressed throughout the entire early embryo, suggesting that it would be surprising for it to have differential activity in these two cell types and thereby contribute to their separate specification during development. It seems equally possible that this just mildly influences the level of Nodal or FGF signaling, which would create this effect.

Thank the Reviewer for this question. As suggested, we performed Wilcoxon tests to compare srcap expression between PP and Endo populations. The analysis shows that while srcap expression is moderately elevated in PP compared to in Endo, this difference is not statistically significant. The corresponding p-value and fold change have now been included in the revised figure (Please see Figure 4J and S7H). Although the transcriptional level of srcap shows no significant difference between PP and anterior endoderm, our subsequent experiments—using AU15330 (an inhibitor of the SWI/SNF complex) and injecting morpholino targeting srcap, a key component of the SWI/SNF complex—demonstrated that its inhibition indeed promotes anterior endoderm fate while reducing PP cell specification. Therefore, we propose that subtle differences in the SWI/SNF complex may regulate the fate specification of PP and anterior endoderm through two mechanisms. First, as mentioned in our study, these chromatin remodelers modulate the expression of master regulators such as Gsc and Ripply1, thereby influencing cell fate decisions. Second, as noted by the reviewer, these chromatin remodelers may affect the interpretation of Nodal signaling, ultimately contributing to the divergence between PP and anterior endoderm fates.

The multiome data seems like a valuable data set for researchers interested in this stage of zebrafish development. However, the presentation of the data doesn't make many conclusions, aside from identifying an element adjacent to ripply1 whose chromatin is open in prechordal plate cells and not endodermal cells and showing that there are a number of loci with differential accessibility between these cell types. That seems fairly expected since both cell types have several differentially expressed transcriptional regulators (for instance, ripply1 has previously been demonstrated in multiple studies to be specific to the prechordal plate during blastula stages). The manuscript implies that SWI/SNF remodeling by Srcap is responsible for the chromatin accessibility differences between these cell types, but that has not actually been tested. It seems more likely that the differences in chromatin accessibility observed are a result of transcription factors binding downstream of Nodal signaling.

We thank the reviewer for recognizing the value of our newly generated data. Through integrative analysis of single-cell data from wild-type, ndr1 kd, and lft1 ko groups of Nodal-injected explants at 6 hours post-fertilization (hpf), we identified a critical branching point in the fate segregation of the prechordal plate (PP) and anterior endoderm (Endo), where chromatin remodelers may play a significant role. Based on this finding, we performed single-cell RNA and ATAC sequencing on zebrafish embryos at 6 hpf. Analysis of this multi-omics dataset revealed that transcriptional repressors such as Gsc, Ripply1, and Osr1 exhibit differences in both transcriptional and chromatin accessibility levels between the PP and anterior Endo. Subsequent overexpression and loss-of-function experiments further demonstrated that Gsc and Ripply1 collaboratively suppress endodermal gene expression, thereby inhibiting endodermal cell fate. Previous studies have reported that for the activation of certain Nodal downstream target genes, the pSMAD2 protein of the Nodal signaling pathway recruits chromatin remodelers to facilitate chromatin opening and promote further transcription of target genes[16]. Therefore, our data provide chromatin accessibility profiles for Gsc and Ripply1, offering a valuable resource for future investigations into their pSMAD2 binding sites.

Minor issues:

Figure 2 E-F: It's not clear which cells from E are quantitated in F. For instance, the dorsal forerunner cells are likely to behave very differently from other endodermal progenitors in this assay. It would be helpful to indicate which cells are analyzed in Fig F with an outline or other indicator of some kind. Or - if both DFCs and endodermal cells are included in F, to perhaps use different colors for their points to help indicate if their fluorescence changes differently.

Thank you for the reviewer's suggestion. In the revised version of the figure, we have outlined the regions of the analyzed cells.

Fig 3 J: Should the reference be Dubrulle et al 2015, rather than Julien et al?

Thanks, we have corrected.

References:

Alexander, J. & Stainier, D. Y. A molecular pathway leading to endoderm formation in zebrafish. Current biology : CB 9, 1147-1157 (1999).

Barone, V. et al. An Effective Feedback Loop between Cell-Cell Contact Duration and Morphogen Signaling Determines Cell Fate. Dev. Cell 43, 198-211.e12 (2017).

Economou, A. D., Guglielmi, L., East, P. & Hill, C. S. Nodal signaling establishes a competency window for stochastic cell fate switching. Dev. Cell 57, 2604-2622.e5 (2022).

Gritsman, K. et al. The EGF-CFC protein one-eyed pinhead is essential for nodal signaling. Cell 97, 121-132 (1999).

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Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aimed to elucidate the recruitment order and assembly of the Cdv proteins during Sulfolobus acidocaldarius archaeal cell division using a bottom-up reconstitution approach. They employed liposome-binding assays, EM, and fluorescence microscopy with in vitro reconstitution in dumbbellshaped liposomes to explore how CdvA, CdvB, and the homologues of ESCRT-III proteins (CdvB, CdvB1, and CdvB2) interact to form membrane remodeling complexes.

The study sought to reconstitute the Cdv machinery by first analyzing their assembly as two subcomplexes: CdvA:CdvB and CdvB1:CdvB2ΔC. The authors report that CdvA binds lipid membranes only in the presence of CdvB and localizes preferentially to membrane necks. Similarly, the findings on CdvB1:CdvB2ΔC indicate that truncation of CdvB2 facilitates filament formation and enhances curvature sensitivity in interaction with CdvB1. Finally, while the authors reconstitute a quaternary CdvA:CdvB:CdvB1:CdvB2 complex and demonstrate its enrichment at membrane necks, the mechanistic details of how these complexes drive membrane remodeling by subcomplexes removal by the proteasome and/or CdvC remain speculative.

Although the work highlights intriguing similarities with eukaryotic ESCRT-III systems and explores unique archaeal adaptations, the conclusions drawn would benefit from stronger experimental validation and a more comprehensive mechanistic framework.

Strengths:

The study of machinery assembly and its involvement in membrane remodeling, particularly using bottom-up reconstituted in vitro systems, presents significant challenges. This is particularly true for systems like the ESCRT-III complex, which localizes uniquely at the lumen of membrane necks prior to scission. The use of dumbbell-shaped liposomes in this study provides a promising experimental model to investigate ESCRT-III and ESCRT-III-like protein activity at membrane necks.

The authors present intriguing evidence regarding the sequential recruitment of ESCRT-III proteins in crenarchaea-a close relative of eukaryotes. This finding suggests that the hierarchical recruitment characteristic of eukaryotic systems may predate eukaryogenesis, which is a significant and exciting contribution. However, the broader implications of these findings for membrane remodeling mechanisms remain speculative, and the study would benefit from stronger experimental validation and expanded contextualization within the field.

We thank the Referee for his/her appreciation of our work.

Weaknesses:

This manuscript presents several methodological inconsistencies and lacks key controls to validate its claims. Additionally, there is insufficient information about the number of experimental repetitions, statistical analyses, and a broader discussion of the major findings in the context of open questions in the field.

We have now added more controls, information about repetitions, and discussion.

Reviewer #2 (Public review):

Summary:

The Crenarchaeal Cdv division system represents a reduced form of the universal and ubiquitous ESCRT membrane reverse-topology scission machinery, and therefore a prime candidate for synthetic and reconstitution studies. The work here represents a solid extension of previous work in the field, clarifying the order of recruitment of Cdv proteins to curved membranes.

Strengths:

The use of a recently developed approach to produce dumbbell-shaped liposomes (De Franceschi et al. 2022), which allowed the authors to assess recruitment of various Cdv assemblies to curved membranes or membrane necks; reconstitution of a quaternary Cdv complex at a membrane neck.

We thank the Referee for his/her appreciation of the work.

Weaknesses:

The manuscript is a bit light on quantitative detail, across the various figures, and several key controls are missing (CdvA, B alone to better interpret the co-polymerisation phenotypes and establish the true order of recruitment, for example) - addressing this would make the paper much stronger. The authors could also include in the discussion a short paragraph on implications for our understanding of ESCRT function in other contexts and/or in archaeal evolution, as well as a brief exploration of the possible reasons for the discrepancy between the foci observed in their liposome assays and the large rings observed in cells - to better serve the interests of a broad audience.

We have now added more controls, information about repetitions, and discussion.

Reviewer #3 (Public review):

Summary:

In this report, De Franceschi et al. purify components of the Cdv machinery in archaeon M. sedula and probe their interactions with membrane and with one-another in vitro using two main assays - liposome flotation and fluorescent imaging of encapsulated proteins. This has the potential to add to the field by showing how the order of protein recruitment seen in cells is related to the differential capacity of individual proteins to bind membranes when alone or when combined.

Strengths:

Using the floatation assay, they demonstrate that CdvA and CdvB bind liposomes when combined. While CdvB1 also binds liposomes under these conditions, in the floatation assay, CdvB2 lacking its C-terminus is not efficiently recruited to membranes unless CdvAB or CdvB1 are present. The authors then employ a clever liposome assay that generates chained spherical liposomes connected by thin membrane necks, which allows them to accurately control the buffer composition inside and outside of the liposome. With this, they show that all four proteins accumulate in necks of dumbbell-shaped liposomes that mimic the shape of constricting necks in cell division. Taken altogether, these data lead them to propose that Cdv proteins are sequentially recruited to the membrane as has also been suggested by in vivo studies of ESCRT-III dependent cell division in crenarchaea.

We thank the Referee for his/her appreciation of the work.

Weaknesses:

These experiments provide a good starting point for the in vitro study the interaction of Cdv system components with the membrane and their consecutive recruitment. However, several experimental controls are missing that complicate their ability to draw strong conclusions. Moreover, some results are inconsistent across the two main assays which make the findings difficult to interpret:

(1) Missing controls.

Various protein mixtures are assessed for their membrane-binding properties in different ways. However, it is difficult to interpret the effect of any specific protein combination, when the same experiment is not presented in a way that includes separate tests for all individual components. In this sense, the paper lacks important controls. For example, Fig 1C is missing the CdvB-only control. The authors remark that CdvB did not polymerise (data not shown) but do not comment on whether it binds membrane in their assays. In the introduction, Samson et al., 2011 is cited as a reference to show that CdvB does not bind membrane. However, here the authors are working with protein from a different organism in a different buffer, using a different membrane composition and a different assay. Given that so many variables are changing, it would be good to present how M. sedula CdvB behaves under these conditions.

We thank the referee for raising this point. We have now added these data in Figure 1C. Indeed it turns out that CdvB from M. sedula exhibits clear membrane binding on its own in a flotation assay.

Similarly, there is no data showing how CdvB alone or CdvA alone behave in the dumbbell liposome assay.

Without these controls, it's impossible to say whether CdvA recruits CdvB or the other way around. The manuscript would be much stronger if such data could be added.

We have now added these data in Figure 1E, 1F and 1G. Overall, we can confirm that CdvA binds the membrane better in the presence of CdvB (although both proteins can bind the membrane on their own). Both proteins appear to recognize the curved region of the membrane neck.

(2) Some of the discrepancies in the data generated using different assays are not discussed.

The authors show that CdvB2∆C binds membrane and localizes to membrane necks in the dumbbell liposome assay, but no membrane binding is detected in the flotation assay. The discrepancy between these results further highlights the need for CdvB-only and CdvA-only controls.

We have now added these controls in Figure 1. In addition, we would like to clarify that the flotation assay and the SMS dumbbell assay serve different purposes and are not directly comparable in quantitative terms. In the flotation assay, all the protein present as input is eventually recovered and visualized. Thus, quantitative information on the proportion of the fraction of the total protein bound to lipids can be inferred from this assay. The SMS assay, in contrast, provides a very different kind of information. Because of the particular protocol required to generate dumbbells (De Franceschi, 2022), the total amount of protein in the inner buffer in dumbbells is not accurately defined, because protein that is not correctly reconstituted (e.g. which aggregates while still in the droplet phase) will interfere with vesicle generation, with the result that dumbbell with such aggregates is generally not formed in the first place. This renders it impossible to draw any quantitative conclusions about the proportion of the sample bound to lipids. The SMS is therefore not directly comparable to the flotation assay, and it is rather complementary to it. Indeed, the purpose of the SMS is to provide information about curvature selectivity of the protein.

(3) Validation of the liposome assay.

The experimental setup to create dumbbell-shaped liposomes seems great and is a clever novel approach pioneered by the team. Not only can the authors manipulate liposome shape, they also state that this allows them to accurately control the species present on the inside and outside of the liposome. Interpreting the results of the liposome assay, however, depends on the geometry being correct. To make this clearer, it would seem important to include controls to prove that all the protein imaged at membrane necks lie on the inside of liposomes. In the images in SFig3 there appears to be protein outside of the liposome. It would also be helpful to present data to show test whether the necks are open, as suggested in the paper, by using FRAP or some other related technique.

We thank the Referee for his/her appreciation. The proteins are encapsulated inside the liposomes, not outside of them. While Figure S3 might give the appearance that there is some protein outside, this is actually just an imaging artifact. Author response image 1 (below) explains this: When the membrane and protein channel are shown separately, it is clear that the protein cluster that appeared to be ‘outside’ actually colocalizes with an extra small dumbbell lobe (yellow arrowhead). The protein appeared to be outside of it because (1) the protein fluorescent signal is stronger than the signal from the membrane, and (2) there is a certain time delay in the acquisition of the two channels (0.5-1 second), thus the membrane may have slightly shifted out of focus when the fluorescence was being acquired. We are confident that the protein is inside in these dumbbells because the procedure for preparing the dumbbells requires extensive emulsification by pipetting, which requires ≈ 1 minute. This time is more than sufficient for proteins with high affinity for the membrane, like ESCRT and Cdv, to bind the membrane. For an example of how fast binding under confinement can be, please see movie 2 from this paper: De Franceschi N, Alqabandi M, Miguet N, Caillat C, Mangenot S, Weissenhorn W, Bassereau P. The ESCRT protein CHMP2B acts as a diffusion barrier on reconstituted membrane necks. J Cell Sci. 2018 Aug 3;132(4):jcs217968.

Moreover, in many instances, we observed that the protein is inside because, by increasing the gain in the images post-acquisition, a clear protein signal appear in the lumen (see Author response image 2).

Author response image 1.

Separate channels showing colocalization of protein and lipids (adapted from Figure S3). The zoom-in shows separate channels, highlighting that the CdvB2 cluster that seems to be ‘outside the dumbbell’ actually colocalizes with the small terminal lobe of the dumbbell, indicating that the protein is encapsulated within that lobe.

Author response image 2.

Residual protein present inside lumen of dumbbells as visualized by increasing the brightness post-acquisition.

We are not sure what the referee means by “test whether the necks are open, as suggested in the paper”. We are confident that the lobes of dumbbells originated from a single floppy vesicle, and were therefore mutually connected with an open neck (at least at the onset of the experiment). We have performed extensive FRAP assays on dumbbells in previous papers (De Franceschi et al., ACS nano 2022 and De Franceschi et al., Nature Nanotech 2024) which unequivocally proved that these chains of dumbbells are connected with open necks. We now also performed a few FRAP assay with reconstituted Cdv proteins, which confirmed this point. We have added a movie of such an experiment to the manuscript (Movie 1).

Investigating whether the necks are open or closed after Cdv reconstitution is indeed a very relevant question, that could be rephrased as “verify whether Cdv proteins or their combination can induce membrane scission”. This is however beyond the scope of this manuscript, as the current work merely addressed the question of hierarchical recruitment of Cdv proteins at the membrane. We plan to examine this in future work.

(4) Quantification of results from the liposome assay.

The paper would be strengthened by the inclusion of more quantitative data relating to the liposome assay. Firstly, only a single field of view is shown for each condition. Because of this, the reader cannot know whether this is a representative image, or an outlier? Can the authors do some quantification of the data to demonstrate this? The line scan profiles in the supplemental figures would be an example of this, but again in these Figures only a single image is analyzed.

The images that we showed are indeed representative. The dumbbells that are generated by the SMS approach contain an “internal control”: in each dumbbell, the protein has the option of localizing at the neck or localizing elsewhere in the region of flat membrane. We see consistently that Cdv proteins have a strong preference for localizing at the neck.

We would recommend that the authors present quantitative data to show the extent of co-localization at the necks in each case. They also need a metric to report instances in which protein is not seen at the neck, e.g. CdvB2 but not CdvB1 in Fig2I, which rules out a simple curvature preference for CdvB2 as stated in line 182.

While the request for better quantitation is reasonable, this would require carrying out very significant new experiments at the microscope, which is rendered near-impossible since both first authors left the lab on to new positions.

Secondly, the authors state that they see CdvB2∆C recruited to the membrane by CdvB1 (lines 184-187, Fig 2I). However, this simple conclusion is not borne out in the data. Inspecting the CdvB2∆C panels of Fig 2I, Fig3C, and Fig3D, CdvB2∆C signal can be seen at positions which don't colocalize with other proteins. The authors also observe CdvB2∆C localizing to membrane necks by itself (Fig 2E). Therefore, while CdvB1 and CdvB2∆C colocalize in the flotation assay, there is no strong evidence for CdvB2∆C recruitment by CdvB1 in dumbbells. This is further underscored by the observation that in the presented data, all Cdv proteins always appear to localize at dumbbell necks, irrespective of what other components are present inside the liposome. Although one nice control is presented (ZipA), this suggests that more work is required to be sure that the proteins are behaving properly in this assay. For example, if membrane binding surfaces of Cdv proteins are mutated, does this lead to the accumulation of proteins in the bulk of the liposome as expected?

In the particular example of Figure 2I, it indeed appears that there are some clusters of CdvB2ΔC that do not contain CdvB1 (we indicated them in Author response image 3 by red arrowheads), while the yellow arrowheads indicate clusters that contain both proteins. It can be clearly seen that the clusters that do contain both proteins (yellow arrows) are localized at necks, while those that only contain CdvB2ΔC (red arrows) are not localized at necks. This is no coincidence. The clusters indicated by the red arrow do contain CdvB1. However, these clusters rapidly diffuse on the membrane plane because they are not fixed at the neck: therefore, they constantly shift in and out of focus. Because there is a time delay in the acquisition of each channel (between 0.5 and 1 second), these cluster were in focus when the CdvB2ΔC signal was being acquired, but sifted out of focus when the CdvB1 signal was being acquired. This implies that the clusters indicated by the yellow arrowheads are stably localized at necks, which is precisely the point we wished to make with this experiment: because Cdv proteins have an affinity for curved geometry, they preferentially and stably localize at necks. Why don’t all the clusters localize at necks then? We estimate that the simple answer is that, in this particular case, there are more clusters than there are necks, so some of the clusters must necessarily localize somewhere else.

Author response image 3.

Current Figure 2H, where clusters that are double-positive for both CdvB1 and CdvB2ΔC are indicated by yellow arrowheads, while cluster that apparently only contain CdvB2ΔC are indicated by red arrowheads. It is observed that all the double-positive clusters are localized at necks.

(5) Rings.

The authors should comment on why they never observe large Cdv rings in their experiments. In crenarchaeal cell division, CdvA and CdvB have been observed to form large rings in the middle of the 1 micron cell, before constriction. Only in the later stages of division are the ESCRTs localized to the constricting neck, at a time when CdvA is no longer present in the ring. Therefore, if the in vitro assay used by the authors really recapitulated the biology, one would expect to see large CdvAB rings in Figs 1EF. This is ignored in the model. In the proposed model of ring assembly (line 252), CdvAB ring formation is mentioned, but authors do not discuss the fact that they do not observe CdvAB rings - only foci at membrane necks. The discussion section would benefit from the authors commenting on this.

The referee is correct: it is intriguing that we don’t see micron-sized rings for CdvA and CdvB. We do note that our EM data (Fig.S1) show that CdvA in its own can form rings of about 100-200nm diameter, well below the diffraction limit, that could well correspond to the foci that we optically resolve in Figure 1. We now added a brief comment on this to the manuscript on lines 256-264.

(6) Stoichiometry

It is not clear why 100% of the visible CdvA and 100% of the the visible CdvB are shifted to the lipid fraction in 1C. Perhaps this is a matter of quantification. Can the authors comment on the stoichiometry here?

We agree that this was unclear. Since that particular gel was stained by coumassie, the quantitative signals might be unreliable, and hence we have repeated this experiment using fluorescently labelled proteins, which show indeed a less extreme distribution. This was also done to make the data more uniform, as requested by the referees.

(7) Significance of quantification of MBP-tagged filaments.

Authors use tagging and removal of MBP as a convenient, controllable system to trigger polymerisation of various Cdv proteins. However, it is unclear what is the value and significance of reporting the width and length of the short linear filaments that are formed by the MBP-tagged proteins. Presumably they are artefactual assemblies generated by the presence of the tag?

Providing a measure of the changes induced by MBP removal, in fact, validates that this actually has an effect. But perhaps this places too much emphasis on the short filaments. We now opted for a compromise, removing the quantification of the width and length of short filaments formed by MBPtagged protein from the text, but keeping the supplementary figure showing their distribution as compared to the other filaments (Figure S2E, SF).

Similar Figure 2C doesn't seem a useful addition to the paper.

We removed panel 2C, and now merely report these values in the text.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I would suggest the authors perform a deeper discussion about their findings, such as what are the evolutionary implications, how they think lipids from these archaea may affect the recruitment process,...

Because there is no exact homology between Archaea Cdv proteins and Eukaryotic ESCRT-III proteins, we do not feel our work brings new evolutionary implications beyond what we already state in the manuscript. We also dis not perform experiments using Archaea lipids, thus we would rather not speculate on how they may potentially affect the recruitment of Cdv proteins.

In general, the manuscript lacks information regarding some scale bars, number of experimental repetitions (n or N), statistical analysis when needed, information about protein concentrations used in their assays.

We have now added this information in the manuscript.

Below, I provide a list of comments that I think the authors should address to improve the manuscript:

(1) Line 113-114: The authors test protein-membrane interactions using flotation assays with positively curved SUV membranes but encapsulate proteins in dumbbell-shaped liposomes with negative curvature at the connecting necks. Might the use of membranes with opposite curvatures affect the recruitment process? Since the proteins are fluorescently labeled, I suggest testing recruitment using flat giant unilamellar vesicles or supported lipid bilayers (with zero curvature) to validate their findings.

We thank the referee for this suggestion. Please do note that we are not claiming in our paper that Cdv proteins recognize negative curvature. We merely observe that they localize at necks. The neck of a dumbbell exhibits the so-called “catenoid” geometry, which is characterized by having both positive and negative curvature.

Experimentally, on the SUVs, we now realize there was a mistake in the method section: In the flotation assay we in fact used multilamellar vesicles, not SUVs, precisely for the reason mentioned by the referee. We apologize for the oversight and have now corrected this in the methods. Multilamellar vesicles are not characterized by a strong positive curvature as SUVs do, but we do agree that they likely don’t have negative curvature there either. Because of the heterogeneous nature of the multilamellar vesicles, they provide a binding assay that was rather independent of the curvature. Complementary to the flotation assay, the SMS approach was employed to reveal the curvature preference of proteins.

Finally, we performed the experiment on large GUVs suggested by the referee using CdvB as an example, but this turned out to be inconclusive because the protein forms clusters: these clusters may be creating local curvature at the nanometer scale, which cannot be resolved by optical microscopy (Author response image 4). This is quite typical for proteins that recognize curvature (cf. for instance: De Franceschi N, Alqabandi M, Miguet N, Caillat C, Mangenot S, Weissenhorn W, Bassereau P. The ESCRT protein CHMP2B acts as a diffusion barrier on reconstituted membrane necks. J Cell Sci. 2018 Aug 3;132(4):jcs217968.)

Author response image 4.

Fluorescently labelled CdvB bound to giant unilamellar vesicle. The protein was added in the outer buffer. CdvB forms distinct clusters, which may generate a local region of high membrane curvature.

(2) Line 138-139: How is His-ZipA binding the membrane? Wouldn't Ni²⁺-NTA lipids be required? If not, how is the binding achieved?

Indeed, NTA-lipids were present. This is now stated both in the legend and in the methods.

(3) In the encapsulated protein assays, why does the luminal fluorescence intensity of the encapsulated protein sometimes appear similar to the bulk fluorescence signal? Since only a small fraction of the protein assembles at membrane necks, shouldn't the luminal pool of unbound protein show higher fluorescence intensity inside the liposomes?

We thank the referee for raising this point and giving us the opportunity to explain this. The reason is that Cdv proteins have a very high affinity for the neck, and when they cluster at the neck the fluorescence intensity of the cluster is many times higher than the background fluorescence. Because we were interested in imaging the clusters and avoiding overexposing them, we adjusted the imaging conditions accordingly, with the result that the fluorescence from both the lumen and the bulk is at very low level.

By choosing different imaging conditions, however, it can be actually seen that the signal inside the lumen is clearly higher than the bulk: this can be seen for instance in Author response image 2, where the brightness has been properly adjusted.

(4) Line 184-185: In Fig. 2I, some CdvB2ΔC puncta seem independent of CdvB1 and are not localized at membrane necks. How many such puncta exist? For example, in the provided micrograph, 2 out of 5 clusters are independent of CdvB1. This proportion is significant. Could the authors quantify the prevalence of these structures and discuss why they form?

We thank the referee for giving us the opportunity to explain this apparent discrepancy. We’ll like to stress the fact that CdvB2ΔC and CdvB1 form an obligate heterodimer: in all our experiments, without exception, we find that they form a strong complex when we mix the two proteins. This is true both in dumbbells and in flotation assays.

In the particular example of Figure 2I, it indeed appears that there are some clusters of CdvB2ΔC that do not contain CdvB1 (we indicated them in Author response image 3 by red arrowheads), while the yellow arrowheads indicate clusters that contain both proteins. It can be clearly seen that the clusters that do contain both proteins (yellow arrows) are localized at necks, while those that only contain CdvB2ΔC (red arrows) are not localized at necks. This is no coincidence. The clusters indicated by the red arrow do contain CdvB1. However, these clusters rapidly diffuse on the membrane plane because they are not fixed at the neck: therefore, they constantly shift in and out of focus. Because there is a time delay in the acquisition of each channel (between 0.5 and 1 second), these cluster were in focus when the CdvB2ΔC signal was being acquired, but sifted out of focus when the CdvB1 signal was being acquired. This implies that the clusters indicated by the yellow arrowheads are stably localized at necks, which is precisely the point we wished to make with this experiment: because Cdv proteins have affinity for curved geometry, they preferentially and stably localize at necks. Why don’t all the clusters localize at necks then?

(5) Figure 1E and 1F: Why do lipids accumulate and colocalize with the proteins? How can the authors confirm lumen connectivity between vesicles? Performing FRAP assays could validate protein localization and enrichment at the lumen of the membrane necks.

At first sight, indeed some lipid enrichment seems to be observed at the neck between lobes of dumbbells.

This is, however, an imaging artifact due to the fact that the neck is diffraction limited. As shown in the Author response image 5, we are acquiring the membrane signal from both lobes at the neck region, and therefore the signal is roughly double, hence the apparent lipid enrichment.

Author response image 5.

Schematic illustrating that the neck between two lobes is smaller than the diffraction limit of optical microscopy (the size of a typical pixel is indicated by the green square). Because of this technical limitation, the fluorescence intensity of the membrane at the neck is twice that of a single membrane.

The referee is correct in pointing out that these images do not prove that the lobes are connected, and that FRAP assays is the only way to prove this point. However, in previous papers we have confirmed extensively that in chains of dumbbells the lobes are connected:

- De Franceschi N, Pezeshkian W, Fragasso A, Bruininks BMH, Tsai S, Marrink SJ, Dekker C. Synthetic Membrane Shaper for Controlled Liposome Deformation. ACS Nano. 2022 Nov 28;17(2):966–78. doi: 10.1021/acsnano.2c06125.

- De Franceschi N, Barth R, Meindlhumer S, Fragasso A, Dekker C. Dynamin A as a one-component division machinery for synthetic cells. Nat Nanotechnol. 2024 Jan;19(1):70-76. doi: 10.1038/s41565023-01510-3.

Random sticking of liposomes would also generate clusters of vesicles, not linear chains. We now provide also a Movie (Movie 1) supporting this point.

Investigating whether the necks are open or closed after Cdv reconstitution is indeed a very relevant question, that could be rephrased as “verify whether Cdv proteins or their combination can induce membrane scission”. This is however beyond the scope of this manuscript, as the current work merely addressed the question of hierarchical recruitment of Cdv proteins at the membrane. We plan to examine this in future work.

(6) Why didn't the authors use the same lipid composition, particularly the same proportion of negatively charged lipids, on the SUVs of the flotation assays and on the dumbbell-shaped liposomes?

In flotation assays, it is typical to use a relatively large proportion of negatively charged lipids, to promote protein binding. This is because the aim is to maximize membrane coverage by the protein. The SMS procedure to generate dumbbell-shaped GUVs is completely different, however. Rather than covering the membrane with protein, the idea is to reduce the amount of protein to a minimum, so that any curvature preference can be best visualized. This is e.g. routinely done in tube pulling experiments, for the same reason (See for instance Prévost C, Zhao H, Manzi J, Lemichez E, Lappalainen P, Callan-Jones A, Bassereau P. IRSp53 senses negative membrane curvature and phase separates along membrane tubules. Nat Commun. 2015 Oct 15;6:8529. doi: 10.1038/ncomms9529).

(7) Line 117-119: The suggestion that polymer formation between CdvA and CdvB facilitates membrane recruitment is intriguing. However, fluorescence microscopy experiments could better elucidate whether there is sequential recruitment of CdvB followed by CdvA, or if these proteins form a heteropolymer composite for membrane binding. Can CdvB bind membranes independently, or does this require synergy between CdvA and CdvB.

We thank the referee for prompting us to perform this experiment. As we now show in Figure 1C, CdvB indeed is able to bind the membrane independently of CdvA. Whether this happens sequentially or simultaneously is an interesting question, but one that is impossible to address with either the SMS or the flotation assay, because in both cases we can only observe the endpoint of the recruitment.

We would also like to clarify one specific experimental detail. Perhaps unsurprisingly, the results from the flotation assay are dependent on the way the assay is performed. In particular, we observed that the same protein can exhibit a different binding profile depending on whether it is being loaded either at the top or at the bottom of the gradient. This can be seen in Author response image 6. This is counterintuitive, since once the equilibrium is reached, the result should only depend on the density of the sample. We performed an overnight centrifugation (> 16 hours) on a short tube (< 3 cm tall), thus equilibrium is being reached (which is corroborated by the fact that CdvB1 and CdvB2 can float to the top of the gradient within this timespan, as shown in Figure 2C, 2E, 2G). We ascribe the difference between top and bottom loading to the fact that, when the sample is loaded at the bottom, it has to be mixed with a concentrated sucrose solution, while in the case of loading from the top, this is not done.

In literature, both loading from top and from bottom have been used:

- Lata S, Schoehn G, Jain A, Pires R, Piehler J, Gottlinger HG, Weissenhorn W. Helical structures of ESCRTIII are disassembled by VPS4. Science. 2008 Sep 5;321(5894):1354-7. doi: 10.1126/science.1161070

- Moriscot C, Gribaldo S, Jault JM, Krupovic M, Arnaud J, Jamin M, Schoehn G, Forterre P, Weissenhorn W, Renesto P. Crenarchaeal CdvA forms double-helical filaments containing DNA and interacts with ESCRT-III-like CdvB. PLoS One. 2011;6(7):e21921. doi: 10.1371/journal.pone.0021921.

- Senju Y, Lappalainen P, Zhao H. Liposome Co-sedimentation and Co-flotation Assays to Study LipidProtein Interactions. Methods Mol Biol. 2021;2251:195-204. doi: 10.1007/978-1-0716-1142-5_14. In performing the flotation assay for CdvB1 and CdvB2ΔC, or when using all 4 proteins together, we loaded the sample at the bottom, and we could detect reproducible binding to liposomes (Figures 2D, 2F, 2H, 3A). However, CdvB does not bind the membrane when loaded at the bottom. Thus, for the experiments shown in figure 1C, we loaded the proteins at the top. This experimental setup allowed us to highlight that CdvB indeed induce a stronger interaction between CdvA and the membrane.

Author response image 6.

CdvB binding to multilamellar vesicles in a flotation assay. In the left panel, the sample was loaded at the top of the sucrose gradient; in the right panel it was loaded at the bottom.

(8) Line 165-173: The authors claim that filament curvature differs between CdvB2ΔC alone and the CdvB1:CdvB2ΔC complex. Are these differences statistically significant? What is the sample size (N)? Furthermore, how do the authors confirm interactions between these proteins in the absence of membranes based solely on EM micrographs?

We can confirm that the filaments are composed by both proteins, because the filaments have different curvature when both proteins are present. However, as requested by referee 3, point (7), we removed the quantification of curvature from panel 2C. We report the N number in the text.

(9) Line 121-123: Are the authors referring to positive or negative membrane curvatures? The cited literature suggests ESCRT-III proteins either lack curvature preferences (e.g., Snf7, CHMP4B) or prefer high positive curvature (e.g., late ESCRT-III subunits). This is confusing since the authors later test recruitment to negatively curved necks.

We do not claim that Cdv proteins prefer positive or negative curvature, because the necks present in dumbbells have a catenoid geometry, which include both positive and negative curvature. We have now clarified this in the discussion.

(10) Since the conclusions rely on the oligomeric state of the proteins, providing SEC-MALS spectra to show the protein oligomeric state right after the purification would strengthen the claims.

While such SEC-MALDI experiments may be interesting, practical implementation of this is not possible since both first authors left the lab on to new positions.

(11) Line 157-160: Suppl. Fig. 2 shows only a single EM micrograph of a small filament. Could the authors provide lower magnification images showing more filaments?

As requested by Referee 3, point (7), we have toned down the importance of these short filaments.

Also, why are the sample sizes for filament length (N=161) and width (N=129) different?

Protein filaments formed by Cdv tend to stick to each other side by side, so that for some filaments the width could not be accurately assessed, and accordingly those were removed from the analysis.

(12) The introduction states that CdvA binds membranes while CdvB does not. However, the results suggest CdvB facilitates membrane binding, helping CdvA attach. This discrepancy needs further explanation.

We thank the referee for raising this point. We have now performed additional experiments (both SMS assay and flotation assays) showing that indeed CdvB from M. sedula is (unlike CdvB from Sulfolobus) able to bind the membrane on its own (Figure 1C, 1F).

Reviewer #2 (Recommendations for the authors):

Best practice would be to show single fluorescence channels in grayscale or inverted grayscale, retaining pseudocolouring only for the merged multichannel image.

We decided to retain and standardize the colors, both for gels and for microscopy images, in order to have the same color-code for each protein. We believe this improves readability, and this was also a request from Referee 3. Thus, throughout the manuscript, CdvA is in grayscale, CdvB in yellow, CdvB1 in green, CdvB2ΔC in cyan and the membrane in magenta.

It would be great to include a quantification of liposome curvature vs focal intensity of the various Cdv components - across figures.

Quantification of liposome curvature at the neck can be done (De Franceschi et al., Nature Nanotech. 2024). However, in practice, this requires transferring of the sample post-preparation into a new chamber in order to increase the signal-to-noise ratio of the encapsulated dye, a procedure that drastically reduces the yield of dumbbells. The very sizeable amount of work required to obtain reliable measurements, especially considering all the proteins and protein combinations used in this study, indicates that this represents a project in itself, which goes well beyond the scope of this manuscript.

Reviewer #3 (Recommendations for the authors):

(1) We would encourage the authors to consider including the length of the scale bar next to the scale bar in each image and not in the figure description. This would greatly aid in clarity and interpretation of figures.

We have now written the length of the scale bar in the figures.

(2) In a similar vein, could the authors consider labeling panels throughout the manuscript, writing that sample is being presented? This goes mainly for the negative stain and the dumbbell fluorescence images, as having to continuously consult the figure legend again hinders clarity.

We have now labelled the EM images as requested by the referee.

(3) Lines 254-256: would the statement hold not only for CdvB2∆C, but for all imaged proteins? They all seem to localize to membrane necks, presumably favoring membrane binding to a specific membrane topology.

We agree with the referee, and changed the phrasing accordingly.

(4) CdvB2∆C construct - presumably this was a truncation of helix 5 of the ESCRT-III domain? Figure 1A shows that the ESCRT-III domain spans residues 34-170 and therefore implies that all five ESCRT-III helices (which make up the ESCRT-III domain) are present in the C-terminal truncation. Could the authors clarify?

Indeed, the truncation was done at residue 170.

(5) Results of the liposome flotation assays are presented inconsistently across the three figures (Figs 1C, 2DFH, and 3A). This makes it more difficult than it needs to be to interpret and compare results. Could the authors consider presenting the three gels in a more similar, standardized way across the three figures?

To improve readability, we now standardized the colors, both for gels and for microscopy images, in order to have the same color-code for each protein. Thus, throughout the manuscript, CdvA is in grayscale, CdvB in yellow, CdvB1 in green, CdvB2ΔC in cyan and the membrane in magenta.

(6) From the data presented in Fig 1EF, it cannot be concluded whether CdvB and CdvA colocalize, as only one protein is labelled. Is there a technical reason for this?

We have now repeated the same experiment by having both proteins labelled, confirming that there is co-localization at the neck (Figure 1G).

(7) Fig 2C: is the difference between the two samples significant

As requested by Referee 3, we have removed Figure 2C.

(8) Fig 2I is missing a 'merged' panel.

We have now added the merged panel.

(9) The fluorescence intensity plots in Supp Figs 1C and 3C would be easier to interpret if the lipid and protein signal would be plotted on the same plot (say, with normalized fluorescence intensity)

It is not immediately obvious to us what the signal should be normalized to. What we wished to convey with these plots was that the intensity of proteins spikes at the neck region. In an attempt to improve clarity, we have now aligned the plots vertically, and highlighted the position of the neck.

(10) CdvA should have a capital "A" in Figure 3A, panel 3.

We have now corrected this.

(11) The discussion doesn't comment on the need to truncate CdvB2.

This is explained in the result session.

Kilroy Was Here (album)<br /> https://en.wikipedia.org/wiki/Kilroy_Was_Here_(album)

relationship to World War II graffiti tag "Kilroy was here" see also notes on Immerwahr's book on Empire

a while

reply to u/KingCollectA at https://reddit.com/r/typewriters/comments/1rpr1ha/got_quite_lucky_finding_a_free_olympia_sg1_had_to/

Typically the SG1 has at least 3 serial numbers. Two matching ones on the main body (one hiding deep inside), and the third on the bottom portion of the carriage, which may or may not match the other two. (The carriages were meant to be easily swappable for machines with the same CPI/escapement sizes.) Removing the carriage will usually reveal the body serial number (typically a 7-XXXXXXXXX) format which you can compare with the grid of serial number ranges to see where yours fits in at https://typewriterdatabase.com/olympia.61.typewriter-serial-number-database.

I just got mine and have finished most of its servicing, though one or two small adjustments remain for it to be where I want it to be. Beyond this, it's been spectacular. See also: https://boffosocko.com/tag/Olympia-sg1/

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

The authors have adequately responded to all comments.

We thank Reviewer 1 for their positive assessment of our previous round of revisions.

Reviewer #2 (Public review):

Summary:

The authors combine a clever use of historical clinical data on infection duration in immunologically naive individuals and queuing theory to infer the force of infection (FOI) from measured multiplicity of infection (MOI) in a sparsely sampled setting. They conduct extensive simulations using agent based modeling to recapitulate realistic population dynamics and successfully apply their method to recover FOI from measured MOI. They then go on to apply their method to real world data from Ghana before and after an indoor residual spraying campaign.

Strengths:

- The use of historical clinical data is very clever in this context

- The simulations are very sophisticated with respect to trying to capture realistic population dynamics

- The mathematical approach is simple and elegant, and thus easy to understand

Weakness:

The assumptions of the approach are quite strong, and the authors have made clear that applicability is constrained to individuals with immune profiles that are similar to malaria naive patients with neurosyphilis. While the historical clinical data is a unique resource and likely directionally correct, it remains somewhat dubious to use the exact estimated values as inputs to other models without extensive sensitivity analysis.

We thank reviewer 2 for their comments on our previous round of revisions. The statement here that “it remains somewhat dubious to use the exact estimated values as inputs to other models” suggests that we may not have been sufficiently clear on how infection duration is represented in our agent-based model (ABM) of malaria population dynamics. Because our analysis uses simulated outputs from the ABM to validate the performance of the two queuing-theory methods, we believe this point warrants clarification, which we provide below.

When simulating with the ABM, we do not use empirical estimates of infection duration in immunologically naïve individuals from the historical clinical data as direct inputs. Instead, infection duration emerges from the within-host dynamics modeled in the ABM (lines 800-816, second paragraph of the subsection Within-host dynamics in Appendix 1-Simulation data of the previous revision). Briefly, each Plasmodium falciparum parasite carries approximately 50-60 var genes, each encoding a distinct variant surface antigen expressed during the blood stage of infection. Empirical evidence[1,2] indicates that these var genes are expressed largely sequentially. If a host has previously encountered the antigenic product of a given var gene and retains immunity to it, subject to waning at empirically estimated rates[3,4], the corresponding parasite subpopulation is rapidly cleared. Conversely, if the host is naïve to that gene, it takes approximately seven days for the immune system to mount an effective antibody response, resulting in a rapid decline or elimination of the expressed variant[5]. This seven-day timescale aligns with the duration of each successive parasitemia peak observed in Plasmodium falciparum infections[6,7], each arising primarily from the expression of a single var gene and occasionally from a small number of var genes.

In our previous analyses, we therefore modeled an average expression duration of seven days per gene in naïve hosts. Specifically, the switching time to the next gene was drawn from an exponential distribution with a mean of seven days. Each var gene is represented as a linear combination of two epitopes (alleles), based on the empirical characterization of two hypervariable regions in the var tag region[8], and immunity is acquired against these alleles. Immunity to one allele of a given gene reduces its average expression duration by approximately half, whereas immunity to both alleles results in an immediate switch to another var gene within the infection. Consequently, the total duration of infection is proportional to the number of unseen alleles by the host across all var genes expressed during that infection (lines 800-816, second paragraph of the subsection Within-host dynamics in Appendix 1-Simulation data of the previous revision).

Prompted by the reviewer’s comments, in this revision we additionally tested mean expression durations of 7.5 and 8 days per var gene, together with an extension of the within-host rules. These values were applied in combination with the extended within-host rules (see the next paragraph for motivation and details). Although differences among the three mean expression durations are modest at the per-gene level, when aggregated across all var genes expressed within an individual parasite, the resulting total infection duration can differ by on the order of several months. The resulting distributions of infection duration across immunologically naïve individuals and those aged 1-5 years, together with those generated under our previous simulation settings, span a range of means and variances that lies above and below, but encompasses, scenarios comparable to the historical clinical data from naïve neurosyphilis patients treated with P. falciparum malaria. We have provided example supplementary figures illustrating that the distributions of infection duration from the simulated outputs overlap with, and closely resemble, the empirical distribution from the historical clinical data (Appendix 1-Figure 27-32).

We considered the following modification of the within-host rules. In our previous ABM simulations, we had assumed that an infection would clear only once the parasite had exhausted its entire var gene repertoire, that is, after every var gene had been expressed and recognized. However, biological evidence indicates that clearance can occur earlier for several reasons, including stochastic extinction before full repertoire exhaustion. Even if some var genes remain unexpressed, an infection can terminate due to demographic stochasticity once parasite densities fall to very low levels. This decline in parasite densities may result from non-variant-specific immune mechanisms or from cross-immunity among var genes that share sequence similarity or alleles[9,10,11], both of which can substantially reduce parasite numbers. To model the possibility of termination or clearance before full repertoire exhaustion, we implemented a simple scenario in which there is a small probability of clearing the current infection while a given var gene-whether non-final or final-is being expressed. This probability is a function of the host’s pre-existing immunity to the two epitopes (alleles) of that gene, thereby capturing in a parsimonious manner the effects of cross-immunity among sequence- or allele-sharing var genes in reducing parasitemia. Specifically, it is modeled as a Bernoulli draw whose success probability equals the immunity level against the gene (0 for no immunity to either epitope, 0.5 for immunity to one epitope, and 1 for immunity to both epitopes) multiplied by a constant factor of 0.025. Thus, the probability scales with pre-existing variant-specific immunity to the gene but remains small overall, while introducing additional variance into the emergent distribution of total infection duration across hosts.

We acknowledge that the ABM used to simulate malaria population dynamics cannot capture all mechanisms and complexities underlying within-host processes, many of which remain poorly understood. However, we emphasize that the resulting distributions of infection duration generated by the ABM span a broad range of means, variances, and shapes, including distributions that closely match those observed in the clinical historical data. Because the queueing-theory methods rely on only the mean and variance of infection duration to estimate the force of infection (FOI), these scenarios, which collectively span and encompass values comparable to the empirical ones, provide an appropriate basis for evaluating the performance of the methods using simulated outputs. We have added supplementary figures (see Appendix 1-Figure 16-22) illustrating the corresponding FOI inference results when we allow for clearance before the complete expression of the var repertoire, and the accuracy of FOI estimation remains comparable across all the scenarios examined.

Finally, we emphasize that the application of the queuing-theory methods to the simulated outputs and to the Ghana field survey data involve two self-contained steps. For the simulations, FOI is inferred directly from the emergent distributions of infection duration generated by the ABM. For the Ghana surveys, FOI is inferred using the historical clinical data, which remains one of the few credible and widely used empirical sources for infection duration in immunologically naïve individuals[6]. By exploring different mean expression durations and within-host rules in the ABM, which generates distributions of infection duration that span and encompass those comparable to the empirical distribution, we demonstrate that the queueing-theory methods perform comparably across diverse scenarios and are well suited for application to the Ghana field surveys.

We expanded the section on within-host dynamics in Appendix 1 to elaborate on this point (Lines 817-854).

Reviewer #3 (Public review):

I think the authors gave a robust but thorough response to our reviews and made some important changes to the manuscript which certainly clarify things for me.

We thank Reviewer 3 for their positive feedback on our previous round of revisions.

References

(1) Zhang, X. & Deitsch, K. W. The mystery of persistent, asymptomatic Plasmodium falciparum infections. Curr. Opin. Microbiol 70, 102231 (2022).

(2) Deitsch, K. W. & Dzikowski, R. Variant gene expression and antigenic variation by malaria parasites. Annu. Rev. Microbiol. 71, 625–641 (2017).

(3) Collins, W. E., Skinner, J. C. & Jeffery, G. M. Studies on the persistence of malarial antibody response. American journal of epidemiology, 87(3), 592–598 (1968).

(4) Collins, W. E., Jeffery, G. M. & Skinner, J. C. Fluorescent Antibody Studies in Human Malaria. II. Development and Persistence of Antibodies to Plasmodium falciparum. The American journal of tropical medicine and hygiene, 13, 256–260 (1964).

(5) Gatton, M. L., & Cheng, Q. Investigating antigenic variation and other parasite-host interactions in Plasmodium falciparum infections in naïve hosts. Parasitology, 128(Pt 4), 367–376 (2004).

(6) Maire, N., Smith, T., Ross, A., Owusu-Agyei, S., Dietz, K., & Molineaux, L. A model for natural immunity to asexual blood stages of Plasmodium falciparum malaria in endemic areas. The American journal of tropical medicine and hygiene, 75(2 Suppl), 19–31 (2006).

(7) Chen D. S., Barry A. E., Leliwa-Sytek A., Smith T-A., Peterson I., Brown S. M., et al. A Molecular Epidemiological Study of var Gene Diversity to Characterize the Reservoir of Plasmodium falciparum in Humans in Africa. PLoS ONE 6(2): e16629 (2011).

(8) Larremore D. B., Clauset A., & Buckee C. O. A Network Approach to Analyzing Highly Recombinant Malaria Parasite Genes. PLoS Comput Biol 9(10): e1003268 (2013).

(9) Holding T. & Recker M. Maintenance of phenotypic diversity within a set of virulence encoding genes of the malaria parasite Plasmodium falciparum. J. R. Soc. Interface.1220150848 (2015).

(10) Crompton, P. D., Moebius, J., Portugal, S., Waisberg, M., Hart, G., Garver, L. S., Miller, L. H., Barillas-Mury, C., & Pierce, S. K. Malaria immunity in man and mosquito: insights into unsolved mysteries of a deadly infectious disease. Annual review of immunology, 32, 157–187 (2014).

(11) Langhorne, J., Ndungu, F., Sponaas, AM. et al. Immunity to malaria: more questions than answers. Nat Immunol 9, 725–732 (2008).

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work, Huang et al. revealed the complex regulatory functions and transcription network of 172 unknown transcriptional factors (TFs) in Pseudomonas aeruginosa PAO1. They have built a global TF-DNA binding landscape and elucidated binding preferences and functional roles of these TFs. More specifically, the authors established a hierarchical regulatory network and identified ternary regulatory motifs, and co-association modules. Since P. aeruginosa is a well known pathogen, the authors thus identified key TFs associated with virulence pathways (e.g., quorum sensing [QS], motility, biofilm formation), which could be potential drug targets for future development. The authors also explored the TF conservation and functional evolution through pan-genome and phylogenetic analyses. For the easy searching by other researchers, the authors developed a publicly accessible database (PATF_Net) integrating ChIP-seq and HT-SELEX data.

Strengths:

(1) The authors performed ChIP-seq analysis of 172 TFs (nearly half of the 373 predicted TFs in P. aeruginosa) and identified 81,009 significant binding peaks, representing one of the largest TF-DNA interaction studies in the field. Also, The integration of HT-SELEX, pan-genome, and phylogenetic analyses provided multi-dimensional insights into TF conservation and function.

(2) The authors provided informative analytical Framework for presenting the TFs, where a hierarchical network model based on the "hierarchy index (h)" classified TFs into top, middle, and bottom levels. They identified 13 ternary regulatory motifs and co-association clusters, which deepened our understanding of complex regulatory interactions.

(3) The PATF_Net database provides TF-target network visualization and data-sharing capabilities, offering practical utility for researchers especially for the P. aeruginosa field.

Thank you for your positive feedback!

Weaknesses:

(1) There is very limited experimental validation for this study. Although 24 virulence-related master regulators (e.g., PA0815 regulating motility, biofilm, and QS) were identified, functional validation (e.g., gene knockout or phenotypic assays) is lacking, leaving some conclusions reliant on bioinformatic predictions. Another approach for validation is checking the mutations of these TFs from clinical strains of P. aeruginosa, where chronically adapted isolates often gain mutations in virulence regulators.

Thank you for this valuable suggestion. We have performed the EMSA experiment to validate the binding result and also constructed the mutants for further functional validation. The details can be found in Figure S5.

(2) ChIP-seq in bacteria may suffer from low-abundance TF signals and off-target effects. The functional implications of non-promoter binding peaks (e.g., coding regions) were not discussed.

Thank you for this insightful comment regarding ChIP-seq data quality and non-promoter binding events. While we acknowledge that completely eliminating all non-specific binding signals is technically challenging in bacterial ChIP-seq experiments, we implemented stringent quality control measures including replicates, negative controls, and FDR cutoffs to minimize false positives.

Although the coding binding peaks represent a smaller fraction of total binding events, they are functionally significant rather than mere technical artifacts. Our previous work systematically demonstrated that bacterial TFs can bind to coding sequences and regulate gene expression through multiple mechanisms, including modulating cryptic promoter activity and antisense RNA transcription, hindering transcriptional elongation, and influencing translational efficiency[1]. We have now expanded the Discussion section to address these regulatory mechanisms.

(3) PATF_Net currently supports basic queries but lacks advanced tools (e.g., dynamic network modeling or cross-species comparisons). User experience and accessibility remain underevaluated. But this could be improved in the future.

Thank you for this constructive feedback on PATF_Net. We acknowledge that more advanced features would further enhance the platform’s utility. To enhance the utility of PA_TFNet, we have implemented two new features: (1) a virulence pathway browser that allows users to explore TF binding across curated gene sets for key virulence pathways (quorum sensing, secretion systems, biofilm, motility, etc.), and (2) a target gene search function that enables rapid identification of all TFs regulating any gene of interest by locus tag query.

Achievement of Aims and Support for Conclusions

(1) The authors successfully mapped global P. aeruginosa TF binding sites, constructed hierarchical networks and co-association modules, and identified virulence-related TFs, fulfilling the primary objectives. The database and pan-genome analysis provide foundational resources for future studies.

(2) The hierarchical model aligns with known virulence mechanisms (e.g., LasR and ExsA at the bottom level directly regulating virulence genes). Co-association findings (e.g., PA2417 and PA2718 co-regulating pqsH) resonate with prior studies, though experimental confirmation of synergy is needed.

Thank you for your positive feedback! We have added experimental validation in the Results section.

Impact on the Field and Utility of Data/Methods

(1) This study fills critical gaps in TF functional annotation in P. aeruginosa, offering new insights into pathogenicity mechanisms (e.g., antibiotic resistance, host adaptation). The hierarchical and co-association frameworks are transferable to other pathogens, advancing comparative studies of bacterial regulatory networks.

(2) PATF_Net enables rapid exploration of TF-target interactions, accelerating candidate regulator discovery.

Thank you for your positive feedback!

Reviewer #3 (Public review):

Summary:

The authors utilized ChIP-seq on strains containing tagged transcription factor (TF)-overexpression plasmids to identify binding sites for 172 transcription factors in P. aeruginosa. High-quality binding site data provides a rich resource for understanding regulation in this critical pathogen. These TFs were selected to fill gaps in prior studies measuring TF binding sites in P. aeruginosa. The authors further perform a structured analysis of the resulting transcriptional regulatory network, focusing on regulators of virulence and metabolism, in addition to performing a pangenomic analysis of the TFs. The resulting dataset has been made available through an online database. While the implemented approach to determining functional TF binding sites has limitations, the resulting dataset still has substantial value to P. aeruginosa research.

Strengths:

The generated TF binding site database fills an important gap in regulatory data in the key pathogen P. aeruginosa. Key analyses of this dataset presented include an analysis of TF interactions and regulators of virulence and metabolism, which should provide important context for future studies into these processes. The online database containing this data is well organized and easy to access. As a data resource, this work should be of significant value to the infectious disease community.

Thank you for your positive feedback!

Weaknesses:

Drawbacks of the study include 1) challenges interpreting binding site data obtained from TF overexpression due to unknown activity state of the TFs on the measured conditions, 2) limited practical value of the presented TRN topological analysis, and 3) lack of independent experimental validation of the proposed master regulators of virulence and metabolism.

We thank the reviewer for summarizing these key concerns. We acknowledge the limitations raised regarding TF overexpression, TRN topological analysis interpretation, and experimental validation. We provide detailed point-by-point responses to each of these concerns in our replies to the specific comments below, where we explain our rationale, the measures taken to address these limitations, and our plans for improvement.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Future Directions for the authors to consider for next steps:

(1) Key TFs (e.g., PA1380, PA5428) should be validated via gene knock out experiments, fluorescent reporter assays, or animal models to confirm roles in virulence pathways.

Thank you for this important suggestion. We agree that experimental validation is essential to confirm their regulatory roles and biological functions.

Firstly, we selected a subset of key TFs, including PA0167, PA1380, PA0815, and PA3094, and performed Electrophoretic Mobility Shift Assays (EMSA) experiments to validate their direct binding to target promoters. These results confirmed the ChIP-seq-identified interactions and are now included as Figure S5A-F.

We also constructed a clean deletion mutant of PA1380 and PA 3094 (ΔPA1380 and ΔPA3094) and their complementary strains (ΔPA1380/p and ΔPA3094/p). We then performed RT-qPCR analysis to validate their regulatory effects on key target genes. We found that PA1380 positively regulate the expression of cupB1 and cupB3 genes (Figure S5F). While the CupB cluster was known not be as important as CupA cluster in the biofilm information, so we did not find significant difference in biofilm formation between WT and ΔPA1380. Additionally, we found TF PA3094 also positively regulate lecA expression, which were shown in Figure S5G.

We agree that comprehensive functional validation, including animal model studies, would further strengthen the biological significance of these findings. Such experiments are currently underway in our laboratory and will be the subject of follow-up studies.

We have revised the Results section and Method section to include these validation experiments and their implications. Please see Figure S5 and Lines 283-300.

“To experimentally validate the regulatory interactions identified by ChIP-seq, we performed biochemical and genetic analyses on selected TFs. First, we conducted Electrophoretic Mobility Shift Assays (EMSA) for four TFs, including PA0167, PA0815, PA1380, and PA3094, using DNA fragments containing their predicted binding sites from target gene promoters. These TFs showed specific binding to their cognate DNA sequences (Figure S5A-D), confirming the direct binding of the ChIP-seq-identified interactions.

To further validate the functional regulatory roles of these TFs, we constructed clean deletion mutants of PA1380 and PA3094 (ΔPA1380 and ΔPA3094) along with their complemented strains (ΔPA1380/p and ΔPA3094/p). RT-qPCR analysis revealed that PA1380 positively regulates the expression of cupB1 and cupB3 (Figure S5E), two genes within the CupB fimbrial cluster identified as ChIP-seq targets. Similarly, PA3094 was confirmed to positively regulate lecA expression (Figure S5F), which encodes a lectin involved in biofilm formation and host interactions[2]. Expression of these target genes was restored to wild-type (WT) levels in the complemented strains, validating the regulatory relationships predicted by ChIP-seq. These combined biochemical and genetic validations demonstrate the accuracy and biological relevance of our TF binding data.”

(2) Non-promoter binding events (e.g., coding regions) may regulate RNA stability, warranting integration with translatomics or epigenomics data.

Thank you for this suggestion. We have now expanded the Discussion section to address this comment. Please see Lines 478-482.

“Our analysis revealed that TF binding events occur within coding regions, which is consistent with our previous study demonstrating that bacterial TFs possess binding capabilities for coding regions and can regulate transcription through multiple mechanisms [1]. Besides, it may also regulate RNA stability, warranting integration with translatomics or epigenomics data.”

(3) Incorporate strain-specific TF data (e.g., clinical isolates) and dynamic visualization tools to broaden PATF_Net's applicability.

Thank you for this constructive suggestion. To enhance the utility of PA_TFNet, we have implemented two new features: (1) a virulence pathway browser that allows users to explore TF binding across curated gene sets for key virulence pathways (quorum sensing, secretion systems, biofilm, motility, etc.), and (2) a target gene search function that enables rapid identification of all TFs regulating any gene of interest by locus tag query. These features are now live on the database and described in the revised manuscript.

Regarding strain-specific TF data, we agree this would be valuable for understanding regulatory diversity in clinical isolates. However, such an expansion would require ChIP-seq profiling across multiple strains. The current dataset is based on the reference strain PAO1, which serves as the foundation for most P. aeruginosa research and allows direct comparison with existing genomic and functional studies. We have added a statement in the revised manuscript acknowledging this limitation and highlighting strain-specific TF analysis as an important future direction for the field. Please see Lines 372-390.

“The database offers multiple search modalities to facilitate data exploration: users can perform TF-centric searches to query binding sites, target genes, and regulatory networks for individual TFs, or utilize the target gene search function to identify all TFs that regulate any gene of interest by entering its locus tag. To connect regulatory data with biological function, we have implemented a virulence pathway browser that allows users to explore TF binding patterns across curated gene sets for major P. aeruginosa virulence pathways. Interactive visualization tools, including network graphs and binding profile plots, facilitate intuitive exploration of regulatory relationships. The primary purpose of PATF_Net is to store, search, and mine valuable information on P. aeruginosa TFs for researchers investigating P. aeruginosa infection. The current resource is based on the reference strain PAO1, which serves as the foundation for most P. aeruginosa molecular studies and allows direct integration with existing genomic annotations and functional data. However, P. aeruginosa exhibits substantial genomic diversity across clinical isolates, and strain-specific differences in TF binding patterns may contribute to phenotypic variation in virulence, antibiotic resistance, and host adaptation. Extension of this resource to include strain-specific regulatory maps from diverse clinical isolates would provide valuable insights into the regulatory basis and represents an important direction for future investigation.”

(4) Phylogenetic analysis highlights TF conservation in bacteria; future work could explore functional homology in other Gram-negative pathogens (e.g., E. coli).

Thank for this insightful suggestion. Our phylogenetic analysis revealed that P. aeruginosa TFs exhibit varying degrees of conservation across bacterial species, with some showing broad distribution across Gram-negative pathogens while others are lineage-specific.

We agree that exploring functional homology of orthologous TFs across species would be highly valuable. Such comparative studies could address whether conserved TFs regulate similar target genes and biological processes across species, or whether regulatory networks have been rewired during evolution. For example, comparative ChIP-seq analysis of P. aeruginosa TFs and their orthologs in Klebsiella pneumoniae or even Gram-positive pathogen like Bacillus cereus could reveal conserved regulatory modules governing universal virulence or metabolic strategies versus species-specific adaptations. This represents an important direction for future investigation and would be facilitated by the comprehensive TF binding dataset we provide here. We have expanded the Discussion section to highlight this future direction. Please see Lines 539-550.

“While our phylogenetic analysis reveals varying degrees of TF conservation across bacterial species, the functional implications of this conservation remain to be fully explored. Many P. aeruginosa TFs have clear orthologs in both Gram-negative (e.g., Klebsiella pneumoniae) and Gram-positive pathogens (e.g., Bacillus cereus), yet whether these orthologs regulate similar target genes and biological processes is largely unknown. Future comparative ChIP-seq profiling of orthologous TFs could reveal the extent to which regulatory network architecture is conserved versus rewired during bacterial evolution, potentially identifying core regulatory modules governing universal bacterial strategies versus species-specific innovations. Such cross-species comparisons would enhance our understanding of regulatory network evolution and enable functional prediction in less well-characterized pathogens based on homology to experimentally validated P. aeruginosa regulators.”

Reviewer #3 (Recommendations for the authors):

Major comments

- Limitations of the ChIP-seq approach: With overexpression plasmids as an approach to TRN elucidation, there are always a set of concerns. First, TF expression is not enough to ensure regulatory activity - metabolite effects must be such that the TF is active which requires growing the cells in activating conditions. Second, the presence of a binding event does not mean that the binding has a regulatory effect - the authors are clearly aware of this as they specify binding sites in promoter regions, which should be helpful, but they also mention the possibility of regulatory binding events in coding regions. These issues should be listed as weaknesses of the approach in the Discussion.

Thank you for these important suggestions. We agree that these limitations should be explicitly discussed. We have now added a dedicated paragraph in the Discussion section addressing these concerns. Please see Lines 492-501.

“However, several limitations of the ChIP-seq approach should be acknowledged. Firstly, TF overexpression ensures sufficient protein levels for ChIP-seq signal detection but does not guarantee that all TFs are in their active conformational states, as many bacterial TFs require allosteric activation by metabolites, cofactors, or post-translational modifications. The cells under standard laboratory conditions which may not activate all TFs to their maximal regulatory states, potentially leading to underestimation of condition-specific binding peaks. Secondly, while we observed TF binding at thousands of genomic sites, binding per se does not equate to functional regulation, as chromatin context, cofactor availability, and competitive binding all influence regulatory outcomes.”

- Lack of independent validation: The study seems to lack substantial independent validation of either the functional nature of the binding sites as well as the proposed physiological regulatory role of the TFs. For example, for the 103 identified TF motifs, do any of these agree with existing motifs in motif databases that may be homologous to P. aeruginosa TFs? The authors claim to have discovered master regulators of virulence and associated core regulatory clusters - but there does not seem to be any independent validation of the proposed associations. The authors selected the TF targets to cover TFs that had not yet been characterized; however, it would have been nice to have some overlap with previous studies so that consistency and data quality could be assessed.

Thank you for raising these critical points about validation.

As for motif validation, we compared the existing motifs in the RegPrecise database[3] and we found that the motif of PA3587 show significant similarity to homologous TFs in Pseudomonadaceae. We have added the related description in the Results section. Please see Figure S3B and Lines 228-231.

As for the validation of master regulators, we have performed EMSA experiments for validating the binding events and constructed the mutants for function validation. We have added the related contents in Results section. Please see Figure S5 and Lines 283-300.

We have discussed the overlap between our results and previous studies in the Discussion section. Please see Lines 530-538.

“PA0797 is known to regulate the pqs system and pyocyanin production[4]. In the present study, it was also found to bind to the pqsH promoter region and its motif was visualised. PA5428 was found to bind to the promoter regions of aceA and glcB genes[5], which was also demonstrated in our ChIP-seq results. PA4381 (CloR) was found to be associated with polymyxin resistance in a previous study[6] and to be possibly related to ROS resistance in the present study. Furthermore, PA5032 plays a putative role in biofilm regulation and also forms an operon with PA5033, an HP associated with biofilm formation[7].”

- Uncertain value of TRN topology analysis: The relationship between ternary motifs and pathogenicity of P. aeruginosa, and why the authors argue these results motivated TF-targeting drugs (the topic of the last paragraph of the Discussion), are unclear to me. The authors allude to possible connections between pathogenicity, growth, and drug resistance, but I don't see concrete examples here of related TF interactions that clearly represent these relationships. The sections "Hierarchical networks of TFs based on pairwise interactions" and "Ternary regulatory motifs show flexible relationships among TFs in P. aeruginosa" seem to not say much in terms of results that are actionable or possible to validate. A topological graph is constructed based on observed TF-TF connections in measured binding sites - however, it's unclear if any of these connections are physiologically meaningful. Line 178 - Why would there be any connection between the structural family of TF and its location in the proposed TRN hierarchy?

Thank you for this valuable comment on TRN topology analysis. It is hard to quantify precisely how much this resource will accelerate P. aeruginosa research or drug development, but we believe providing this foundational network architecture has inherent value for the community, which is valued for enabling hypothesis generation even before comprehensive functional validation. We would like to clarify our perspective on these findings and have added the discussion in the revised manuscript to better describe their nature and value. Please see Lines 517-528.

“Additionally, although the TRN analysis revealed organizational patterns in P. aeruginosa regulatory network, the functional significance these topological features, including their specific contributions to pathogenicity, metabolic adaptation, and antibiotic resistance remains to be experimentally determined in the future work. The hierarchical structure and regulatory motifs we identified represent objective network properties derived from our binding data, but translating these structural observations into mechanistic understanding will require condition-specific functional studies, genetic validation, and phenotypic characterization. Our analysis provided a systematic framework and generating testable hypotheses rather than definitive functional conclusions. Nevertheless, these network-level organizational principles provided value to the community as a foundational reference, similar to other regulatory network maps[8] that were useful even before comprehensive validation.”

- Identification of "master" regulators: Line 527 on virulence regulators: "We first generated gene lists associated with nine pathways" - is this not somewhat circular, i.e. using gene lists generated from (I assume) co-regulated gene sets to identify regulators of those gene lists? I can't tell from the cited reference (80), which is their own prior review article, what the original source of these gene lists was. Somewhat related to this point - Line 32: 24 "master regulators" - if there are that many, is it still considered a master regulator? Line 270: This term "master regulator" would seem to require some quantitative justification. Identifying 24 (a large number of) "master" regulators of virulence would seem to dilute the implied power of the term.

We apologize for the lack of clarity regarding the virulence pathway gene lists, and we have provided complete gene lists for virulence-related pathways, which were compiled from functional annotations, in our online PA_TFNet database.

Additionally, we appreciate your concern about the use of “master” regulator. The usage is based on previous studies[9,10], and the master regulator is commonly known in the development of multicellular organisms as a subset of TFs that control the expression of multiple downstream genes and govern lineage commitment or key biological processes. We employed the term "master regulator" in an analogous manner to specify a class of functionally crucial TFs that participate in a pathway or biological event by regulating multiple downstream genes statistically enriched in that pathway. In line with this definition, we identified TFs whose targets were significantly enriched in genes associated with specific virulence pathways (hypergeometric test, P < 0.05).

We understand the concern that identifying 24 master regulators might seem to dilute the term. However, we would like to clarify that each of these 24 TFs is a "master regulator" with respect to specific virulence pathways based on statistical criteria, not necessarily a global master regulator of multiple pathways of P. aeruginosa. We have revised the Method section. Please see Lines 604-612.

- Line 234: "Genome-wide synergistic co-association of TFs in P. aeruginosa." This section was an interesting analysis. As I mention above, the weakness of an overexpression approach is not knowing whether the TF is active on the examined conditions. By looking at shared binding peaks across overexpression of different TFs, it should indeed be possible to glean some regulatory connections across TFs. Furthermore, the authors discuss specific examples that appear physiologically reasonable, which is appreciated.

We thank the reviewer for this positive assessment of our co-association analysis. We agree with the limitation of the overexpression approach, which have been discussed in the Discussion section. We are pleased that the reviewer found the approach and specific examples valuable.

Minor comments

- Line 35 - "high-throughput systematic evolution of ligands by exponential enrichment" - no idea what this means. Is this related to the web-based database, or why is it mentioned in the same sentence?

We apologize for the unclear presentation. To clarify: “High-throughput systematic evolution of ligands by exponential enrichment” (HT-SELEX) is an in vitro technique for determining TF DNA-binding motifs, which our group previously applied to a subset of P. aeruginosa TFs in a prior publication[11]. In the current study, we performed ChIP-seq for 172 TFs, which represent the majority of TFs not covered by the previous HT-SELEX study. Together, these two complementary approaches (HT-SELEX for in vitro binding motifs, ChIP-seq for in vivo genomic binding sites) provide near-complete coverage of the P. aeruginosa TF repertoire. Both datasets are integrated into our PA_TFNet database.

Due to space constraints in the abstract, we could not provide detailed explanation of HT-SELEX, but we have now improved the clarity in the Introduction to better explain the relationship between our previous HT-SELEX work and the current ChIP-seq study, and why both are mentioned together in the context of the database. Please see Lines 99-105.

- Line 193 - Only 9 auto-regulating TFs seems like a low number, given the frequency of negative auto-regulation in other organisms like E. coli. Could the authors comment on their expectations based on well-curated TRNs?

Thank you for this comment. We agree that 9 auto-regulating TFs is lower than might be expected based on E. coli, where auto-regulation is more prevalent. This likely reflects technical limitations of ChIP-seq approach that our detection was limited to standard growth conditions rather than the diverse physiological states where auto-regulation often occurs. Therefore, the 9 TFs we report represent a high-confidence subset, and the true frequency of auto-regulation in P. aeruginosa likely is higher. We added the content in the revised manuscript. Please see Lines 193-196.

“This number likely represents a conservative estimate, as experiments may not optimally capture auto-regulatory events that depend on native expression levels or specific physiological conditions.”

- Line 230 - "This conservation suggests that TFs within the same cluster co-regulate similar sets of genes." - Why would clustering of TF binding site motifs need to be done to make this assessment? Couldn't the shared set of regulated genes be identified directly from the binding site data? Computing TF binding site motifs has obvious value, but I am struggling to understand the point of clustering the motifs. Is there some implied evolutionary or physiological connection here? No specific physiological roles or hypotheses are discussed in this section.

Thank you for this important question. We agree that shared target genes can be identified directly from ChIP-seq binding data, which we also analyzed (co-association analysis). The motif clustering analysis serves a complementary and distinct purpose that provides information not directly obtainable from overlapped targets alone. Specifically, target overlap is inherently condition dependent, and motif clustering captures this intrinsic binding specificity, which reflects the structural similarity of DBDs, evolutionary relationships, and potential for functional redundancy or cooperativity under specific conditions. We have revised the related content in the manuscript, and please see Lines 236-242.

“Clustering of TF binding motifs identified groups of TFs with similar intrinsic DNA-binding specificities. As expected, many clusters contained TFs from the same DBD families, reflecting evolutionary conservation and potential functional redundancy or competitive binding at shared regulatory elements. Notably, the clustering also uncovered associations between TFs from different DBD families, suggesting convergent evolution of binding specificity or novel regulatory interactions that warrant further investigation.”

- Line 284 - should "metabolomic" be "metabolic"? I didn't see metabolomic data

Yes, we have revised. Please see Line 311.

- Several of the figures are too small (e.g. Fig S4A) or complex (Fig 2A) to see clearly or glean information from.

Thank you for this comment. We acknowledge that Figure 2A and Figure S4A contain dense information due to the comprehensive nature of the regulatory network and the large number of TFs analyzed. We believe these overview figures serve an important purpose in conveying the scale and organization of the regulatory network, while the tables (Table S6 for Fig. S4A and Table S3 for Fig. 2A) provide the granular data needed for specific inquiries. We have also made the figures available in higher resolution and increased font sizes where possible without compromising the overall layout.

- I don't understand the organization of the "Ternary regulatory motifs" in Supplementary Data File 4 - A table of contents explaining the tabs and columns would be welcome (for this as well as other supplementary files, some of which are more straightforward than others).

Thank you for this suggestion. We have now revised all supplementary data files to include header and necessary annotations in the first row. Specifically for Supplementary Data File 4, the three columns (Top, Middle, Bottom) represent the left, middle, and right node, respectively, in each ternary regulatory motif.

- I would have expected genomic locations of TF binding sites would have been one of the Supplementary Tables, to increase the accessibility of the data. However, the data is made available through their website, https://jiadhuang0417.shinyapps.io/PATF_Net/, which was easy to access and download the full dataset, so this is a minor issue.

Thank for accessing our PA_TFNet database and for the positive feedback on data accessibility. We agree that providing genomic locations of TF binding sites is crucial. These data are fully available and downloadable through the web interface, which allows flexible searching, filtering, and batch download of binding sites. We felt that the interactive and database format provides more functionality than static supplementary tables (e.g., dynamic filtering by TF, genomic region, or binding strength), given the large scale of this dataset.

References

(1) Hua, C., Huang, J., Wang, T., Sun, Y., Liu, J., Huang, L. et al. Bacterial Transcription Factors Bind to Coding Regions and Regulate Internal Cryptic Promoters. Mbio 13, e0164322 (2022).

(2) Chemani, C., Imberty, A., de Bentzmann, S., Pierre, M., Wimmerová, M., Guery, B. P. et al. Role of LecA and LecB lectins in Pseudomonas aeruginosa-induced lung injury and effect of carbohydrate ligands. Infect Immun 77, 2065-2075 (2009).

(3) Novichkov, P. S., Kazakov, A. E., Ravcheev, D. A., Leyn, S. A., Kovaleva, G. Y., Sutormin, R. A. et al. RegPrecise 3.0–a resource for genome-scale exploration of transcriptional regulation in bacteria. Bmc Genomics 14, 745 (2013).

(4) Cui, G. Y., Zhang, Y. X., Xu, X. J., Liu, Y. Y., Li, Z., Wu, M. et al. PmiR senses 2-methylisocitrate levels to regulate bacterial virulence in Pseudomonas aeruginosa. Sci Adv 8 (2022).

(5) Hwang, W., Yong, J. H., Min, K. B., Lee, K.-M., Pascoe, B., Sheppard, S. K. et al. Genome-wide association study of signature genetic alterations among pseudomonas aeruginosa cystic fibrosis isolates. Plos Pathog 17, e1009681 (2021).

(6) Gutu, A. D., Sgambati, N., Strasbourger, P., Brannon, M. K., Jacobs, M. A., Haugen, E. et al. Polymyxin resistance of Pseudomonas aeruginosa phoQ mutants is dependent on additional two-component regulatory systems. Antimicrob Agents Chemother 57, 2204-2215 (2013).

(7) Zhang, L., Fritsch, M., Hammond, L., Landreville, R., Slatculescu, C., Colavita, A. et al. Identification of genes involved in Pseudomonas aeruginosa biofilm-specific resistance to antibiotics. PLoS One 8, e61625 (2013).

(8) Galan-Vasquez, E., Luna, B. & Martinez-Antonio, A. The Regulatory Network of Pseudomonas aeruginosa. Microb Inform Exp 1, 3 (2011).

(9) Fan, L. G., Wang, T. T., Hua, C. F., Sun, W. J., Li, X. Y., Grunwald, L. et al. A compendium of DNA-binding specificities of transcription factors in Pseudomonas syringae. Nat Commun 11 (2020).

(10) Chan, S. S.-K. & Kyba, M. What is a master regulator? Journal of stem cell research & therapy 3, 114 (2013).

(11) Wang, T. T., Sun, W. J., Fan, L. G., Hua, C. F., Wu, N., Fan, S. R. et al. An atlas of the binding specificities of transcription factors in Pseudomonas aeruginosa directs prediction of novel regulators in virulence. Elife 10 (2021).

Reviewer #3 (Public review):

Summary:

The researchers performed a genetic screen to identify a protein, ZNF-236, which belongs to the zinc finger family, and is required for repression of heat shock inducible genes. The researchers applied a new method to map the binding sites of ZNF-236, and based on the data, suggested that the protein does not repress genes by directly binding to their regulatory regions targeted by HSF1. Insertion of a reporter in multiple genomic regions indicates that repression is not needed in repetitive genomic contexts. Together, this work identifies ZNF-236, a protein that is important to repress heat-shock-responsive genes in the absence of heat shock.

Strengths:

A hit from a productive genetic screen was validated, and followed up by a series of well-designed experiments to characterize how the repression occurs. The evidence that the identified protein is required for the repression of heat shock response genes is strong.

Weaknesses:

The researchers propose and discuss one model of repression based on protein binding data, which depends on a new technique and data that are not fully characterized.

Major Comments:

(1) The phrase "results from a shift in genome organization" in the abstract lacks strong evidence. This interpretation heavily relies on the protein binding technique, using ELT-2 as a positive and an imperfect negative control. If we assume that the binding is a red herring, the interpretation would require some other indirect regulation mechanism. Is it possible that ZNF-236 binds to the RNA of a protein that is required to limit HSF-1 and potentially other transcription factors' activation function? In the extrachromosomal array/rDNA context, perhaps other repressive mechanisms are redundant, and thus active repression by ZNF-236 is not required. This possibility is mentioned in one sentence in the discussion, but most of the other interpretations rely on the ZNF-236 binding data to be correct. Given that there is other evidence for a transcriptional role for ZNF-236, and no negative control (e.g. deletion of the zinc fingers, or a control akin to those done for ChIP-seq (like a null mutant or knockdown), a stronger foundation is needed for the presented model for genome organization.

(2) Continuing along the same line, the study assumes that ZNF-236 function is transcriptional. Is it possible to tag a protein and look at localization? If it is in the nucleus, it could be additional evidence that this is true.

(3) I suggest that the authors analyze the genomic data further. A MEME analysis for ZNF-236 can be done to test if the motif occurrences are enriched at the binding sites. Binding site locations in the genome with respect to genes (exon, intron, promoter, enhancer?) can be analyzed and compared to existing data, such as ATAC-seq. The authors also propose that this protein could be similar to CTCF. There are numerous high-quality and high-resolution Hi-C data in C. elegans larvae, and so the authors can readily compare their binding peak locations to the insulation scores to test their hypothesis.

(4) The researchers suggest that ZNF-236 is important for some genomic context. Based on the transcriptomic data, can they find a clue for what that context may be? Are the ZNF-236 repressed genes enriched for not expressed genes in regions surrounded by highly expressed genes?

Another way of approaching the implementation versus abstraction issue when it comes to misconceptions about programming languages and their toolchains/runtimes is to make "[programming languages are notation, and] notation is not machinery" something of a catchphrase.

This passage is something like an ideal target (case study is misapprehension).

This is the prime example I use to illustrate implicit step zero.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

BK channels are widely distributed and involved in many physiological functions. They have also proven a highly useful tool for studying general allosteric mechanisms for gating and modulation by auxiliary subunits. Tetrameric BK channels are assembled from four separate alpha subunits, which would be identical for homozygous alleles and potentially of five different combinations for heterozygous alleles (Geng et al., 2023, https://doi.org/10.1085/jgp.202213302). Construction of BK channels with concatenated subunits in order to strictly control heteromeric subunit composition had not yet been used because the N-terminus in BK channels is extracellular, whereas the C-terminus is intracellular. In this new work, Chen, Li, and Yan devise clever methods to construct and assemble BK channels of known subunit composition, as well as to fix the number of γ1 axillary subunits per channel. With their novel molecular approaches, Chen, Li and Yan report that a single γ1 axillary subunit is sufficient to fully modulate a BK channel, that the deep conducting pore mutation L312A exhibited a graded effect on gating with each addition mutated subunit replacing a WT subunit in the channel adding an additional incremental left shift in activation, and that the V288A mutation at the selectivity filter must be present on all four alpha subunits in order to induce channel inactivation. Chen, Li, and Yan have been successful in introducing new molecular tools to generate BK channels of known stoichiometry and subunit composition. They validate their methods and provide three examples of their use with useful observations.

Strengths:

Powerful new molecular tools for the study of channel gating have been developed and validated in the study.

Weaknesses:

(1) One example each of auxiliary, deep pore, and selectivity filter allosteric actions is presented, but this is sufficient for the purposes of the paper to establish their methods and present specific examples of applicability.

We sincerely thank Reviewer #1 for the thoughtful and supportive evaluation of our work. We greatly appreciate the reviewer’s clear summary of the study and the recognition of the novelty and utility of our molecular concatemer strategy for controlling BK channel subunit composition and stoichiometry.

We also appreciate the reviewer’s positive assessment that the three examples (auxiliary subunit modulation, deep pore mutation, and selectivity filter mutation) are sufficient to establish the method and demonstrate its applicability. We are encouraged that the reviewer found the new molecular tools to be powerful and well validated.

We have no further changes to make in response to this review, but we are grateful for the reviewer’s constructive and encouraging comments.

Reviewer #2 (Public review):

Summary:

This manuscript describes novel BK channel concatemers as a tool to study the stoichiometry of the gamma subunit and mutations in the modulation of the channel. Taking advantage of the modular design of the BK channel alpha subunit, the authors connected S1-S6/1st RCK as two- and four-subunit concatemers and coexpressed with S0-RCK2 to form normal function channels. These concatemers avoided the difficulty that the extracellular N-terminus of S0 was unable to connect with the cytosolic C-terminus of the gamma subunit, allowing a single gamma subunit to be connected to the concatemers. The concatemers also helped reveal the required stoichiometry of mutant BK subunits in modulating channel function. These include L312A in the deep pore region that altered channel function additively with each additional subunit harboring the mutation, and V288A at the selectivity filter that altered channel function cooperatively only when all four subunits were mutated. These results demonstrate that the concatemers are robust and effective in studying BK channel function and molecular mechanisms related to stoichiometry. The different requirement of the gamma subunit and the mutations stoichiometry for altering channel function is interesting, which may relate to the fundamental mechanism of how different motifs of the channel protein control function.

Strengths:

The manuscript presents well-designed experiments with high-quality data, which convincingly demonstrate the BK channel concatemers and their utility. The results are clearly presented.

Weaknesses:

This reviewer did not identify any major concerns with the manuscript.

We sincerely thank Reviewer #2 for the careful reading of our manuscript and for the highly positive and supportive comments. We appreciate the reviewer’s detailed summary of our concatemer design strategy and its use in studying gamma subunit stoichiometry and mutation-dependent modulation of BK channel function.

We are especially grateful for the reviewer’s recognition that the experiments are well designed, the data are of high quality, and the results demonstrate the robustness and utility of the concatemer approach. We also appreciate the reviewer’s thoughtful note on the mechanistic implications of the distinct stoichiometric requirements observed for the gamma subunit, L312A, and V288A.

We are pleased that the reviewer identified no major concerns. We have no further changes to make in response to this review, and we thank the reviewer again for the positive evaluation.

Recommendations for the authors:

Reviewing Editor Comments:

While the study presents a great methodological advancement, the phenomenological examples described could perhaps benefit from a little more mechanistic description/discussion. In particular, the functional effect of the V288A mutant is very novel. It could be useful to discuss whether this mutant impacts channel selectivity/conductance. It could be beneficial to also contrast the subunit dependence of V288A with that of the W434F mutant of the Shaker channel. In the latter, C-type inactivation gating is accelerated even when the mutant is present in a single subunit, which contrasts with the effect in V288A.

We greatly appreciate the editor’s and reviewers’ thorough and constructive evaluation, and we have revised the manuscript accordingly.

We added discussion with citation about the potential effect of V288A on selectivity (lines 348349). We also added the reported stoichiometric effects of mutations in Shaker and hERG1 channels on C-inactivation in discussion (lines 336-351). From these studies and our findings with V288A in BK channels, it is interesting to note that the stoichiometric effects of these mutations varies and those located near or within selectivity filter signature exhibited an all-or-none effect in both hERG1 and BK channels.

The authors might also want to consider performing and showing immunoblots with the alpha_deltaM fragment co-expressed with the other channel fragments. Together with the GFP tag, this alpha_deltaM would perhaps be a ~90 kDa protein. It should be captured by anti-V5 IP and resolved on an SDS-PAGE gel (at least with the quad construct).

We added supplemental data (Fig.1 – figure supplement 1) to show co-expression and co-IP of the α^ΔM-GFP construct and a FLAG-tagged α_M construct. The α^ΔM-GFP displayed right size on SDS-PAGE. It is of note that the single unit α_M construct tended to oligomerize even under denatured condition on SDS-PAGE.

For Figure 4, providing details about the inter-pulse intervals and interpulse holding voltage would be helpful. I was not able to find this information in the methods or text.

The inter-pulse intervals and holder voltage are now added in Fig. 4 legend (line 638).

Reviewer #1 (Recommendations for the authors):

(1) Submitted papers should have page numbers to facilitate reviewing.

Both page and line numbers are added.

(2) The designation of the various channel types, such as BKα and BKαM should be identical in the text and figures, so either drop BK in the text or add BK in the figures. Maybe drop BK in the text, as it is known that BK channels are the topic of this study.

We appreciate the suggestion to be consistent in text and figures. We have dropped “BK” for “BKα_M” throughout the text.

(3) "Single Boltzmann fits of G-V curves" would be consistent with a homogenous channel population but do not necessarily suggest a single homogenous channel population of BK channels, as was shown by Geng et al. (2023) (https://doi.org/10.1085/jgp.202213302) where the G-V curve for simultaneous expression of five BK channel types with different V1/2s for each channel type was well approximated by a single Boltzmann function. The dogma that a single Boltzmann fit suggests one channel type needs to be reset. So wave a red flag here: whereas a single Boltzmann fit is consistent with a single channel type, it does not establish a single channel type nor even suggest a single channel type.

We fully agree that a good Single Boltzmann fit doesn’t mean homogenous channel population. We have changed “suggesting” to “consistent with” (line 203) and “reflecting” to “agreeing with” (line 205).

(4) Geng et al. (2023) demonstrated that the pore mutation G375R in BK channels gave a left shift in activation linearly related to the number of WT subunits replaced with mutant subunits. This should incremental shift in activation for G375R should be mentioned, as it is consistent with the incremental effects of the L312A deep pore mutation on activation as reported by the authors in their Figure 3D.

We appreciate the pointing-out of this highly relevant publication. We have now included this reference and discussed together with L312A mutation (lines 309-313).

(5) I went back and looked at the Lingle laboratory papers on the gamma subunit. An additional sentence or two on what the Lingle lab found and didn't find would be useful here for readers.

In the Introduction, we have listed the Lingle lab’s findings and the limitations of their experimental methods that warrants the development of a concatenated construct method as proposed in this study (lines 84-88). We prefer to not discuss further in the Discussion as it will be redundant.

(6) For the two examined mutations L312A and V288A, include in the Methods a 21 amino acid sequence for each mutation with the amino acid to be mutated (L or V) in the center, with beginning and end numbering at the beginning and end of each list. This will allow the reader/experimenter to readily locate the mutated residue on their BK amino acid sequences, which may have different numbering than U11058. Interestingly, for the so-called canonical sequence Q12791 · KCMA1_HUMAN that I found in UniProt starting with U11058, there is an L312, but I found no V288, but an F288. Am I doing this correctly? Do I have the correct sequence/isoform? The only sure way to identify an AA is with an extensive pre and post-sequence so that the chance of misidentification approaches zero.

We verified that the listed Gene Bank IDs of U11058 for cDNA and AAB65837 for protein should point to the right sequences. In the section of Results, we have now included the peptide sequences of the selectivity filter signature motif and part of the S6 TM where V288 and L312A are located, respectively (lines 179 and 220).

Reviewer #2 (Recommendations for the authors):

The different stoichiometry of the gamma subunit and the mutations in regulating channel function raise important questions. For instance, what are the structural and energetic bases for their different stoichiometric requirements? Does the structure motif, such as the selectivity filter or deep pore, act as a unit? Or does a specific residue, such as V288 or L312, act individually to determine the different stoichiometric requirements? What molecular interactions are involved for these residues and subunit to influence the cooperativity among the four alpha subunits in channel function? Some of these questions are discussed in the manuscript, but it may help the readers to clarify what aspects of the mechanistic bases for the findings in this manuscript are known and what aspects remain to be studied.

We agree that these are all important questions. We have now cited more previous studies on C-inactivation in other K⁺ channels and on deep pore mutations in BK channels in terms of subunit stoichiometry (lines 336-351). The results appear to be consistent, suggesting shared properties among residues within the selectivity filter motif or among residues in deep pore region.

Some minor comments are as follows.

(1) Page 7, 2nd paragraph: "Page 2B" change to "Page 3B"? Also, "delay in deactivation" is not precise. The term "Delay" in channel kinetics has a specific meaning, and the use of this word here causes some confusion. The authors may want to delete "substantial delay in deactivation evident as a”.

Corrected by changing Fig. 2B to Fig. 3B and deleting “a substantial delay in deactivation evident as” (line 191).

(2) Page 9, 1st paragraph: "used in the voltage protocol used". Drop one of the instances of used".

Corrected by deleting the first “used” (line 246).

(3) Page 12, 1st paragraph: "Nonetheless, the tight inter-subunit cooperativity observed at the selectivity filter makes it a plausible candidate for serving as the activation gate, a property not yet demonstrated for the lower S6 segment." This seems to be an interesting idea. However, it is not clearly explained. The authors may want to clarify how the cooperativity is related to the activation gate.

We have now added a sentence with citations to discuss the requirement of intersubunit cooperativity for an activation gate to function (lines 354-357).

Other major changes: We updated immunoblot figures Fig1C and Fig2C for better presentation.

So document the process for updating the site in an SOP, making sure they're written in sufficient detail to be executable (by an agent—a user agent—sans LLMs), and then host the documents that detail those procedures on your site, as first-class content.

"Updating the site" then entails 1. consulting the SOP, and 2. carrying out the procedure there (either manually, or having your agent do it).

This is all achievable on a static site, provided there are Web-accessible (and, ideally, CORS-enabled) endpoints to control what content appears there (like the GitHub API, to name one example).

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors investigate how UVC-induced DNA damage alters the interaction between the mitochondrial transcription factor TFAM and mtDNA. Using live-cell imaging, qPCR, atomic force microscopy (AFM), fluorescence anisotropy, and high-throughput DNA-chip assays, they show that UVC irradiation reduces TFAM sequence specificity and increases mtDNA compaction without protecting mtDNA from lesion formation. From these findings, the authors suggest that TFAM acts as a "sensor" of damage rather than a protective or repair-promoting factor.

Strengths:

(1) The focus on UVC damage offers a clean system to study mtDNA damage sensing independently of more commonly studied repair pathways, such as oxidative DNA damage. The impact of UVC damage is not well understood in the mitochondria, and this study fills that gap in knowledge.

(2) In particular, the custom mitochondrial genome DNA chip provides high-resolution mapping of TFAM binding and reveals a global loss of sequence specificity following UVC exposure.

(3) The combination of in vitro TFAM DNA biophysical approaches, combined with cellular responses (gene expression, mtDNA turnover), provides a coherent multi-scale view.

(4) The authors demonstrate that TFAM-induced compaction does not protect mtDNA from UVC lesions, an important contribution given assumptions about TFAM providing protection.

Weaknesses:

(1) The authors show a decrease in mtDNA levels and increased lysosomal colocalization but do not define the pathway responsible for degradation. Distinguishing between replication dilution, mitophagy, or targeted degradation would strengthen the interpretation

We thank the reviewer for their careful reading of our manuscript and thoughtful suggestions. We agree that distinguishing between replication dilution, mitophagy, and/or targeted degradation would strengthen our understanding of how UV-induced DNA damage is handled in the mitochondria. Currently we are undertaking experiments to tease this apart, but consider the scope of those experiments to be beyond this manuscript and expect to publish them in a subsequent paper rather than this one. We added text explicitly stating that these possibilities are not distinguished by our results in pages 8-9 in the Discussion under the subsection ‘Mitochondria respond to UVC-induced mtDNA damage in the absence of apparent mitochondrial dysfunction’.

(2) The sudden induction of mtDNA replication genes and transcription at 24 h suggests that intermediate timepoints (e.g., 12 hours) could clarify the kinetics of the response and avoid the impression that the sampling coincidentally captured the peak.

We agree and have added additional timepoints of 12 hours and 18 hours post exposure. We have updated Figure 2 to include the new data and have added text on page 4 to include these results.

(3) The authors report no loss of mitochondrial membrane potential, but this single measure is limited. Complementary assays such as Seahorse analysis, ATP quantification, or reactive oxygen species measurement could more fully assess functional integrity.

We focused on membrane potential because loss of membrane potential is such a well-understood of mechanism for triggering mitophagy, but agree that these additional measurements are useful. We have added experiments to assess ATP levels, but did not see changes; we have added this data to Figure 2. We have also added text highlighting that we previously assessed mtROS following the same levels of UV exposure and observed no changes (in the results section on page 5 and in the discussion section on page 9). Given that we observe no changes in membrane potential or ATP, we have opted to not move forward with Seahorse analysis for the purposes of this paper.

(4) The manuscript briefly notes enrichment of TFAM at certain regions of the mitochondrial genome but provides little interpretation of why these regions are favored. Discussion of whether high-occupancy sites correspond to regulatory or structural elements would add valuable context.

We agree a discussion of these findings provides context and insight into where the field is currently in understanding TFAM sequence specificity. We have updated text in the discussion (pages 9-10) to include our thoughts on the drivers of TFAM sequence specificity with regard to the discrepancy with the anisotropy data and the lack of overlap with regulatory/structural elements.

(5) It remains unclear whether the altered DNA topology promotes TFAM compaction or vice versa. Addressing this directionality, perhaps by including UVC-only controls for plasmid conformation, would help disentangle these effects if UVC is causing compaction alone.

We have added an additional control making this comparison and updated the text on page 7 in the results section. UVC by itself (without TFAM being present) does not alter the plasmid compaction; see new supplemental Figure S16.

(6) The authors provide a discrepancy between the anisotropy and binding array results. The reason for this is not clear, and one wonders if an orthogonal approach for the binding experiments would elucidate this difference (minor point).

The discrepancy between anisotropy and the binding array results is certainly unusual and contrary to previous studies that have used these arrays. In addition to the anisotropy experiments, we selected a ‘high occupancy’ and ‘low occupancy’ sequence from the binding array and performed oligomerization experiments using atomic force microscopy, which allowed us to detect small changes in cooperativity (see supplemental Figure S15). We previously only discussed this briefly in the results section on page 6, but we have now updated the discussion section (pages 9-10) to highlight this finding and put forth ideas for the field as to why we think this might be the case. While we do see that the binding array data aligns with oligomerization and cooperativity of TFAM, we still do not know what it is about these sequences that would drive such differences in TFAM binding, but we speculate that it could have something to do with flexibility of the DNA sequences.

Assessment of conclusions:

The manuscript successfully meets its primary goal of testing whether TFAM protects mtDNA from UVC damage and the impact this has on the mtDNA. While their data points to an intriguing model that TFAM acts as a sensor of damaged mtDNA, the validation of this model requires further investigation to make the model more convincing. This is likely warranted for a follow-up study. Also, the biological impact of this compaction, such as altering transcription levels, is not clear in this study.

We have updated wording in the Abstract, Introduction, and elsewhere in the text (as detailed in other portions of our response) to make as explicit and clear as possible which results are supported by the in vitro versus in vivo data, and which parts are conclusions supported by the data versus hypothesized models to be tested in future work.

Impact and utility of the methods:

This work advances our understanding of how mitochondria manage UVC genome damage and proposes a structural mechanism for damage "sensing" independent of canonical repair. The methodology, including the custom TFAM DNA chip, will be broadly useful to the scientific community.

Context:

The study supports a model in which mitochondrial genome integrity is maintained not only by repair factors, but also by selective sequestration or removal of damaged genomes. The demonstration that TFAM compaction correlates with damage rather than protection reframes an interesting role in mtDNA quality control.

Reviewer #2 (Public review):

Summary:

King et al. present several sets of experiments aimed to address the potential impact of UV irradiation on human mitochondrial DNA as well as the possible role of mitochondrial TFAM protein in handling UV-irradiated mitochondrial genomes. The carefully worded conclusion derived from the results of experiments performed with human HeLa cells, in vitro small plasmid DNA, with PCR-generated human mitochondrial DNA, and with UV-irradiated small oligonucleotides is presented in the title of the manuscript: "UV irradiation alters TFAM binding to mitochondrial DNA". The authors also interpret results of somewhat unconnected experimental approaches to speculate that "TFAM is a potential DNA damage sensing protein in that it promotes UVC-dependent conformational changes in the [mitochondrial] nucleoids, making them more compact." They further propose that such a proposed compaction triggers the removal of UV-damaged mitochondrial genomes as well as facilitates replication of undamaged mitochondrial genomes.

Strengths:

(1) The authors presented convincing evidence that a very high dose (1500 J/m2) of UVC applied to oligonucleotides covering the entire mitochondrial DNA genome alleviates sequence specificity of TFAM binding (Figure 3). This high dose was sufficient to cause UV lesions in a large fraction of individual oligonucleotides. The method was developed in the lab of one of the corresponding authors (reference 74) and is technically well-refined. This result can be published as is or in combination with other data.

(2) The manuscript also presents AFM evidence (Figure 4) that TFAM, which was long known to facilitate compaction of the mitochondrial genome (Alam et al., 2003; PMID 12626705 and follow-up citations), causes in vitro compaction of a small pUC19 plasmid and that approximately 3 UVC lesions per plasmid molecule result in a slight, albeit detectable, increase in TFAM compaction of the plasmid. Both results can be discussed in line with a possible extrapolation to in vivo phenomena, but such a discussion should include a clear statement that no in vivo support was provided within the set of experiments presented in the manuscript.

We thank this reviewer for their careful reading and interpretation of the manuscript. We agree that discussion of in vivo implications and extrapolations need clear statements indicating where there is not currently in vivo support. We have updated the text throughout the paper to include this.

Weaknesses:

Besides the experiments presented in Figures 3 and 4, other results do not either support or contradict the speculation that TFAM can play a protective role, eliminating mitochondrial genomes with bulky lesions by way of excessive compaction and removing damaged genomes from the in vivo pool.

To specify these weaknesses:

(1) Figure 1 - presents evidence that UVC causes a reduction in the number of mitochondrial spots in cells. The role of TFAM is not assessed.

We are working to understand the role of TFAM in vivo following UV irradiation, but believe that work should be included in follow up studies rather than this publication.

(2) Figure 2 - presents evidence that UVC causes lesions in mitochondrial genomes in vivo, detectable by qPCR. No direct assessment of TFAM roles in damage repair or mitochondrial DNA turnover is assessed despite the statements in the title of Figure 2 or in associated text. Approximately 2-fold change in gene expression of TFAM and of the three other genes does not provide any reasonable support to suggestion about increased mitochondrial DNA turnover over multiple explanations on related to mitochondrial DNA maintenance.

We agree and have updated the title of Figure 2 to better reflect the findings outlined in the figure as well as the text.

The new title is, “UVC causes mtDNA damage that decreases over time and is associated with upregulation of mtDNA replication genes, in the absence of apparent mitochondrial dysfunction.”

We agree that there are numerous mechanistic hypotheses that could explain the decrease in mtDNA damage over time. In Figure 1, we show that there is an overall decrease in mtDNA spots, and an increase in mtDNA-lysosome colocalization, suggestive of mtDNA degradation, which could serve to remove damaged genomes. One possibility is that TFAM is playing a role in the damage removal (but not repair per cell as these lesions are not repaired). Another is changes in mtDNA turnover via increasing the replication machinery in order the synthesize non-damaged mtDNA molecules to dilute out damage. These and other possibilities are not mutually exclusive. We have added text (pages 8-9) to make explicit that additional work will be required to distinguish these possibilities. We note that we have also added an additional experiment showing that TFAM knockdown affects mtDNA damage at baseline, as well as after UVC exposure (Figure 5J).

(3) Figure 5. Shows that TFAM does not protect either mitochondrial nucleoids formed in vitro or mitochondrial DNA in vivo from UVC lesions as well as has no effect on in vivo repair of UV lesions.

We agree that Figure 5 shows that TFAM does not protect DNA from UVC-induced lesions, and that a roughly 2-fold increase in TFAM protein does not alter damage reduction over time. We have added new data showing that in vivo, knockdown of TFAM results in an increase in baseline (control conditions) mtDNA damage, and also alters the rate of decrease of mtDNA damage over time after UVC (Figure 5J).

(4) Figure 6: Based on the above analysis, the model of the role of TFAM in sensing mtDNA damage and elimination of damaged genomes in vivo appears unsupported.

We have updated the legend for Figure 6 in which we outline our hypothesized role of TFAM in sensing mtDNA damage to ensure that readers know this has yet to be fully tested in vivo. We have also updated the Figure legend title from “proposed model” to “hypothesized model,” and changed the wording in the conclusion section (page 11) to highlight more clearly that this is a working model.

(5) Additional concern about Figure 3 and relevant discussion: It is not clear if more uniform TFAM binding to UV irradiated oligonucleotides with varying sequence as compared to non-irradiated oligonucleotides can be explained by just overall reduced binding eliminating sequence specific peaks.

We do not believe this is the case given the similar K_D values for the sequences tested. In our hands and in other publications (reviewed in PMID: 34440420), it has been well established that TFAM binds damaged DNA very well—essentially just as well as nondamaged DNA or better.

Additionally, a reduction in overall binding on these DNA arrays tends to make sequence specific peaks more apparent. We ran our experiments at both 30 nM and 300 nM TFAM specifically to be able to assess this question. The 300 nM data can be found in supplemental Figure S7. In this figure, we notice that the peaks appear more uniform at the high concentration (comparing Figure 3A to Figure S7A). That is presumably because there is so much more binding happening across the array that the peaks associated with the strongest binders become less pronounced. For the sake of brevity, we have not added this reasoning to the text, but are willing to do so if the Reviewers and Editor feel that it is important to include.

Reviewer #3 (Public review):

Summary:

The study is grounded in the observations that mitochondrial DNA (mtDNA) exhibits a degree of resistance to mutagenesis under genotoxic stress. The manuscript focuses on the effects of UVC-induced DNA damage on TFAM-DNA binding in vitro and in cells. The authors demonstrate increased TFAM-DNA compaction following UVC irradiation in vitro based on high-throughput protein-DNA binding and atomic force microscopy (AFM) experiments. They did not observe a similar trend in fluorescence polarization assays. In cells, the authors found that UVC exposure upregulated TFAM, POLG, and POLRMT mRNA levels without affecting the mitochondrial membrane potential. Overexpressing TFAM in cells or varying TFAM concentration in reconstituted nucleoids did not alter the accumulation or disappearance of mtDNA damage. Based on their data, the authors proposed a plausible model that, following UVC-induced DNA damage, TFAM facilitates nucleoid compaction, which may serve to signal damage in the mitochondrial genome.

Strengths:

The presented data are solid, technically rigorous, and consistent with established literature findings. The experiments are well-executed, providing reliable evidence on the change of TFAM-DNA interactions following UVC irradiation. The proposed model may inspire future follow-up studies to further study the role of TFAM in sensing UVC-induced damage.

Weaknesses:

The manuscript could be further improved by refining specific interpretations and ensuring terminology aligns precisely with the data presented.

(1) In line 322, the claim of increased "nucleoid compaction" in cells should be removed, as there is a lack of direct cellular evidence. Given that non-DNA-bound TFAM is subject to protease digestion, it is uncertain to what extent the overexpressed TFAM actually integrates into and compacts mitochondrial nucleoids in the absence of supporting immunofluorescence data.

We would like to thank this reviewer for their comments and suggestions. We feel these specific language changes have strengthened the interpretability of the text. The TFAM overexpression cells used in this experiment were given to us by Isaac et al., who demonstrated that when TFAM was overexpressed in this specific cell line, the nucleoids were indeed more compact, measured by Fiber-seq (Isaac et al., 2024; PMID: 38347148). We have removed the claim “increased compaction” from the section title, Figure 5 legend title, and from line 322 (now on page 8), and have also added an additional sentence to ensure the reader knows these cells have been shown to have presumed increased compaction by other groups.

(2) In lines 405 and 406, the authors should avoid equating TFAM overexpression with compaction in the cellular context unless the compaction is directly visualized or measured.

We have updated the text to ensure that it is clear that this was tested by other groups. We also changed the wording to “inaccessible (presumably compacted) nucleoids.” While we did not demonstrate altered compaction in our study, we think that based on the results from Isaac et al., it is likely that there was increased compaction. In addition, some readers might not have the context to make the connection between compaction and accessibility, so eliminating all reference to compaction could obscure the point.

(3) In lines 304 and 305 (and several other places throughout the manuscript), the authors use the term "removal rates". A "removal rate" requires a direct comparison of accumulated lesion levels over a time course under different conditions. Given the complexity of UV-induced DNA damage-which involves both damage formation and potential removal via multiple pathways-a more accurate term that reflects the net result of these opposing processes is "accumulated DNA damage levels." This terminology better reflects the final state measured and avoids implying a single, active 'removal' pathway without sufficient kinetic data.

We agree and have updated the language throughout the text as well as the results heading for this section.

(4) In line 357, the authors refer to the decrease in the total DNA damage level as "The removal of damaged mtDNA". The decrease may be simply due to the turnover and resynthesis of non-damaged mtDNA molecules. The term "removal" may mislead the casual reader into interpreting the effect as an active repair/removal process.

We agree and have restructured this sentence for clarity. We do believe there is some removal happening, given the increase in mtDNA colocalization in lysosomes alongside decrease of mtDNA spots in our live cell imaging. We have written it to reflect the inclusion of removal and resynthesis of nondamaged mtDNA molecules (see pages 8-9).

Recommendations for the authors:

Reviewing Editor Comments:

The reviewers appreciate the quality of the presented data but concur that they do not support the primary claims in the title and abstract. The reviewers also realize that in vivo evidence for the model would require extensive new experimentation that goes beyond a reasonable revision. The recommendation is to change the title and significantly revise text, figure titles and legends for transparency, and conclusions within results and discussion sections.

We thank the editor and all the reviewers for their feedback. We have added additional experiments, updated text throughout the entire paper to ensure our claims are supported, and revised our title. We feel that the changes we have made have indeed made the paper stronger, more transparent, and that the evidence put forth in this paper provides support for all claims made.

Reviewer #1 (Recommendations for the authors):

(1) Clarify mitochondrial response kinetics by adding an intermediate (e.g., 12 hrs) recovery timepoint for transcriptional analysis to resolve when TFAM and replication genes are induced.

We have added additional timepoints of 12 and 18 hours following exposure in Figure 2. These results strengthen our finding that the nuclear transcriptional program supporting mtDNA replication appears to be activated prior to the nuclear transcriptional program supporting mitochondrial transcription, in that POLG and TFAM come up before POLRMT and ND1.

(2) Strengthen functional readouts by assessing additional parameters of mitochondrial function to substantiate the claim that UVC does not impair mitochondrial performance.

We have referenced our previously-published data on mtROS and added a measurement of ATP following UVC exposure in Figure 2.

(3) Consider exploring whether mtDNA degradation occurs via mitophagy, nucleoid-phagy, or another pathway-potentially by using inhibitors or markers of these processes.

While we agree that this is an important follow up question and are currently working on experiments to address this, those experiments are outside the scope of this manuscript.

(4) Provide additional details for the high occupancy TFAM sites. Provide brief annotation or discussion of genomic regions showing strong TFAM binding under non-irradiated conditions that are lost during UVC treatment. This would be helpful to the field as a whole.

We have updated our discussion section to include this.

(5) Include or discuss a control using UVC irradiated pUC19 without TFAM to confirm that observed compaction categories are TFAM dependent rather than an UVC induced DNA distortion.

We have added in a supplemental figure (Figure S16) containing comparison of area analysis of control pUC19 and UV-irradiated pUC19 and we have added associated text in the results section of the paper.

(6) It would be interesting to explore the link between compaction to transcriptional output. In the TFAM overexpression model, the authors could measure expression of mtDNA encoded transcripts (e.g., ND1, COX1) to connect increased compaction with altered mitochondrial transcription.

While we agree that understanding how the compactional status alters mitochondrial transcription is worthwhile, we believe this is beyond the scope of this paper. Furthermore, this connection has previously been shown by Bruser et al., 2021 (PMID: 34818548) who showed that more compact nucleoids are not undergoing active transcription. It will be interesting to see in future work if mtDNA damage drives changes in both compaction as well as transcriptional activity.

(7) Clarify quantitative presentation in figure 2F to explicitly note whether the observed increase in fluorescence intensity was statistically insignificant and confirm that the assay sensitivity is sufficient to detect small potential changes. As presented it is not clear if there is a change.

We have changed the presentation of Figure 2F. There is a slight increase in membrane potential at the 24-hour time point and we have made that clear in the text as well. We included FCCP as a (standard) positive control, for which we can detect the associated decrease in membrane potential for. While it is always possible that a very small decrease occurred that we were unable to detect, we note that none of the six UVC-exposed groups that we tested even trended towards a decrease in MMP, making it less likely that there was an effect that we simply lacked the power or sensitivity to detect.

(8) It would be interesting if the authors can comment on whether TFAM induced compaction after UVC might shield mtDNA from other, repairable lesions (e.g., oxidative or alkylation damage), offering a broader context for this mechanism beyond just UVC.

In theory, we believe this is possible. It will also be interesting to see if the increased compaction following UVC also protects or shields the mtDNA from other enzymatic processes, such as repair proteins that may be searching for repairable lesions such as oxidative or alkylation damage. In this case, it seems as though the increased compaction would prevent the repair from happening at genomes harboring damage.

In this study we show with our in vitro nucleoids that the increased compaction does not protect against UVC, but this is likely because UVC does not need physical access to the DNA in order to damage it, as the wavelengths of UVC (centered in this case at 254nm) are readily absorbed by proteins and thus can go right through the proteins. Currently, we know that increased compaction by TFAM makes the DNA inaccessible to the enzymes required to methylate DNA used in Fiber-seq (PMID: 38347148), but we do not know if the compaction is tight enough to prevent ROS or alkylating agents from damaging the DNA. We have updated text in the discussion on page 10 to highlight some of these ideas.

Reviewer #2 (Recommendations for the authors):

Please, go over all display items and text and clarify details that can help readers to understand important specifics of the experiments. Examples are provided below:

(1) Abstract and Introduction - indicate species and cell line

We have updated the text to include this information.

(2) Table 1 "TFAM KD measurements"- title and footnotes are entirely cryptic. Please, clarify the experimental design, question(s) addressed and conclusions drawn from data.

We have updated the title of Table 1 to "Binding of TFAM to array sequences, measured using fluorescence anisotropy,” and clarified the footnotes to make sure it is clear which sequences were selected for AFM oligomerization experiments.

(3) Figure 3 and Material and Methods - specify UVC dose.

We have added this information to both the figure legend and the methods section.

(4) Figure 4 - specify UVC dose.

We have added this information to the figure legend.

(5) Figure 5. Panel B indicate which band is TFAM and which is HA-tag; Indicate clearly which panel is showing in vivo or in vitro results.

We have updated the figure to label the untagged TFAM and HA-tagged TFAM and changed the panel titles to specify if they are in vivo results.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Review of the manuscript titled " Mycobacterial Metallophosphatase MmpE acts as a nucleomodulin to regulate host gene expression and promotes intracellular survival".

The study provides an insightful characterization of the mycobacterial secreted effector protein MmpE, which translocates to the host nucleus and exhibits phosphatase activity. The study characterizes the nuclear localization signal sequences and residues critical for the phosphatase activity, both of which are required for intracellular survival.

Strengths:

(1) The study addresses the role of nucleomodulins, an understudied aspect in mycobacterial infections.

(2) The authors employ a combination of biochemical and computational analyses along with in vitro and in vivo validations to characterize the role of MmpE.

Weaknesses:

(1) While the study establishes that the phosphatase activity of MmpE operates independently of its NLS, there is a clear gap in understanding how this phosphatase activity supports mycobacterial infection. The investigation lacks experimental data on specific substrates of MmpE or pathways influenced by this virulence factor.

We thank the reviewer for this insightful comment and agree that identification of the substrates of MmpE is important to fully understand its role in mycobacterial infection. MmpE is a putative purple acid phosphatase (PAP) and a member of the metallophosphoesterase (MPE) superfamily. Enzymes in this family are known for their catalytic promiscuity and broad substrate specificity, acting on phosphomonoesters, phosphodiesters, and phosphotriesters (Matange et al., Biochem J, 2015). In bacteria, several characterized MPEs have been shown to hydrolyze substrates such as cyclic nucleotides (e.g., cAMP) (Keppetipola et al., J Biol Chem, 2008; Shenoy et al., J Mol Biol, 2007), nucleotide derivatives (e.g., AMP, UDP-glucose) (Innokentev et al., mBio, 2025), and pyrophosphate-containing compounds (e.g., Ap4A, UDP-DAGn) (Matange et al., Biochem J., 2015). Although the binding motif of MmpE has been identified, determining its physiological substrates remains challenging due to the low abundance and instability of potential metabolites, as well as the limited sensitivity and coverage of current metabolomic technologies in mycobacteria.

(2) The study does not explore whether the phosphatase activity of MmpE is dependent on the NLS within macrophages, which would provide critical insights into its biological relevance in host cells. Conducting experiments with double knockout/mutant strains and comparing their intracellular survival with single mutants could elucidate these dependencies and further validate the significance of MmpE's dual functions.

We thank the reviewer for the comment. Deletion of the NLS motifs did not impair MmpE’s phosphatase activity in vitro (Figure 2F), indicating that MmpE's enzymatic function operates independently of its nuclear localization. Indeed, we confirmed that Fe³⁺-binding ability via the residues H348 and N359 is required for enzymatic activity of MmpE. We have expanded on this point in the Discussion section “MmpE is a bifunctional virulence factor in Mtb”.

(3) The study does not provide direct experimental validation of the MmpE deletion on lysosomal trafficking of the bacteria.

We thank the reviewer for the comment. To validate the role of MmpE in lysosome maturation during infection, we conducted fluorescence colocalization assays in THP-1 macrophages infected with BCG strains, including WT, ∆MmpE, Comp-MmpE, Comp-MmpE^ΔNLS1, Comp-MmpE^ΔNLS2, Comp-MmpE^ΔNLS1-2. These strains were stained with the lipophilic membrane dye DiD, while macrophages were treated with the acidotropic probe LysoTracker^TM Green (Martins et al., Autophagy, 2019). The result indicated that ΔMmpE and MmpE^NLS1-2 mutants exhibited significantly higher co-localization with LysoTracker compared to WT and Comp-MmpE strains (New Figure 5G), suggesting that MmpE deletion leads to enhanced lysosomal maturation during infection.

(4) The role of MmpE as a mycobacterial effector would be more relevant using virulent mycobacterial strains such as H37Rv.

We thank the reviewer for the comment. Previously, the role of Rv2577/MmpE as a virulence factor has been demonstrated in M. tuberculosis CDC 1551, where its deletion significantly reduced bacterial replication in mouse lungs at 30 days post-infection (Forrellad et al., Front Microbiol, 2020). However, that study did not explore the underlying mechanism of MmpE function. In our study, we found that MmpE enhances M. bovis BCG survival in macrophages (THP-1 and RAW264.7 both) and in mice (Figure 3, Figure 7A), consistent with its proposed role in virulence. To investigate the molecular mechanism by which MmpE promotes intracellular survival, we used M. bovis BCG as a biosafe surrogate and this model is widely accepted for studying mycobacterial pathogenesis (Wang et al., Nat Immunol, 2015; Wang et al., Nat Commun, 2017; Péan et al., Nat Commun, 2017).

Reviewer #2 (Public review):

Summary:

In this paper, the authors have characterized Rv2577 as a Fe3+/Zn2+ -dependent metallophosphatase and a nucleomodulin protein. The authors have also identified His348 and Asn359 as critical residues for Fe3+ coordination. The authors show that the proteins encode for two nuclease localization signals. Using C-terminal Flag expression constructs, the authors have shown that the MmpE protein is secretory. The authors have prepared genetic deletion strains and show that MmpE is essential for intracellular survival of M. bovis BCG in THP-1 macrophages, RAW264.7 macrophages, and a mouse model of infection. The authors have also performed RNA-seq analysis to compare the transcriptional profiles of macrophages infected with wild-type and MmpE mutant strains. The relative levels of ~ 175 transcripts were altered in MmpE mutant-infected macrophages and the majority of these were associated with various immune and inflammatory signalling pathways. Using these deletion strains, the authors proposed that MmpE inhibits inflammatory gene expression by binding to the promoter region of a vitamin D receptor. The authors also showed that MmpE arrests phagosome maturation by regulating the expression of several lysosome-associated genes such as TFEB, LAMP1, LAMP2, etc. These findings reveal a sophisticated mechanism by which a bacterial effector protein manipulates gene transcription and promotes intracellular survival.

Strength:

The authors have used a combination of cell biology, microbiology, and transcriptomics to elucidate the mechanisms by which Rv2577 contributes to intracellular survival.

Weakness:

The authors should thoroughly check the mice data and show individual replicate values in bar graphs.

We kindly appreciate the reviewer for the advice. We have now updated the relevant mice data in the revised manuscript.

Reviewer #3 (Public review):

Summary:

In this manuscript titled "Mycobacterial Metallophosphatase MmpE Acts as a Nucleomodulin to Regulate Host Gene Expression and Promote Intracellular Survival", Chen et al describe biochemical characterisation, localisation and potential functions of the gene using a genetic approach in M. bovis BCG and perform macrophage and mice infections to understand the roles of this potentially secreted protein in the host cell nucleus. The findings demonstrate the role of a secreted phosphatase of M. bovis BCG in shaping the transcriptional profile of infected macrophages, potentially through nuclear localisation and direct binding to transcriptional start sites, thereby regulating the inflammatory response to infection.

Strengths:

The authors demonstrate using a transient transfection method that MmpE when expressed as a GFP-tagged protein in HEK293T cells, exhibits nuclear localisation. The authors identify two NLS motifs that together are required for nuclear localisation of the protein. A deletion of the gene in M. bovis BCG results in poorer survival compared to the wild-type parent strain, which is also killed by macrophages. Relative to the WT strain-infected macrophages, macrophages infected with the ∆mmpE strain exhibited differential gene expression. Overexpression of the gene in HEK293T led to occupancy of the transcription start site of several genes, including the Vitamin D Receptor. Expression of VDR in THP1 macrophages was lower in the case of ∆mmpE infection compared to WT infection. This data supports the utility of the overexpression system in identifying potential target loci of MmpE using the HEK293T transfection model. The authors also demonstrate that the protein is a phosphatase, and the phosphatase activity of the protein is partially required for bacterial survival but not for the regulation of the VDR gene expression.

Weaknesses:

(1) While the motifs can most certainly behave as NLSs, the overexpression of a mycobacterial protein in HEK293T cells can also result in artefacts of nuclear localisation. This is not unprecedented. Therefore, to prove that the protein is indeed secreted from BCG, and is able to elicit transcriptional changes during infection, I recommend that the authors (i) establish that the protein is indeed secreted into the host cell nucleus, and (ii) the NLS mutation prevents its localisation to the nucleus without disrupting its secretion.

We kindly appreciate the reviewer for this insightful comment. To confirm the translocation of MmpE into the host nucleus during BCG infection, we first detected the secretion of MmpE by M. bovis BCG, using Ag85B as a positive control and GlpX as a negative control (Zhang et al., Nat commun, 2022). Our results showed that MmpE- Flag was present in the culture supernatant, indicating that MmpE is secreted by BCG indeed (new Figure S1C).

Next, we performed immunoblot analysis of the nuclear fractions from infected THP-1 macrophages expressing FLAG-tagged wild-type MmpE and NLS mutants. The results revealed that only wild-type MmpE was detected in the nucleus, while MmpE^ΔNLS1, MmpE^ΔNLS2 and MmpE^ΔNLS1-2 were not detectable in the nucleus (New Figure S1D). Taken together, these findings demonstrated that MmpE is a secreted protein and that its nuclear translocation during infection requires both NLS motifs.

Demonstration that the protein is secreted: Supplementary Figure 3 - Immunoblotting should be performed for a cytosolic protein, also to rule out detection of proteins from lysis of dead cells. Also, for detecting proteins in the secreted fraction, it would be better to use Sauton's media without detergent, and grow the cultures without agitation or with gentle agitation. The method used by the authors is not a recommended protocol for obtaining the secreted fraction of mycobacteria.

We kindly appreciate the reviewer for the advice. To avoid the effects of bacterial lysis, we cultured the BCG strains expressing MmpE-Flag in Middlebrook 7H9 broth with 0.5% glycerol, 0.02% Tyloxapol, and 50 µg/mL kanamycin at 37 °C with gentle agitation (80 rpm) until an OD₆₀₀ of approximately 0.6 (Zhang et al., Nat Commun, 2022). Subsequently, we assessed the secretion of MmpE-Flag in the culture supernatant, using Ag85B as a positive control and GlpX as a negative control (New Figure S1C). The results showed that GlpX was not detected in the supernatant, while MmpE and Ag85B were detected, indicating that MmpE is indeed a secreted protein in BCG.

Demonstration that the protein localises to the host cell nucleus upon infection: Perform an infection followed by immunofluorescence to demonstrate that the endogenous protein of BCG can translocate to the host cell nucleus. This should be done for an NLS1-2 mutant expressing cell also.

We thank the reviewer for the suggestion. We agree that this experiment would be helpful to further verify the ability of MmpE for nuclear import. However, MmpE specific antibody is not available for us for immunofluorescence experiment. Alternatively, we performed nuclear-cytoplasmic fractionation for the THP-1 cells infected with the M. bovis BCG strains expressing FLAG-tagged wild-type MmpE, as well as NLS deletion mutants (MmpE^ΔNLS1, MmpE^ΔNLS2, and MmpE^ΔNLS1-2). The WT MmpE is detectable in both cytoplasmic and nuclear compartments, while MmpE^ΔNLS1, MmpE^ΔNLS2 or MmpE^ΔNLS1-2 were almost undetectable in nuclear fractions (New Figure S1D), suggesting that both NLS motifs are necessary for nuclear import.

(2) In the RNA-seq analysis, the directionality of change of each of the reported pathways is not apparent in the way the data have been presented. For example, are genes in the cytokine-cytokine receptor interaction or TNF signalling pathway expressed more, or less in the ∆mmpE strain?

We thank the reviewer for the comment. The KEGG pathway enrichment diagrams in our RNA-seq analysis primarily reflect the statistical significance of pathway enrichment based on differentially expressed genes, but do not indicate the directionality of genes expression changes. To address this concern, we conducted qRT-PCR on genes associated with the cytokine-cytokine receptor interaction pathway, specifically IL23A, CSF2, and IL12B. The results showed that, compared to the WT strain, infection with the ΔMmpE strain resulted in significantly increased expression levels of these genes in THP-1 cells (Figure 4F, Figure S4B), consistent with the RNA-seq data. Furthermore, we have submitted the complete RNA-seq dataset to the NCBI GEO repository [GSE312039], which includes normalized expression values and differential expression results for all detected genes.

(3) Several of these pathways are affected as a result of infection, while others are not induced by BCG infection. For example, BCG infection does not, on its own, produce changes in IL1β levels. As the author s did not compare the uninfected macrophages as a control, it is difficult to interpret whether ∆mmpE induced higher expression than the WT strain, or simply did not induce a gene while the WT strain suppressed expression of a gene. This is particularly important because the strain is attenuated. Does the attenuation have anything to do with the ability of the protein to induce lysosomal pathway genes? Does induction of this pathway lead to attenuation of the strain? Similarly, for pathways that seem to be downregulated in the ∆mmpE strain compared to the WT strain, these might have been induced upon infection with the WT strain but not sufficiently by the ∆mmpE strain due to its attenuation/ lower bacterial burden.

We thank the reviewer for the comment. Previous studies have shown that wild-type BCG induces relatively low levels of IL-1β, while retaining partial capacity to activate the inflammasome (Qu et al., Sci Adv, 2020). Our data (Figures 3G) show that infection with the ΔMmpE strain results in enhanced IL-1β expression, consistent with findings by Master et al. (Cell Host Microbe, 2008), in which deletion of zmp1 in BCG or M. tuberculosis led to increased IL-1β levels due to reduced inhibition of inflammasome activation.

In the revised manuscript, we have provided additional qRT-PCR data using uninfected macrophages as a baseline control. These results demonstrate that the WT strain suppresses lysosome-associated gene expression, whereas the ΔMmpE strain upregulates these genes, indicating that MmpE inhibits lysosome-related genes expression (Figure 4G). Furthermore, bacterial burden analysis revealed that ∆mmpE exhibited ~3-fold lower intracellular survival than the WT strain in THP-1 cells. However, when lysosomal maturation was inhibited, the difference in bacterial load between the two strains was reduced to ~1-fold (New Figures S6B and C). These findings indicate that MmpE promotes intracellular survival primarily by inhibiting lysosomal maturation, which is consistent with a previous study (Chandra et al., Sci Rep, 2015).

(4) CHIP-seq should be performed in THP1 macrophages, and not in HEK293T. Overexpression of a nuclear-localised protein in a non-relevant line is likely to lead to several transcriptional changes that do not inform us of the role of the gene as a transcriptional regulator during infection.

We thank the reviewer for the comment. We performed ChIP-seq in HEK293T cells based on their high transfection efficiency, robust nuclear protein expression, and well-annotated genome (Lampe et al., Nat Biotechnol, 2024; Marasco et al., Cell, 2022). These characteristics make HEK293T an ideal system for the initial identification of genome-wide chromatin binding profiles by MmpE.

Further, we performed comprehensive validation of the ChIP-seq findings in THP-1 macrophages. First, CUT&Tag and RNA-seq analyses in THP-1 cells revealed that MmpE modulates genes involved in the PI3K–AKT signaling and lysosomal maturation pathways (Figure 4C; Figure S5A-B). Correspondingly, we found that infection with the ΔMmpE strain led to reduced phosphorylation of AKT (S473), mTOR (S2448), and p70S6K (T389) (New Figure 5E-F), and upregulation of lysosomal genes such as TFEB, LAMP1, and LAMP2 (Figure 4G), compared to infection with the WT strain, and lysosomal maturation in cells infected with the ΔMmpE strain more obviously (New Figure 5G). Additionally, CUT&Tag profiling identified MmpE binding at the promoter region of the VDR gene, which was further validated by EMSA and ChIP-qPCR. Also, qRT-PCR demonstrated that MmpE suppresses VDR transcription, supporting its role as a transcriptional regulator (Figure 6). Collectively, these data confirm the biological relevance and functional significance of the ChIP-seq findings obtained in HEK293T cells.

(5) I would not expect to see such large inflammatory reactions persisting 56 days post-infection with M. bovis BCG. Is this something peculiar for an intratracheal infection with 1x107 bacilli? For images of animal tissue, the authors should provide images of the entire lung lobe with the zoomed-in image indicated as an inset.

We thank the reviewer for the comment. The lung inflammation peaked at days 21–28 and had clearly subsided by day 56 across all groups (New Figure 7B), consistent with the expected resolution of immune responses to an attenuated strain like M. bovis BCG. This temporal pattern is in line with previous studies using intravenous or intratracheal BCG vaccination in mice and macaques, which also demonstrated robust early immune activation followed by resolution over time (Smith et al., Nat Microbiol, 2025; Darrah et al., Nature, 2020).

In this study, the infectious dose (1×10⁷ CFU intratracheal) was selected based on previous studies in which intratracheal delivery of 1×10⁷ CFU produced consistent and measurable lung immune responses and pathology without causing overt illness or mortality (Xu et al., Sci Rep, 2017; Niroula et al., Sci Rep, 2025). We have provided whole-lung lobe images with zoomed-in insets in the source dataset.

(6) For the qRT-PCR based validation, infections should be performed with the MmpE-complemented strain in the same experiments as those for the WT and ∆mmpE strain so that they can be on the same graph, in the main manuscript file. Supplementary Figure 4 has three complementary strains. Again, the absence of the uninfected, WT, and ∆mmpE infected condition makes interpretation of these data very difficult.

We thank the reviewer for the comment. As suggested, we have conducted the qRT-PCR experiment including the uninfected, WT, ∆mmpE, Comp-MmpE, and the three complementary strains infecting THP-1 cells (Figure 4F and G; New Figure S4B–D).

(7) The abstract mentions that MmpE represses the PI3K-Akt-mTOR pathway, which arrests phagosome maturation. There is not enough data in this manuscript in support of this claim. Supplementary Figure 5 does provide qRT-PCR validation of genes of this pathway, but the data do not indicate that higher expression of these pathways, whether by VDR repression or otherwise, is driving the growth restriction of the ∆mmpE strain.

We thank the reviewer for the comment. In the updated manuscript, we have provided more evidence. First, the RNA-seq analysis indicated that MmpE affects the PI3K-AKT signaling pathway (Figure 4C). Second, CUT&Tag analysis suggested that MmpE binds to the promoter regions of key pathway components, including PRKCB, PLCG2, and PIK3CB (Figure S5A). Third, confocal microscopy showed that ΔMmpE strain promotes significantly increased lysosomal maturation compared to the WT, a process downstream of the PI3K-AKT-mTOR axis (New Figure 5G).

Further, we measured protein phosphorylation for validating activation of the pathway (Zhang et al., Stem Cell Reports, 2017). Our results showed that cells infected with WT strains exhibited significantly higher phosphorylation of Akt, mTOR, and p70S6K compared to those infected with ΔMmpE strains (New Figures 5E and F). Moreover, the dual PI3K/mTOR inhibitor BEZ235 abolished the survival advantage of WT strains over ΔMmpE mutants in THP-1 macrophages (New Figure S6B and C). Collectively, these results support that MmpE activates the PI3K–Akt–mTOR signaling pathway to enhance bacterial survival within the host.

(8) The relevance of the NLS and the phosphatase activity is not completely clear in the CFU assays and in the gene expression data. Firstly, there needs to be immunoblot data provided for the expression and secretion of the NLS-deficient and phosphatase mutants. Secondly, CFU data in Figure 3A, C, and E must consistently include both the WT and ∆mmpE strain.

We thank the reviewer for the comment. We have now added immunoblot analysis for expression and secretion of MmpE mutants. The result show that NLS-deficient and phosphatase mutants can detected in supernatant (New Figure S1C). Additionally, we have revised Figures 3A, 3C, and 3E to consistently include both the WT and ΔMmpE strains in the CFU assays (Figures 3A, 3C, and 3E).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The authors should attempt to address the following comments:

(1) Please perform densitometric analysis for the western blot shown in Figure 1E.

We sincerely thank the reviewer for the suggestion. In the updated manuscript, we have performed densitometric analysis of the western blot shown in New Figure 1F and G.

(2) Is it possible to measure the protein levels for MmpE in lysates prepared from infected macrophages.

We thank the reviewer for the comment. In the revised manuscript, we performed immunoblot analysis to measure MmpE levels in lysates from infected macrophages. The results demonstrated that wild-type MmpE was present in both the cytoplasmic and nuclear fractions during infection in THP-1 cells (New Figure S1D).

(3) The authors should perform circular dichroism studies to compare the secondary structure of wild type and mutant proteins (in particular MmpEHis348 and MmpEAsn359.

We thank the reviewer for this valuable suggestion. We agree that circular dichroism spectroscopy could provide useful information in comparison of the differences on the secondary structures. However, due to the technical limitations, we instead compared the structures of wild-type MmpE and the His348 and Asn359 mutant proteins predicted by AlphaFold. These structural models showed almost no differences in secondary structures between the wild-type and mutants (Figure S1B).

(4) The authors should perform more experiments to determine the binding motif for MmpE in the promoter region of VDR.

We thank the reviewer for this suggestion. In the current study, we have identified the MmpE-binding motif within the promoter region of VDR using CUT&Tag sequencing. This prediction was further validated by ChIP-qPCR and EMSA (Figure 6). These complementary approaches collectively support the identification of a specific MmpE-binding motif and demonstrate its functional relevance. Such approach was acceptable in many publications (Wen et al., Commun Biol, 2020; Li et al., Nat Commun, 2022).

(5) Were the transcript levels of VDR also measured in the lung tissues of infected animals?

We thank the reviewer for this suggestion. In the revised manuscript, we have performed qRT-PCR to assess VDR transcript levels in the lung tissues of infected mice (New Figure S8B).

(6) How does MmpE regulate the expression of lysosome-associated genes?

We thank the reviewer for this question. Our experiments suggested that MmpE suppresses lysosomal maturation probably by activating the host PI3K–AKT–mTOR signaling pathway (New Figure 5E–I). This pathway is well established as a negative regulator of lysosome biogenesis and function (Yang et al., Signal Transduct Target Ther, 2020; Cui et al., Nature, 2023; Cui et al., Nature, 2025). During infection, THP-1 cells infected with the WT showed increased phosphorylation of Akt, mTOR, and p70S6K compared to those infected with ΔMmpE (New Figure S5C, New Figure 5E and F), and concurrently downregulated key lysosomal maturation markers, including TFEB, LAMP1, LAMP2, and multiple V-ATPase subunits (Figure 4G). Given that PI3K–AKT–mTOR signaling suppresses TFEB activity and lysosomal gene transcription (Palmieri et al., Nat Commun, 2017), we propose that MmpE modulates lysosome-associated gene expression and lysosomal function probably by PI3K–AKT–mTOR signaling pathway.

(7) Mice experiment:

(a) The methods section states that mice were infected intranasally, but the legend for Figure 6 states intratracheally. Kindly check?

(b) Supplementary Figure 7 - this is not clear. The legend says bacterial loads in spleens (CFU/g) instead of DNA expression, as shown in the figure.

(c) The data in Figure 6 and Figure S7 seem to be derived from the same experiment, but the number of animals is different. In Figure 6, it is n = 6, and in Figure S7, it is n=3.

We thank the reviewer for the comments.

(a) The infection was performed intranasally, and the figure legend for New Figure 7 has now been corrected.

(b) We adopted quantitative PCR method to measure bacterial DNA levels in the spleens of infected mice. We have now revised the legend.

(c) We have conducted new experiments where each experiment now includes six mice. The results are showed in Figure 7B and C, as well as in the new Figure S8.

(8) The authors should show individual values for various replicates in bar graphs (for all figures).

We thank the reviewer for this helpful suggestion. We have now updated all relevant bar graphs to include individual data points for each biological replicate.

(9) The authors should validate the relative levels of a few DEGs shown in Figure 3F, Figure 3G, and Figure S4C, in the lung tissues of mice infected with wild-type, mutant, and complemented strains.

We thank the reviewer for this suggestion. In the revised manuscript, we have performed qRT-PCR to validate the expression levels of selected DEGs, including inflammation-related and lysosome-associated genes, in lung tissues from mice infected with wild-type, mutant, and complemented strains (New Figure S8C-H).

(10) Did the authors perform an animal experiment using a mutant strain complemented with the phosphatase-deficient MmpE (Comp-MmpE-H348AN359H)?

We appreciate the reviewer's comment. We agree that an additional animal experiment would be useful to assess the effects of the phosphatase. However, our study mainly focused on interpreting the function of the nuclear localization of MmpE during BCG infection. Additionally, we have assessed the role of the phosphatase of MmpE during infection with cell model (Figure 3E).

Minor comment:

The mutant strain should be verified by either Southern blot or whole genome sequencing.

We thank the reviewer for this comment. We verified deletion of mmpE gene by PCR method (Figure S3A-D) which was acceptable in many publications (Zhang et al., PLoS Pathog, 2020; Zhang et al., Nat Commun, 2022).

Reviewer #3 (Recommendations for the authors):

(1) Line 195: cytokine.

We thank the reviewer for the comments. We have now corrected it.

(2) Line 225: rewording required.

Corrected.

(3) Figure 4A. "No difference" instead of "No different".

Corrected.

(4) "KommpE" should be replaced with "∆mmpE strain" (∆=delta symbol).

Corrected.

(5) Supplementary Figure 7. The figure legend states CFU assays, but the y-axis and the graph seem to depict IS1081 quantification.

We thank the reviewer for the comment. The figure is based on IS1081 quantification using qRT-PCR, not CFU assays. We have now revised the legend for New Figure S8A.

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Reviewer #2 (Public review):

This manuscript by Carmona, Zagotta, and Gordon is generally well-written. It presents a crude and incomplete structural analysis of the voltage-gated proton channel based on measured FRET distances. The primary experimental approach is Förster Resonance Energy Transfer (FRET), using a fluorescent probe attached to a noncanonical amino acid. This strategy is advantageous because the noncanonical amino acid likely occupies less space than conventional labels, allowing more effective incorporation into the channel structure.

Fourteen individual positions within the channel were mutated for site-specific labeling, twelve of which yielded functional protein expression. These twelve labeling sites span discrete regions of the channel, including P1, P2, S0, S1, S2, S3, S4, and the dimer-connecting coiled-coil domain. FRET measurements are achieved using acridon-2-ylalanine (Acd) as the acceptor, with four tryptophan or four tyrosine residues per monomer serving as donors. In addition to estimating distances from FRET efficiency, the authors analyze full FRET spectra and investigate fluorescence lifetimes on the nanosecond timescale.

Despite these strengths, the manuscript does not provide a clear explanation of how channel structure changes during gating. While a discrepancy between AlphaFold structural predictions and the experimental measurements is noted, it remains unclear whether this mismatch arises from limitations of the model or from the experimental approach. No further structural analysis is presented to resolve this issue or to clarify the conformational states of the protein.

The manuscript successfully demonstrates that Acd can be incorporated at specific positions without abolishing channel function, and it is noteworthy that the reconstituted proteins function as voltage-activated proton channels in liposomes. The authors also report reversible zinc inhibition of the channel, suggesting that zinc induces structural changes in certain channel regions that can be reversed by EDTA chelation. However, this observation is not explored in sufficient depth to yield meaningful mechanistic insight.

Overall, while the study introduces an interesting labeling strategy and provides valuable methodological observations, the analysis appears incomplete. Additional structural interpretation and mechanistic insight are needed.

Major Points

(1) Tryptophan and tyrosine exhibit similar quantum yields, but their extinction coefficients differ substantially. Is this difference accounted for in your FRET analysis? Please clarify whether this would result in a stronger weighting of tryptophan compared to tyrosine.

(2) Is the fluorescence of acridon-2-ylalanine (Acd) pH-dependent? If so, could local pH variations within the channel environment influence the probe's photophysical properties and affect the measurements?

(3) Several constructs (e.g., K125Tag, Y134Tag, I217Tag, and Q233Tag) display two bands on SDS-PAGE rather than a single band. Could this indicate incomplete translation or premature termination at the introduced tag site? Please clarify.

(4) In Figure 5F, the comparison between predicted FRET values and experimentally determined ratio values appears largely uninformative. The discussion on page 9 suggests either an inaccurate structural model or insufficient quantification of protein dynamics. If the underlying cause cannot be distinguished, how do the authors propose to improve the structural model of hHV1 or better describe its conformational dynamics?

(5) Cu²⁺, Ru²⁺, and Ni²⁺ are presented as suitable FRET acceptors for Acd. Would Zn²⁺ also be expected to function as an acceptor in this context? If so, could structural information be derived from zinc binding independently of Trp/Tyr?

(6) The investigated structure is most likely dimeric. Previous studies report that zinc stabilizes interactions between hHV1 monomers more strongly than in the native dimeric state. Could this provide an explanation for the observed zinc-dependent effects? Additionally, do the detergent micelles used in this study predominantly contain monomers or dimers?

(7) hHV1 normally inserts into a phospholipid bilayer, as used in the reconstitution experiments. In contrast, detergent micelles may form monolayers rather than bilayers. Could the authors clarify the nature of the micelles used and discuss whether the protein is expected to adopt the same fold in a monolayer environment as in a bilayer?

[Paragraph-level] PMCID: PMC5491373 Section: RESULTS PassageIndex: 29

Evidence Type(s): Functional

Justification: Functional: The passage discusses how the variant Lys48 affects the molecular function of PTENL320S by influencing its nuclear localization, indicating a change in biochemical activity related to polyubiquitination.

Gene→Variant (gene-first): 5728:Lys48

Genes: 5728

Variants: Lys48

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Wu et al. uses endogenous bruchpilot expression in a cell-type-specific manner to assess synaptic heterogeneity in adult Drosophila melanogaster mushroom body output neurons. The authors performed genomic on locus tagging of the presynaptic scaffold protein bruchpilot (BRP) with one part of splitGFP (GFP11) using the CRISPR/Cas9 methodology and co-expressed the other part of splitGFP (GFP1-10) using the GAL4/UAS system. Upon expression of both parts of splitGFP, fluorescent GFP is assembled at the N-terminus of BRP, exactly where BRP is endogenously expressed in active zones. For manageable analysis, a high-throughput pipeline was developed. This analysis evaluated parameters like location of BRP clusters, volume of clusters, and cluster intensity as a direct measure of the relative amount of BRP expression levels on site, using publicly available 3D analysis tools that are integrated in Fiji. Analysis was conducted for different mushroom body cell types in different mushroom body lobes using various specific GAL4 drivers. To test this new method of synapse assessment, Wu et al. performed an associative learning experiment in which an odor was paired with an aversive stimulus and found that, in a specific time frame after conditioning, the new analysis solidly revealed changes in BRP levels at specific synapses that are associated with aversive learning.

Strengths:

Expression of splitGFP bound to BRP enables intensity analysis of BRP expression levels as exactly one GFP molecule is expressed per BRP. This is a great tool for synapse assessment. This tool can be widely used for any synapse as long as driver lines are available to co-express the other part of splitGFP in a cell-type-specific manner. As neuropils and thus the BRP label can be extremely dense, the analysis pipeline developed here is very useful and important. The authors have chosen an exceptionally dense neuropil - the mushroom bodies - for their analysis and convincingly show that BRP assessment can be achieved with such densely packed active zones. The result that BRP levels change upon associative learning in an experiment with odor presentation paired with punishment is likewise convincing, and strongly suggests that the tool and pipeline developed here can be used in an in vivo context.

Weaknesses:

Although BRP is an important scaffold protein and its expression levels were associated with function and plasticity, I am still somewhat reluctant to accept that synapse structure profiling can be inferred from only assessing BRP expression levels and BRP cluster volume. Also, is it guaranteed that synaptic plasticity is not impaired by the large GFP fluorophore? Could the GFP10 construct that is tagged to BRP in all BRP-expressing cells, independent of GAL4, possibly hamper neuronal function? Is it certain that only active zones are labeled? I do see that plastic changes are made visible in this study after an associative learning experiment with BRP intensity and cluster volume as read-out, but I would be reassured by direct measurement of synaptic plasticity with splitGFP directly connected to BRP, maybe at a different synapse that is more accessible.

We appreciate the reviewer’s comments. In the revised manuscript, we have clarified that Brp is an important, but not the only player in the active zone. We have included new data to demonstrate that split-GFP tagging does not severely affect the localization and plasticity of Brp and the function of synapses by showing: (1) nanoscopic localization of Brp::rGFP using STED imaging; (2) colocalization between Brp::rGFP and anti-Brp signals/VGCCs; (3) activity-dependent Brp remodeling in R8 photoreceptors; (4) no defect in memory performance when labeling Brp::rGFP in KCs; These four lines of additional evidence further corroborate our approach to characterize endogenous Brp as a proxy of active zone structure.

Reviewer #2 (Public review):

Summary:

The authors developed a cell-type specific fluorescence-tagging approach using a CRISPR/Cas9 induced spilt-GFP reconstitution system to visualize endogenous Bruchpilot (BRP) clusters as presynaptic active zones (AZ) in specific cell types of the mushroom body (MB) in the adult Drosophila brain. This AZ profiling approach was implemented in a high-throughput quantification process, allowing for the comparison of synapse profiles within single cells, cell types, MB compartments, and between different individuals. The aim is to analyse in more detail neuronal connectivity and circuits in this centre of associative learning. These are notoriously difficult to investigate due to the density of cells and structures within a cell. The authors detect and characterize cell-type-specific differences in BRP-dependent profiling of presynapses in different compartments of the MB, while intracellular AZ distribution was found to be stereotyped. Next to the descriptive part characterizing various AZ profiles in the MB, the authors apply an associative learning assay and detect consequent AZ re-organisation.

Strengths:

The strength of this study lies in the outstanding resolution of synapse profiling in the extremely dense compartments of the MB. This detailed analysis will be the entry point for many future analyses of synapse diversity in connection with functional specificity to uncover the molecular mechanisms underlying learning and memory formation and neuronal network logics. Therefore, this approach is of high importance for the scientific community and a valuable tool to investigate and correlate AZ architecture and synapse function in the CNS.

Weaknesses:

The results and conclusions presented in this study are, in many aspects, well-supported by the data presented. To further support the key findings of the manuscript, additional controls, comments, and possibly broader functional analysis would be helpful. In particular:

(1) All experiments in the study are based on spilt-GFP lines (BRP:GFP11 and UAS-GFP1-10).The Materials and Methods section does not contain any cloning strategy (gRNA, primer, PCR/sequencing validation, exact position of tag insertion, etc.) and only refers to a bioRxiv publication. It might be helpful to add a Materials and Methods section (at least for the BRP:GFP11 line). Additionally, as this is an on locus insertion the in BRP-ORF, it needs a general validation of this line, including controls (Western Blot and correlative antibody staining against BRP) showing that overall BRP expression is not compromised due to the GFP insertion and localizes as BRP in wild type flies, that flies are viable, have no defects in locomotion and learning and memory formation and MB morphology is not affected compared to wild type animals.

We thank the reviewer for suggesting these important validations. We included details of the design of the construct and insertion site to the Methods section, performed several new experiments to validate the split-GFP tagging of Brp, and present the data in the revision.

First, to examine whether the transcription of the brp gene is unaffected by the insertion of GFP₁₁, we conducted qRT-PCR to compare the brp mRNA levels between brp::GFP₁₁, UAS-GFP1-10 and UAS-GFP1-10 and found no difference (Figure 1 - figure supplement 1A).

To further verify the effect of GFP₁₁ tagging at the protein level, we performed anti-Brp (nc82) immunohistochemistry of brains where GFP is reconstituted pan-neuronally. We found unaltered neuropile localization of nc82 signals (Figure 1 - figure supplement 1C). In presynaptic terminals of the mushroom body calyx, we found integration of Brp::rGFP to nc82 accumulation (Figure 1D). We performed super-resolution microscopy to verify the configuration of Brp::rGFP and confirmed the donut-shape arrangement of Brp::rGFP in the terminals of motor neurons (see Wu, Eno et al., 2025 PLOS Biology), corroborating the nanoscopic assembly of Brp::rGFP at active zones (Kittel et al., 2006 Science).

Furthermore, co-expression of RFP-tagged voltage-gated calcium channel alpha subunit Cacophony (Cac) and Brp::rGFP in PAM-γ5 dopaminergic neurons revealed strong presynaptic colocalization of their punctate clusters (Figure 1E), suggesting that rGFP tagging of Brp did not damage key protein assembly at active zones (Kawasaki et al., 2004 J Neuroscience; Kittel et al., Science).

These lines of evidence suggest that the localization of endogenous Brp is barely affected by the C-terminal GFP₁₁ insertion or GFP reconstitution therewith. This is in line with a large body of studies confirming that the N-terminal region and coiled-coil domains, but not the C-terminal, region of Brp are necessary and sufficient for active zone localization (Fouquet et al., 2009 J Cell Biol; Oswald et al., 2010 J Cell Biol; Mosca and Luo, 2014 eLife; Kiragasi et al., 2017 Cell Rep; Akbergenova et al., 2018 eLife; Nieratschker et al., 2009 PLoS Genet; Johnson et al., 2009 PLoS Biol; Hallermann et al., 2010 J Neurosci). We nevertheless report homozygous lethality and found the decreased immunoreactive signals in flies carrying the GFP₁₁ insertion (Figure 1 - figure supplement 1B).

For these reasons, we always use heterozygotes for all the experiments therefore there is no conspicuous defect in locomotion as reported in the original study (Wagh et al., 2005 Neuron). To functionally validate the heterozygotes, we measured the aversive olfactory memory performance of flies where GFP reconstitution was induced in Kenyon cells using R13F02-GAL4. We found that all these transgenes did not alter mushroom body morphology (Figure 7 - figure supplement 1) or memory performance as compared to wild-type flies (Figure 7 - figure supplement 2), suggesting the synapse function required for short-term memory formation is not affected by split-GFP tagging of Brp.

(2) Several aspects of image acquisition and high-throughput quantification data analysis would benefit from a more detailed clarification.

(a) For BRP cluster segmentation it is stated in the Materials and Methods state, that intensity threshold and noise tolerance were "set" - this setting has a large effect on the quantification, and it should be specified and setting criteria named and justified (if set manually (how and why) or automatically (to what)). Additionally, if Pyhton was used for "Nearest Neigbor" analysis, the code should be made available within this manuscript; otherwise, it is difficult to judge the quality of this quantification step.

(b) To better evaluate the quality of both the imaging analysis and image presentation, it would be important to state, if presented and analysed images are deconvolved and if so, at least one proof of principle example of a comparison of original and deconvoluted file should be shown and quantified to show the impact of deconvolution on the output quality as this is central to this study.

We thank the reviewer for suggesting these clarifications. We have included more description to the revised manuscript to clarify the setting of segmentation, which was manually adjusted to optimize the F-score (previous Figure 1D, now moved to Figure 1 -figure supplement 5). We have included the code used for analyzing nearest neighbor distance, AZ density and local Brp density in the revised manuscript (Supplementary file 1), together with a pre-processed sample data sheet (Supplementary file 2).

Regarding image deconvolution, we have clarified the differential use of deconvolved and not-deconvolved images in the revised manuscript. We have also included a quantitative evaluation of Richardson-Lucy iterative deconvolution (Figure 1 - figure supplement 4). We used 20 iterations due to only marginal FWHM improvement beyond this point (Figure 1 - figure supplement 4).

(3) The major part of this study focuses on the description and comparison of the divergent synapse parameters across cell-types in MB compartments, which is highly relevant and interesting. Yet it would be very interesting to connect this new method with functional aspects of the heterogeneous synapses. This is done in Figure 7 with an associative learning approach, which is, in part, not trivial to follow for the reader and would profit from a more comprehensive analysis.

(a) It would be important for the understanding and validation of the learning induced changes, if not (only) a ratio (of AZ density/local intensity) would be presented, but both values on their own, especially to allow a comparison to the quoted, previous AZ remodelling analysis quantifying BRP intensities (ref. 17, 18). It should be elucidated in more detail why only the ratio was presented here.

We thank the reviewer for the suggestion on the presentation of learning-induced Brp remodeling. The reported values in Figure 7C are the correlation coefficient of AZ density and local intensity in each compartment, but not the ratio. These results suggest that subcompartment-sized clusters of AZs with high Brp accumulation (Figure 6) undergo local structural remodeling upon associative learning (Figure 7). For clarity, we have included a schematic of this correlation and an example scatter plot to Figure 6. Unlike the previous studies (refs 17 and 18), we did not observe robust learning-dependent changes in the Brp intensity, possibly due to some confounding factors such as overall expression levels and conditioning protocols as described in the previous and following points, respectively.

(b) The reason why a single instead of a dual odour conditioning was performed could be clarified and discussed (would that have the same effects?).

(c) Additionally, "controls" for the unpaired values - that is, in flies receiving neither shock nor odour - it would help to evaluate the unpaired control values in the different MB compartments.

We use single odor conditioning because it is the simplest way to examine the effect of odor-shock association by comparing the paired and unpaired group. Standard differential conditioning with two odors contains unpaired odor presentation (CS-) even in the ‘paired’ group. We now show that single-odor conditioning induces memory that lasts one day as in differential conditioning (Figure 7B; Tully and Quinn, J Comp Phys A 1985).

(d) The temporal resolution of the effect is very interesting (Figure 7D), and at more time points, especially between 90 and 270 min, this might raise interesting results.

The sampling time points after training was chosen based on approximately logarithmic intervals, as the memory decay is roughly exponential (Figure 7B). This transient remodeling is consistent with the previous studies reporting that the Brp plasticity was short-lived (Zhang et al., 2018 Neuron; Turrel et al., 2022 Current Biol).

(e) Additionally, it would be very interesting and rewarding to have at least one additional assay, relating structure and function, e.g. on a molecular level by a correlative analysis of BRP and synaptic vesicles (by staining or co-expression of SV-protein markers) or calcium activity imaging or on a functional level by additional learning assays.

We thank the reviewer for raising this important point. We have performed calcium imaging of KC presynaptic terminals to correlate the structure and function in another study (see Figure 2 in Wu, Eno et al., 2025 PLOS Biology for more detail). The basal presynaptic calcium pattern along the γ compartments is strikingly similar to the compartmental heterogeneity of Brp accumulation (see also Figure 2 in this study). Considering colocalization of other active-zone components, such as Cac (Figure 1E), we propose that the learning-induced remodeling of local Brp clusters should transiently modulate synaptic properties.

As a response to other reviewers’ interest, we used Brp::rGFP to measure different forms of Brp-based structural plasticity upon constant light exposure in the photoreceptors and upon silencing rab3 in KCs. Since these experiments nicely reproduced the results of previous studies (Sugie et al., Neuron 2013; Graf et al., Neuron 2009), we believe the learning-induced plasticity of Brp clustering in KCs has a transient nature.

Reviewer #3 (Public review):

Summary:

The authors develop a tool for marking presynaptic active zones in Drosophila brains, dependent on the GAL4 construct used to express a fragment of GFP, which will incorporate with a genome-engineered partial GFP attached to the active zone protein bruchpilot - signal will be specific to the GAL4-expressing neuronal compartment. They then use various GAL4s to examine innervation onto the mushroom bodies to dissect compartment-specific differences in the size and intensity of active zones. After a description of these differences, they induce learning in flies with classic odour/electric shock pairing and observe changes after conditioning that are specific to the paired conditioning/learning paradigm.

Strengths:

The imaging and analysis appear strong. The tool is novel and exciting.

Weaknesses:

I feel that the tool could do with a little more characterisation. It is assumed that the puncta observed are AZs with no further definition or characterisation.

We performed additional validation on the tool, including (1) nanoscopic localization of Brp::rGFP using STED imaging; (2) colocalization between Brp::rGFP and anti-Brp signals/VGCCs (Figure 1D-E); 3) activity-dependent active zone remodeling in R8 photoreceptors (Figure 1F). These will be detailed in our point-by-point response below.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The authors keep stating, they profile or assess synaptic structure by analyzing BRP localization, cluster volume, and intensity. However, I do not think that BRP cluster volume and intensity warrant an educated statement about presynaptic structure as a whole. I do not challenge the usefulness of BRP cluster analysis for synapse evaluation, but as there are so many more players involved in synaptic function, BRP analysis certainly cannot explain it all. This should at least be discussed.

It is correct that Brp is not the only player in the active zone. We have included more discussion on the specific role of Brp (line 84 to 89) and other synaptic markers (line 250) and edited potentially misunderstanding text.

(2) I do see that changes in BRP expression were observed following associative learning, but is it certain, that synaptic plasticity is generally unaffected by the large GFP fluorophore? BRP is grabbing onto other proteins, both with its C- and N-termini. As the GFP is right before the stop codon, it should be at the N-terminus. How far could BRP function be hampered by this? Is there still enough space for other proteins to interact?

We thank the reviewer for sharing the concerns. We here provided three lines of evidence to demonstrate that the Brp assembly at active zones required for synaptic plasticity is unaffected by split-GFP tagging.

First, we assessed olfactory memory of flies that have Brp::rGFP labeled in Kenyon cells and found the performance comparable to wild-type (Figure 7 - figure supplement 2), suggesting the Brp function required for olfactory memory (Knapek et al., J Neurosci 2011) is unaffected by split-GFP tagging.

Second, we measured Brp remodeling in photoreceptors induced by constant light exposure (LL; Sugie et al., 2015 Neuron). Consistent with the previous study, we found that LL decreased the numbers of Brp::rGFP clusters in R8 terminals in the medulla, as compared to constant dark condition (DD). This result validates the synaptic plasticity involving dynamic Brp rearrangement in the photoreceptors. We have included this result into the revised manuscript (Figure 1F).

To further validate protein interaction of Brp::rGFP, we focused on Rab3, as it was previously shown to control Brp allocation at active zones (Graf et al., 2009 Neuron). To this end, we silenced rab3 expression in Kenyon cells using RNAi and measured the intensity of Brp::rGFP clusters in γ Kenyon cells. As previously reported in the neuromuscular junction, we found that rab3 knock-down increased Brp::rGFP accumulation to the active zones, suggesting that Brp::rGFP represents the interaction with Rab3. We have included all the new data to the revised manuscript (Figure 1 - figure supplement 3).

(3) It may well be that not only active-zone-associated BRP is labeled but possibly also BRP molecules elsewhere in the neuron. I would like to see more validation, e.g., the percentage of tagged endogenous BRP associated with other presynaptic proteins.

To answer to what extent Brp::rGFP clusters represent active zones, we double-labelled Brp::rGFP and Cac::tdTomato (Cacophony, the alpha subunit of the voltage-gated calcium channels). We found that 97% of Brp::rGFP clusters showed co-localization with Cac::tdTomato in PAM-γ5 dopamine neurons terminals (Figure 1E), suggesting most Brp::rGFP clusters represent functional AZs.

(4) Z-size is ~200 nm, while x/y pixel size is ~75 nm during acquisition. How far down does the resolution go after deconvolution?

The Z-step was 370 nm and XY pixel size was 79 nm for image acquisition. We performed 20 iterations of Richarson-Lucy deconvolution using an empirical point spread function (PSF). We found that the effect of deconvolution on the full-width at half maximum (FWHM) of Brp::rGFP clusters improves only marginally beyond 20 iterations, when the XY FWHM is around 200 nm and the XZ FWHM is around 450 nm (Figure 1 - figure supplement 4).

(5) Figure Legend 7: What is a "cytoplasm membrane marker"? Does this mean membrane-bound tdTom is sticking into the cytoplasm?

We apologize for the typo and have corrected it to “plasma membrane marker”.

(6) At the end of the introduction: "characterizing multiple structural parameters..." - which were these parameters? I was under the assumption that BRP localization, cluster volume, and intensity were assessed. I do not see how these are structural parameters. Please define what exactly is meant by "structural parameters".

We apologize for the confusion. By "structural parameters”, we indeed referred to the volume, intensity and molecular density of Brp::rGFP clusters. We have revised the sentence to “Characterizing the distinct parameters and localization of Brp::rGFP cluster.”

(7) Next to last sentence of the introduction: "Characterizing multiple structural parameters revealed a significant synaptic heterogeneity within single neurons and AZ distribution stereotypy across individuals." What do the authors mean by "significant synaptic heterogeneity"?

By “synaptic heterogeneity”, we refer to the intracellular variability of active zone cytomatrices reported by Brp clusters. For instance, the intensities of Brp::rGFP clusters within Kenyon cell subtypes were variable among compartments (Figure 2). Intracellular variability of the Brp concentration of individual active zones was higher in DPM and APL neurons than Kenyon cells (Figure 3). These variabilities demonstrate intracellular synaptic heterogeneity. We have revised the sentence to be more specific to the different characters of Brp clusters.

(8) I do not understand the last sentence of the introduction. "These cell-type-specific synapse profiles suggest that AZs are organized at multiple scales, ranging from neighboring synapses to across individuals." What do the authors mean by "ranging from neighboring synapses to across individuals"? Does this mean that even neighboring synapses in the same cell can be different?

We have revised the sentence to “These cell-type-specific synapse profiles suggest that AZs are spatially organized at multiple scales, ranging from interindividual stereotypy to neighboring synapses in the same cells.”

By “neighboring synapses", we refer to the nearest neighbor similarity in Brp levels in some cell-types (Figure 6A-C), and also the sub-compartmental dense AZ clusters with high Brp level in Kenyon cells (Figure 6D-H). By “across individuals”, we refer to the individually conserved active zone distribution patterns in some neurons (Figure 5).

(9) The title talks about cell-type-specific spatial configurations. I do not understand what is meant by "spatial configurations"? Do you mean BRP cluster volume? I think the title is a little misleading.

By “spatial configuration”, we refer to the arrangement of Brp clusters within individual mushroom body neurons. This statement is based on our findings on the intracellular synaptic heterogeneity (see also response to comment #7). We have streamlined the text description in the revised manuscript for clarity.

Reviewer #2 (Recommendations for the authors):

(1) For Figure 3A: exemplary two AZs are compared here, a histogram comparing more AZs would aid in making the point that in general, AZ of similar size have different BRP level (intensities) and how much variation exists.

We have included histograms for Brp::rGFP intensity and cluster volumes to Figure 3 in the revised manuscript.

(2) Line 52: "endogenous synapses" is a confusing term; it's probably meant that the protein levels within the synapse are endogenous and not overexpressed. 

We apologize for the confusion and have revised the term to “endogenous synaptic proteins.”

(3) It is not clear from the Materials and Methods section, whether and where deconvolved or not-deconvolved images were used for the quantification pipeline. Please comment on this. 

We have now revised the Method section to clarify how deconvolved or not-deconvolved images were differently used in the pipeline.

(4) Line 664 (C) not bold.

We have corrected the error.

(5) 725 "Files" should be Flies.

We have corrected the error.

(6) 727 two times "first".

We have corrected the error.

(7) Figure 7. All (A) etc., not bold - there should be consistent annotation. 

We want to thank the reviewer for the detailed proof and have corrected all the errors spotted.

Reviewer #3 (Recommendations for the authors):

(1) Has there been an expression of the construct in a non-neuronal cell? Astrocyte-like cell? Any glia? As some sort of control for background and activity?

As the reviewer suggested, we verified the neuronal expression specificity of Brp::rGFP. Using R86E01-GAL4 and Amon-GAL4, we compared Brp::rGFP in astrocyte-like glia and neuropeptide-releasing neurons. We found no Brp::rGFP puncta in the neuropils in astrocyte-like glia compared to neurons, suggesting Brp::rGFP is specific to neurons. We have included this new dataset to the revised manuscript (Figure 1 - figure supplement 2).

(2) Similarly, expression of the construct co-expressed with a channelrhodopsin, and induction of a 'learning'-like regime of activity, similarly in a control type of experiment, expression of an inwardly rectifying channel (e.g. Kir2.1) to show that increases in size of the BRP puncta are truly activity dependent? The NMJ may be an optimal neuron to use to see the 'donut' structures of the AZs and their increase with activity. Also, are these truly AZs we are seeing here? Perhaps try co-expressing cacophony-dsRed? If the GFP Puncta are active zones, then they should be surrounded by cacophony.

We would like to clarify that we did not find Brp::rGFP size increase upon learning. Instead, we demonstrated that associative training transiently remodelled sub-compartment-sized AZ “hot spots” in Kenyon cells, indicated by the correlation of local intensity and AZ density (Figure 6-7).

To demonstrate split-GFP tagging does not affect activity-dependent plasticity associated with Brp, we measured Brp remodeling in photoreceptors induced by constant light exposure (LL; Sugie et al., 2015 Neuron). Consistent with the previous study, we found that LL decreased the numbers of Brp::rGFP clusters in R8 terminals in the medulla, as compared to constant dark condition (DD). This result validates the synaptic plasticity involving dynamic Brp rearrangement in the photoreceptors (Figure 1F).

As the reviewer suggested, we performed the STED microscopy for the larval motor neuron and confirmed the donut-shape arrangement of Brp::rGFP (Wu, Eno et al., PLOS Biol 2025).

Also following the reviewer’s suggestion, we double-labelled Brp::rGFP and Cac::tdTomato (Cacophony, the alpha subunit of the voltage-gated calcium channels). We found that 97% Brp::rGFP clusters showed co-localization with Cac::tdTomato in PAM-γ5 dopamine neurons terminals (Figure 1E), suggesting most Brp::rGFP clusters represent functional AZs.

(3) In the introduction: Intro, a sentence about BRP - central organiser of the active zone, so a key regulator of activity.

We have included a few more sentences about the role Brp in the active zones to the revised manuscript.

(4) Figure 1 E, line 650 'cite the resource here'. 

We thank the reviewer for pointing out the error and we have corrected it.

(5) Many readers may not be MB aficionados, and to make the data more accessible, perhaps use a cartoon of an MB with the cell bodies of the neurons around the MB expressing the constructs highlighted so that the reader can have a wider idea of the anatomy in relation to the MB.

We appreciate these comments and have appended cartoons of the MB to figures to help readers understand the anatomy.

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 would like to thank all the reviewers for their comments and suggestions.

Please find below our point-by-point response to the Reviewers' comments, which details the corrections already made and outlines the planned revisions, experiments, and analyses.

Reviewer 1

Major comments:

• Reviewer 1 commented that the 'manuscript would greatly benefit from having someone spend time on the figures, and associated text, to ensure they are fully comprehensible'. We agree wholeheartedly with the reviewer and apologise. We have now revisited the text, figures, and associated figure legends to ensure that they are more easily accessible and fully comprehensible to readers from across disciplines. This includes adding labels to point out specific anatomical features on images, and ensuring figures and text align. Further specific examples are included in the points below.
• In response to concerns raised by Reviewer 1 relating to: Figure 1 and the lack of figure citations; 'the persistence of mCherry in the H2B Fucci'; how mCherry seems to persist longer in H1 (compare Figs 1D and 1G)':
• We apologise for the lack of figure citations in the text. We have now reworked the figures relating to the constructs (original Figures 1 and S1) and have made these Figures 1, 2 and S1 in our updated version.
• Figure 1 is now an introductory background figure which illustrates the differences between Fucci(SA) and Fucci(CA) reporters, with additional details provided in the associated legend, and call outs to the figure starting in the introduction.
• Regarding 'the persistence of mCherry in the H2B Fucci', what we are trying to articulate is that the mCherry degradation that we observed in the Fucci(2A) expressing DF1 cells extended beyond the end of S phase and into G2/M, compared with what would be expected (Revised Figure 2H, arrows).
• We have now replaced these montages with a more representative example. Additionally, the new images (Figures 2C and 2G) are synchronised (both starting at G2/M), restricted to a single cell cycle, are larger in size, and have the cell cycle stage labelled. We believe these changes will aid interpretation.
• Specifically relating to the lack of labelling in Figure 3A, we agree that this figure was not labelled sufficiently, and neither was there enough detail included in the text or figure legend for readers to follow easily and make their own conclusions. We have now added additional labels to this figure, broken the figure down into more panels (Figures 4A-4D in revised manuscript), and included more detailed descriptions in the associated figure legend and text.
• We thank the reviewer for making the important point that it is 'hard to know where the biosensor is reporting patterns that are already well established (eg neural tube), and where the biosensor is reporting patterns that are novel - and if so, what these patterns are' which was made more challenging by insufficient references to previous studies.
• Firstly, as for the point above, we have now added labels to many of the panels (Figure 4 in revision), including highlighting features such as the non-proliferative dermal condensates and demarcating the proliferative retinal pigmented epithelium (Figures 4F and 4G in revision). Secondly, we have also now included additional references in the text, specifically relating to the neural tube, digits, and forming feathers, where our proliferation profiles are consistent with previous literature.
• With regards to the Reviewer's comment regarding the difficulty in drawing conclusions 'about cell cycle in different tissue layers without sectioning' in original Figure 3B we will include more sections of FuChi embryos which include structures such as mesenchymal condensates.
• To make our data on cell cycle stages as 'cells egress from the primitive streak, to form prechordal plate' clearer we have added additional labels to the figures (Figures 4B and 6E in revised manuscript). We will complement this adding sections of gastrulating FuChi embryos to further demonstrate the cell cycle status of cells that form the pre-chordal plates.

Minor comments

• We have added additional references relating to the data in original Figure 3 (now Figure 4 see above), and any new descriptions of known proliferation profiles that we include will have appropriate citations.
• In this current revision we have addressed figure call out issues, and added labels to enhance readability, clarity and data interpretation. Reviewer 2

Major comments

• Reviewer 2 rightly pointed out that the 'description of the bicistronic tandem-Fucci(CA) system in paragraph 6 is not consistent with what is described in the original bibliographic reference indicated by the authors'. We have now added additional text to properly explain the CDT1 probe dynamics, as per the cited manuscript, and also referenced the schematics to help readers.
• To address whether the FuChi model can be accurately 'used to study embryogenesis' and following up on the suggestion to 'indicate if the size of the embryos is comparable to the wildtype' we have now included size comparisons of FuChi and wild-type/non-transgenic embryos at mid (E9) and late (E18) gestational stages demonstrating that there is no significant difference between genotypes during embryogenesis (Figure 3D in revised manuscript). For all earlier stages, we did not see any developmental or size differences. We believe if there were any differences, these would be reflected in size at the mid and late gestational stages we analysed.
• Reviewer 2 made very valuable observations and suggestions regarding our data and interpretation of somitogenesis, specifically in response to our sentence saying that "the mesenchyme, which is predominantly in G1 as they undergo condensation". Furthermore, they noted that Supplementary Video 4 "shows distinct green fluorescence (S) in the presomitic mesoderm for the first hour or so, only then turning to magenta (G1)". We were asked to review the sentence/video to clarify if this is a significant finding or if this is not representative of their observations.
• We thank the reviewer for this suggestion. From looking again at our timelapse movies, and also analysing additional static images, we agree that presomitic mesoderm (PSM) does appear to be green (S phase), which then may transition to G1 as the somites form. To address this, we plan to quantify cell cycle status in the PSM on embryos to see if this is a significant finding.
• We hope this quantification of the PSM may also enable us to include discussion on how our findings relate to the Cell Cycle model for somitogenesis proposed in the Collier et al, 2000 paper suggested by the Reviewer.
• We agree with the Reviewer that "the fluorescence profiles in original Figure 4C do not seem similar regarding the Myc-tag epitope" and believe this difference is likely just a reflection of the part of the image we used. We will include a more representative image once we have repeated the staining.
• Reviewer 2 has asked for quantitative support for our fluorescence-based interpretations. We thank the reviewer for this suggestion and are now planning to perform quantitative analyses of different tissues (similar to our quantification in germ cells) and in embryos to support our observations. These will include the PSM (see above), neural tube, intestine, and early embryos (also see Reviewer 3 response for blastoderm quantification).
• Since our original submission, we have further refined our in situ hybridisation protocol on FuChi embryos (Figures 5A & B in revision), finding that strong reporter expression is maintained for all the fluorescent proteins of the H1-Fucci(CA)2 reporter. Therefore, the "notably fainter" appearance of the hGMNN-mVenus in Figure 4A from the first version of the paper was likely a result of the experimental protocol not being 100% optimal.
• *

Minor comments

• We have reordered the paragraphs relating to the different Fucci versions in the introduction as per the suggestions by the reviewer for better clarity.
• To address the issues with Fucci system nomenclatures which made reading difficult, we have now added a background figure (new Figure 1 in revised draft) which is cited in the introduction, made sure constructs are introduced appropriately, and ensured we are consistent with our nomenclature.
• Supplementary Figure lettering corrected.
• All figure panels are now mentioned in the main text, and the incorrect call outs noted by the Reviewer have been corrected
• Removed period and included clarifying statement in the figure legend relating to the comment regarding the extraembryonic region in Figure 5 (original) / Figure 6 (revised).
• Other issues raised relating to reference duplication and missing words have been resolved.
• We have corrected the legend of Figure 1 of the original paper, see related Reviewer 1 response provided above.

Reviewer #3

Minor comments

• We have corrected all the figure call outs (see responses to similar comments by Reviewers 1 and 2) to ensure that all data presented is accurately reported.
• We would like to thank the reviewer for suggesting modifications to the cell cycle montages (original figures 1D, 1G and 2F). We agree it would help the reader to enlarge the image, and therefore reduced the montage to include just one cell cycle, and have also included annotations of cell cycle stages in Figures 2C and 2G of the revised manuscript. We have also added some labels to Figure 3E (original figure 2F) and enlarged this.
• In response to Reviewer 3's comment regarding fluorescent intensity. We quantified fluorescence levels in multiple individual DF1 cells expressing either the H1.0-Fucci(CA)2 or H2B-Fucci(SA)2 reporters, and this is shown as the fluorescent index in Figures 2D, 2E, 2H and 2I of the revised manuscript, where reporter levels were measured across time. In terms of overall mean intensity levels of the reporters, we found the reporters to be comparable in brightness and have similar mean intensity levels across the cell populations in the flow cytometry data (Figures 2F and 2J).
• To enhance speedy interpretation, we will also process our supplementary videos to include annotations and arrows to highlight key cells and events (e.g. a cell undergoing mitosis).
• As recommended by Reviewer 3, we have now quantified cell cycle status in blastoderm cells, confirming that a high proportion are in the G2/M phase. We will include these data in the final revision, which will complement our planned quantification of cell cycle status in other tissues (see response to Reviewer 2).
• For our final revision, we will include higher magnification/zoomed in images of selected regions of the somites, neural tube (lumen) and retina (epithelium). Revisiting our images of the neural tube showed that dividing cells lumen did so in the perpendicular plane and we will include these images in our revision to provide further evidence of the fidelity of the FuChi reporter. We thank the reviewer for this excellent idea to show the efficacy of our system.
• To address the levels of proliferation in somites, we plan to generate a cropped video with a fixed ROI to enable proliferation in individual cells of the forming somites to be more readily visualised. This will be further complemented by the quantification of cell cycle status in forming somites (see responses to other reviewers).
• We have added lines to the discussion regarding the use of our reporter in other conventional model systems.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #2

Evidence, reproducibility and clarity

Summary:

This work presents a novel transgenic chicken model with fluorescent reporters that allow in vivo monitoring of the four phases of the cell cycle. To achieve this, the authors clearly identify the limitations of previous Fucci systems and developed an optimised reporter construct that overcomes the major technical challenges identified. Addition of epitope tags to cell cycle stage-specific markers further enables antibody detection in fixed tissues. Proof of concept is provided by live imaging of chick embryos in early developmental stages, evidencing dynamic cell cycle states in tissues and migrating cells.

Major comments:

1. Introduction: Description of the bicistronic tandem-Fucci(CA) system in paragraph 6 is not consistent with what is described in the original bibliographic reference indicated by the authors. Namely: "...accumulation of the CTD1 probe..." should be expected in the G1-S transition (not S-G2) and the yellow reporter should be expected in G2 and M phases (not S and G2, as described). Please review this portion of the text.
2. The authors state that "Of note, hatched FuChi chicks are initially smaller than wild type counterparts but grow at comparative rates and are fertile". If the model is to be used to study embryogenesis, it would be useful to indicate if the size of the embryos is comparable to the wildtype, at least for the major developmental stages mentioned in the manuscript.
3. When referring to somitogenesis, the authors state "...the mesenchyme, which is predominantly in G1 as they undergo condensation". Suppl Video 4, however, shows distinct green fluorescence (S) in the presomitic mesoderm for the first hour or so, only then turning to magenta (G1). The authors should review the sentence/video to clarify if this is a significant finding or if this is not representative of their observations.
4. (Optional) It would be interesting to describe if the authors' observations of cell cycle dynamics in the presomitic mesoderm support the proposed Cell Cycle model for somitogenesis (Collier et al., J.Theor.Biol.2000).
5. The fluorescence profiles in Figure 4C do not seem similar regarding the Myc-tag epitope (contrarily to what is stated). The authors should rephrase or revisit this image to clarify their findings.
6. Quantitative support for several fluorescence-based interpretations made throughout the manuscript. In some instances, conclusions are drawn from qualitative differences in signal intensity. For example, the statement in Fig. 4A that hGMNN-mVenus appears "notably fainter" than the other reporters. Incorporating simple quantitative analyses would strengthen these claims and ensure that observed differences reflect biological behaviour rather than technical or optical factors.

Minor comments:

1. Organization of the information in the Introduction: Paragraphs 3-5 introduce sequentially improved versions of the Fucci system. Then, paragraph 6 returns to the system described in the 4th paragraph. Authors should consider including paragraph 5 (description of Fucci4 and its limitations) just prior to the description of chickens as valuable developmental models (current paragraph 8) for clarity of the text.
2. Fucci system nomenclature. Many different Fucci systems are mentioned, but nomenclature consistency throughout the manuscript is lacking, which makes reading difficult. For example, the terms "Fucci(SA)2" and "Fucci(CA)2" should be defined in the introduction, as they are employed to describe the construction of the new biosensor in the following sections.
3. Some figure panels are not mentioned in the main text (for ex. Figures 1B and C, Figure 2C)
4. The legend of Figure 1 (D & G) mentions "denoted by *", but the * seems to be missing in the figure.
5. Supplementary Figure 1 has two D panels (and is missing the E).
6. In the main text, where it reads "...Flow cytometry analysis of three independent PGC lines... (Figures 2G & S2E)", S2E should be replaced by S1E.
7. In the Figure 4A legend, hCDT1-mVenus should be corrected to hCDT1-mcherry. Also, it is not clear why the authors state that "hGMNN-mVenus expression is notably fainter compared with hCDT1-mVenus and H1.0-mCerulean expression".
8. In Figure 5E, the optical sections "i" seem to pertain to the extraembryonic tissue/area opaca and not to anterior mesoderm, as stated in the figure legend. Also, there is a period between "prechordal plate" and "and" in the legend's last sentence.
9. Discussion: The last sentence of the third paragraph lacks "to" between "used" and "interrogate".
10. References 10 and 23 are identical.

Referee cross-commenting

I agree with all comments from reviewers 1 and 3

Significance

This is a beautiful paper, describing a long sought-after model system to study cell cycle dynamics in vivo. The methodological details are thorough, and the results obtained are clearly presented, highlighting the utility of the new model in various embryonic stages and tissues/organs.

This work is of pivotal importance to the developmental/stem cell biology community, as well as to the wider community that employs the chicken embryo as a preclinical model to assess therapeutic or teratogenic potential of biologically- or chemically-derived products.

My expertise is in chicken embryo development, namely gastrulation, somitogenesis and limb bud outgrowth.

It is always valuable to give the option to developers to use it how they want. The developer may want to use it without necessarily making it a user-controllable UI preference!!

• The article argues that answering the "What is your current/expected salary?" question with a single number is a strategic mistake that limits your earning potential.
• Giving a specific number early in the process creates an "anchor" that recruiters will use to keep the offer as low as possible.
• Instead of providing a number, the author suggests pivoting the conversation toward the value you bring to the role and the total compensation package.
• A key strategy is to ask for the company's budgeted range for the position first, which puts the onus on the employer to disclose their limits.
• If forced to give a range, ensure the bottom of your range is the minimum you would actually accept, while the top represents your "dream" scenario.
• The goal of salary discussions in early interviews should be to establish "alignment" rather than a final price tag.
• Delaying the specific salary talk until after you have "wowed" the team gives you more leverage, as they are now invested in hiring you specifically.

Hacker News Discussion

• Many commenters emphasize that while "not answering" is a common piece of advice, it can be impractical for those who lack extreme leverage or are in urgent need of work.
• A popular counter-strategy mentioned is to confirm the salary range during the very first recruiter call to avoid wasting hours on interviews for a role that cannot meet your financial requirements.
• Users suggested that if you do provide a number first, you should always include a disclaimer that you "look at the entire package holistically" (benefits, equity, PTO) to maintain flexibility for later negotiation.
• There is a consensus that once a final offer is made, you should almost always ask, "Is there any way you can come up a little bit from that?" as this simple question frequently results in a 5-10% bump with minimal risk.
• Some participants shared "pleasant surprise" stories where refusing to name a price led to offers significantly higher (+50% or more) than what they would have asked for.
• The discussion highlights a shift toward transparency, with many noting that asking for the "salary band" is becoming a standard and respected practice in tech hiring.

Author response:

The following is the authors’ response to the original reviews.

Public reviews:

Reviewer #1 (Public review):

Summary:

In this article, Kawanabe-Kobayashi et al., aim to examine the mechanisms by which stress can modulate pain in mice. They focus on the contribution of noradrenergic neurons (NA) of the locus coeruleus (LC). The authors use acute restraint stress as a stress paradigm and found that following one hour of restraint stress mice display mechanical hypersensitivity. They show that restraint stress causes the activation of LC NA neurons and the release of NA in the spinal cord dorsal horn (SDH). They then examine the spinal mechanisms by which LC→SDH NA produces mechanical hypersensitivity. The authors provide evidence that NA can act on alphaA1Rs expressed by a class of astrocytes defined by the expression of Hes (Hes+). Furthermore, they found that NA, presumably through astrocytic release of ATP following NA action on alphaA1Rs Hes+ astrocytes, can cause an adenosine-mediated inhibition of SDH inhibitory interneurons. They propose that this disinhibition mechanism could explain how restraint stress can cause the mechanical hypersensitivity they measured in their behavioral experiments.

Strengths:

(1) Significance. Stress profoundly influences pain perception; resolving the mechanisms by which stress alters nociception in rodents may explain the well-known phenomenon of stress-induced analgesia and/or facilitate the development of therapies to mitigate the negative consequences of chronic stress on chronic pain.

(2) Novelty. The authors' findings reveal a crucial contribution of Hes+ spinal astrocytes in the modulation of pain thresholds during stress.

(3) Techniques. This study combines multiple approaches to dissect circuit, cellular, and molecular mechanisms including optical recordings of neural and astrocytic Ca2+ activity in behaving mice, intersectional genetic strategies, cell ablation, optogenetics, chemogenetics, CRISPR-based gene knockdown, slice electrophysiology, and behavior.

Weaknesses:

(1) Mouse model of stress. Although chronic stress can increase sensitivity to somatosensory stimuli and contribute to hyperalgesia and anhedonia, particularly in the context of chronic pain states, acute stress is well known to produce analgesia in humans and rodents. The experimental design used by the authors consists of a single one-hour session of restraint stress followed by 30 min to one hour of habituation and measurement of cutaneous mechanical sensitivity with von Frey filaments. This acute stress behavioral paradigm corresponds to the conditions in which the clinical phenomenon of stress-induced analgesia is observed in humans, as well as in animal models. Surprisingly, however, the authors measured that this acute stressor produced hypersensitivity rather than antinociception. This discrepancy is significant and requires further investigation.

We thank the reviewer for evaluating our work and for highlighting both its strengths and weaknesses. As stated by the reviewer, numerous studies have reported acute stress-induced antinociception. However, as shown in a new additional table (Table S1) in which we have summarized previously published data using the acute restraint stress model employed in our present study, most studies reporting antinociceptive effects of acute restraint stress assessed behavioral responses to heat stimuli or formalin. This observation is consistent with the findings from our previous study (Uchiyama et al., Mol Brain, 2022 (PMID: 34980215)). The present study also confirms that acute restraint stress reduces behavioral responses to noxious heat (see also our response to Comment #2 below). In contrast to the robust and consistent antinociceptive effects observed with thermal stimuli, some studies evaluating behavioral responses to mechanical stimuli have reported stress-induced hypersensitivity (see Table S1), which aligns with our current findings. Taken together, these data support our original notion that the effects of acute stress on pain-related behaviors depend on several factors, including the nature, duration, and intensity of the stressor, as well as the sensory modality assessed in behavioral tests. We have incorporated this discussion and Table S1 into the revised manuscript (lines 344-353). Furthermore, we have slightly modified the text including the title, replacing "pain facilitation" with "mechanical pain hypersensitivity" to more accurately reflect our research focus and the conclusion of this study that LC^→SDH NAergic signaling to spinal astrocytes is required for stress-induced mechanical pain hypersensitivity. Finally, while mouse models of stress could provide valuable insights, the clinical relevance of stress-induced mechanical pain hypersensitivity remains to be elucidated and requires further investigation. We hope these clarifications address your concerns.

(2) Specifically, is the hypersensitivity to mechanical stimulation also observed in response to heat or cold on a hotplate or coldplate?

Thank you for your important comment. We have now conducted additional behavioral experiments to assess responses to heat using the hot-plate test. We found that mice subjected to restraint stress did not exhibit behavioral hypersensitivity to heat stimuli; instead, they displayed antinociceptive responses (Figure S2; lines 95-98). These results are consistent with our previous findings (Uchiyama et al., Mol Brain, 2022 (PMID: 34980215)) as well as numerous other reports (Table S1).

(3) Using other stress models, such as a forced swim, do the authors also observe acute stress-induced hypersensitivity instead of stress-induced antinociception?

As suggested by the reviewer, we conducted a forced swim test. We found that mice subjected to forced swimming, which has been reported to produce analgesic effects on thermal stimuli (Contet et al., Neuropsychopharmacology, 2006 (PMID: 16237385)), did not exhibit any changes in mechanical pain hypersensitivity (Figure S2; lines 98-99). Furthermore, a previous study demonstrated that mechanical pain sensitivity is enhanced by other stress models, such as exposure to an elevated open platform for 30 min (Kawabata et al., Neuroscience, 2023 (PMID: 37211084)). However, considering our data showing that changes in mechanosensory behavior induced by restraint stress depend on the duration of exposure (Figure S1), and that restraint stress also produced an antinociceptive effect on heat stimuli (Figure S2), stress-induced modulation of pain is a complex phenomenon influenced by multiple factors, including the stress model, intensity, and duration, as well as the sensory modality used for behavioral testing (lines 100-103).

(4) Measurement of stress hormones in blood would provide an objective measure of the stress of the animals.

A previous study has demonstrated that plasma corticosterone levels—a stress hormone—are elevated following a 1-hour exposure to restraint stress in mice (Kim et al., Sci Rep, 2018 (PMID: 30104581)), using a stress protocol similar to that employed in our current study. We have included this information with citing this paper (lines 104-105).

(5) Results:

(a) Optical recordings of Ca2+ activity in behaving rodents are particularly useful to investigate the relationship between Ca2+ dynamics and the behaviors displayed by rodents.

In the optical recordings of Ca²⁺ activity in LC neurons, we monitored mouse behavior during stress exposure. We have now included a video of this in the revised manuscript (video; lines 111-114).

(b) The authors report an increase in Ca2+ events in LC NA neurons during restraint stress: Did mice display specific behaviors at the time these Ca2+ events were observed such as movements to escape or orofacial behaviors including head movements or whisking?

By reanalyzing the temporal relationship between Ca²⁺ events and mouse behavior during stress exposure, we found that the Ca²⁺ transients and escape behaviors (struggling) occurred almost simultaneously (video). A similar temporal correlation is also observed in Ca²⁺ responses in the bed nucleus of the stria terminalis (Luchsinger et al., Nat Commun, 2021 (PMID: 34117229)). The video file has been included in the revised manuscript (video; lines 111-113, 552-553, 573-575).

Additionally, as described in the Methods section and shown in Figure S2 of the initial version (now Figure S3), non-specific signals or artifacts—such as those caused by head movements—were corrected (although such responses were minimal in our recordings).

(c) Additionally, are similar increases in Ca2+ events in LC NA neurons observed during other stressful behavioral paradigms versus non-stressful paradigms?

We appreciate the reviewer's valuable suggestion. Since the present, initial version of our manuscript focused on acute restraint stress, we did not measure Ca²⁺ events in LC-NA neurons in other stress models, but a recent study has shown an increase in Ca²⁺ responses in LC-NA neurons by social defeat stress (Seiriki et al., BioRxiv, https://www.biorxiv.org/content/10.1101/2025.03.07.641347v1).

(d) Neuronal ablation to reveal the function of a cell population.

This method has been widely used in numerous previous studies as an effective experimental approach to investigate the role of specific neuronal populations—including SDH-projecting LC-NA neurons (Ma et al., Brain Res, 2022 (PMID: 34929182); Kawanabe et al., Mol Brain, 2021 (PMID: 33971918))—in CNS function.

(e) The proportion of LC NA neurons and LC→SDH NA neurons expressing DTR-GFP and ablated should be quantified (Figures 1G and J) to validate the methods and permit interpretation of the behavioral data (Figures 1H and K). Importantly, the nocifensive responses and behavior of these mice in other pain assays in the absence of stress (e.g., hotplate) and a few standard assays (open field, rotarod, elevated plus maze) would help determine the consequences of cell ablation on processing of nociceptive information and general behavior.

As suggested, we conducted additional experiments to quantitatively analyze the number of LC^→SDH-NA neurons. We used WT mice injected with AAVretro-Cre into the SDH (L4 segment) and AAV-FLEx[DTR-EGFP] into the LC. In these mice, 4.4% of total LC-NA neurons [positive for tyrosine hydroxylase (TH)] expressed DTR-GFP, representing the LC^→SDH-NA neuronal population (Figure S4; lines 126-127). Furthermore, treatment with DTX successfully ablated the DTR-expressing LC^→SDH-NA neurons. Importantly, the neurons quantified in this analysis were specifically those projecting to the L4 segment of the SDH; therefore, the total number of SDH-projecting LC-NA neurons across all spinal segments is expected to be much higher.

We also performed the rotarod and paw-flick tests to assess motor function and thermal sensitivity following ablation of LC^→SDH-NA neurons. No significant differences were observed between the ablated and control groups (Figure S5; lines 131-134), indicating that ablation of these neurons does not produce non-specific behavioral deficits in motor function or other sensory modalities.

(f) Confirmation of LC NA neuron function with other methods that alter neuronal excitability or neurotransmission instead of destroying the circuit investigated, such as chemogenetics or chemogenetics, would greatly strengthen the findings. Optogenetics is used in Figure 1M, N but excitation of LCLC^→SDH NA neuron terminals is tested instead of inhibition (to mimic ablation), and in naïve mice instead of stressed mice.

We appreciate the reviewer’s comment. The optogenetic approach is useful for manipulating neuronal excitability; however, prolonged light illumination (> tens of seconds) can lead to undesirable tissue heating, ionic imbalance, and rebound spikes (Wiegert et al., Neuron, 2017 (PMID: 28772120)), making it difficult to apply in our experiments, in which mice are exposed to stress for 60 min. For this reason, we decided to employ the cell-ablation approach in stress experiments, as it is more suitable than optogenetic inhibition. In addition, as described in our response to weakness (1)-a) by Reviewer 3 (Public review), we have now demonstrated the specific expression of DTRs in NA neurons in the LC, but not in A5 or A7 (Figure S4; lines 127-128), confirming the specificity of LCLC^→SDH-NAergic pathway targeting in our study. Chemogenetics represent another promising approach to further strengthen our findings on the role of LCLC^→SDH-NA neurons, but this will be an important subject for future studies, as it will require extensive experiments to assess, for example, the effectiveness of chemogenetic inhibition of these neurons during 60 min of restraint stress, as well as optimization of key parameters (e.g., systemic DCZ doses).

(g) Alpha1Ars. The authors noted that "Adra1a mRNA is also expressed in INs in the SDH".

The expression of α_1ARs in inhibitory interneurons in the SDH is consistent with our previous findings (Uchiyama et al., Mol Brain, 2022 (PMID: 34980215)) as well as with scRNA-seq data (http://linnarssonlab.org/dorsalhorn/, Häring et al., Nat Neurosci, 2018 (PMID: 29686262)).

(h) The authors should comprehensively indicate what other cell types present in the spinal cord and neurons projecting to the spinal cord express alpha1Ars and what is the relative expression level of alpha1Ars in these different cell types.

According to the scRNA-seq data (https://seqseek.ninds.nih.gov/genes, Russ et al., Nat Commun, 2021 (PMID: 34588430); http://linnarssonlab.org/dorsalhorn/, Häring et al., Nat Neurosci, 2018 (PMID: 29686262)), we confirmed that α_1ARs are predominantly expressed in astrocytes and inhibitory interneurons in the spinal cord. Also, an α_1AR-expressing excitatory neuron population (Glut14) expresses Tacr1, GPR83, and Tac1 mRNAs, markers that are known to be enriched in projection neurons of the SDH. This raises the possibility that α_1A Rs may also be expressed in a subset of projection neurons, although further experiments are required to confirm this. In DRG neurons, α_1AR expression was detected to some extent, but its level seems to be much lower than in the spinal cord (http://linnarssonlab.org/drg/ Usoskin et al., Nat Neurosci, 2015 (PMID: 25420068)). Consistent with this, primary afferent glutamatergic synaptic transmission has been shown to be unaffected by α_1AR agonists (Kawasaki et al., Anesthesiology, 2003 (PMID: 12606912); Li and Eisenach, JPET, 2001 (PMID: 11714880)). This information has been incorporated into the Discussion section (lines 317-319).

(i) The conditional KO of alpha1Ars specifically in Hes5+ astrocytes and not in other cell types expressing alpha1Ars should be quantified and validated (Figure 2H).

We have previously shown a selective KO of α_1AR in Hes5⁺ astrocytes in the same mouse line (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)). This information has been included in the revised text (line 166-167).

(j) Depolarization of SDH inhibitory interneurons by NA (Figure 3). The authors' bath applied NA, which presumably activates all NA receptors present in the preparation.

We believe that the reviewer’s concern may pertain to the possibility that NA acts on non-Vgat⁺ neurons, thereby indirectly causing depolarization of Vgat⁺ neurons. As described in the Method section of the initial version, in our electrophysiological experiments, we added four antagonists for excitatory and inhibitory neurotransmitter receptors—CNQX (AMPA receptor), MK-801 (NMDA receptor), bicuculline (GABA_A receptor), and strychnine (glycine receptor)—to the artificial cerebrospinal fluid to block synaptic inputs from other neurons to the recorded Vgat⁺ neurons. Since this method is widely used for this purpose in many previous studies (Wu et al., J Neurosci, 2004 (PMID: 15140934); Liu et al., Nat Neurosci, 2010 (PMID: 20835251)), it is reasonable to conclude that NA directly acts on the recorded SDH Vgat⁺ interneurons to produce excitation (lines 193-196).

(k) The authors' model (Figure 4H) implies that NA released by LC→SDH NA neurons leads to the inhibition of SDH inhibitory interneurons by NA. In other experiments (Figure 1L, Figure 2A), the authors used optogenetics to promote the release of endogenous NA in SDH by LC→SDH NA neurons. This approach would investigate the function of NA endogenously released by LC NA neurons at presynaptic terminals in the SDH and at physiological concentrations and would test the model more convincingly compared to the bath application of NA.

We appreciate the reviewer’s valuable comment. As noted, optogenetic stimulation of LC^→SDH-NA neurons would indeed be useful to test this model. However, in our case, it is technically difficult to investigate the responses of Vgat⁺ inhibitory neurons and Hes5⁺ astrocytes to NA endogenously released from LC^→SDH-NA neurons. This would require the use of Vgat-Cre or Hes5-CreERT2 mice, but employing these lines precludes the use of NET-Cre mice, which are necessary for specific and efficient expression of ChrimsonR in LC^→SDH-NA neurons. Nevertheless, all of our experimental data consistently support the proposed model, and we believe that the reviewer will agree with this, without additional experiments that is difficult to conduct because of technical limitations (lines 382-388).

(l) As for other experiments, the proportion of Hes+ astrocytes that express hM3Dq, and the absence of expression in other cells, should be quantified and validated to interpret behavioral data.

We thank the reviewer for raising this point. In our experiments, we used an HA-tag (fused with hM3Dq) to confirm hM3Dq expression. However, it is difficult to precisely analyze individual astrocytes because, as shown in Figure 3J, the boundaries of many HA-tag⁺ astrocytes are indistinguishable. This seems to be due to the membrane localization of HA-tag, the complex morphology of astrocytes, and their tile-like distribution pattern (Baldwin et al., Trends Cell Biol, 2024 (PMID: 38180380)). Nevertheless, our previous study demonstrated that ~90% of astrocytes in the superficial laminae are Hes5⁺ (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)), and intra-SDH injection of AAV-hM3Dq labeled the majority of superficial astrocytes (Figure 3J). Thus, AAV-FLEx[hM3Dq] injection into Hes5-CreERT2 mice allows efficient expression of hM3Dq in Hes5⁺ astrocytes in the SDH. Importantly, our previous studies using Hes5-CreERT2 mice have confirmed that hM3Dq is not expressed in other cell types (neurons, oligodendrocytes, or microglia) (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652); Kagiyama et al., Mol Brain, 2025 (PMID: 40289116)). This information regarding the cell-type specificity has now been briefly described in the revised version (lines 218-219).

(m) Showing that the effect of CNO is dose-dependent would strengthen the authors' findings.

Thank you for your comment. We have now demonstrated a dose-dependent effect of CNO on Ca²⁺ responses in SDH astrocytes (please see our response to Major Point (4) from Reviewer #2 (Recommendations for the Authors) (Figure S7; lines 225-228). In addition, we also confirmed that the effect of CNO is not nonspecific, as CNO application did not alter sIPSCs in spinal cord slices prepared from mice lacking hM3Dq expression in astrocytes (Figure S7; lines 225-228).

(n) The proportion of SG neurons for which CNO bath application resulted in a reduction in recorded sIPSCs is not clear.

We have included individual data points in each bar graph to more clearly illustrate the effect of CNO on each neuron (Figure 3L, N).

(o) A1Rs. The specific expression of Cas9 and guide RNAs, and the specific KD of A1Rs, in inhibitory interneurons but not in other cell types expressing A1Rs should be quantified and validated.

In addition to the data demonstrating the specific expression of SaCas9 and sgAdora1 in Vgat⁺ inhibitory neurons shown in Figure 3G of the initial version, we have now conducted the same experiments with a different sample and confirmed this specificity: SaCas9 (detected via HA-tag) and sgAdora1 (detected via mCherry) were expressed in PAX2⁺ inhibitory neurons (Author response image 1). Furthermore, as shown in Figure 3H and I in the initial version, the functional reduction of A₁Rs in inhibitory neurons was validated by electrophysiological recordings. Together, these results support the successful deletion of A₁Rs in inhibitory neurons.

Author response image 1.

Expression of HA-tag and mCherry in inhibitory neurons (a different sample from Figure 3G) SaCas9 (yellow, detected by HA-tag) and mCherry (magenta) expression in the PAX2⁺ inhibitory neurons (cyan) at 3 weeks after intra-SDH injection of AAV-FLEx[SaCas9-HA] and AAV-FLEx[mCherry]-U6-sgAdora1 in Vgat-Cre mice. Arrowheads indicate genome-editing Vgat⁺ cells. Scale bar, 25 µm.

(6) Methods:

It is unclear how fiber photometry is performed using "optic cannula" during restraint stress while mice are in a 50ml falcon tube (as shown in Figure 1A).

We apologize for the omission of this detail in the Methods section. To monitor Ca²⁺ events in LC-NA neurons during restraint stress, we created a narrow slit on the top of the conical tube, allowing mice to undergo restraint stress while connected to the optic fiber (see video). This information has now been added to the Methods section (lines 552-553).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Scientific rigor:

It is unclear if the normal distribution of the data was determined before selecting statistical tests.

We apologize for omitting this description. For all statistical analyses in this study, we first assessed the normality of the data and then selected appropriate statistical tests accordingly. We have added this information to the revised manuscript (lines 711-712).

(2) Nomenclature:

(a) Mouse Genome Informatics (MGI) nomenclature should be used to describe mouse genotypes (i.e., gene name in italic, only first letter is capitalized, alleles in superscript).

(b) FLEx should be used instead of flex.

Thank you for the suggestion. We have corrected these terms (including FLEx) according to MGI nomenclature.

Reviewer #2 (Public review):

Summary:

This study investigates the role of spinal astrocytes in mediating stress-induced pain hypersensitivity, focusing on the LC (locus coeruleus)-to-SDH (spinal dorsal horn) circuit and its mechanisms. The authors aimed to delineate how LC activity contributes to spinal astrocytic activation under stress conditions, explore the role of noradrenaline (NA) signaling in this process, and identify the downstream astrocytic mechanisms that influence pain hypersensitivity.

The authors provide strong evidence that 1-hour restraint stress-induced pain hypersensitivity involves the LC-to-SDH circuit, where NA triggers astrocytic calcium activity via alpha1a adrenoceptors (alpha1aRs). Blockade of alpha1aRs on astrocytes - but not on Vgat-positive SDH neurons - reduced stress-induced pain hypersensitivity. These findings are rigorously supported by well-established behavioral models and advanced genetic techniques, uncovering the critical role of spinal astrocytes in modulating stress-induced pain.

However, the study's third aim - to establish a pathway from astrocyte alpha1aRs to adenosine-mediated inhibition of SDH-Vgat neurons - is less compelling. While pharmacological and behavioral evidence is intriguing, the ex vivo findings are indirect and lack a clear connection to the stress-induced pain model. Despite these limitations, the study advances our understanding of astrocyte-neuron interactions in stress-pain contexts and provides a strong foundation for future research into glial mechanisms in pain hypersensitivity.

Strengths:

The study is built on a robust experimental design using a validated 1-hour restraint stress model, providing a reliable framework to investigate stress-induced pain hypersensitivity. The authors utilized advanced genetic tools, including retrograde AAVs, optogenetics, chemogenetics, and subpopulation-specific knockouts, allowing precise manipulation and interrogation of the LC-SDH circuit and astrocytic roles in pain modulation. Clear evidence demonstrates that NA triggers astrocytic calcium activity via alpha1aRs, and blocking these receptors effectively reduces stress-induced pain hypersensitivity.

Weaknesses:

Despite its strengths, the study presents indirect evidence for the proposed NA-to-astrocyte(alpha1aRs)-to-adenosine-to-SDH-Vgat neurons pathway, as the link between astrocytic adenosine release and stress-induced pain remains unclear. The ex vivo experiments, including NA-induced depolarization of Vgat neurons and chemogenetic stimulation of astrocytes, are challenging to interpret in the stress context, with the high CNO concentration raising concerns about specificity. Additionally, the role of astrocyte-derived D-serine is tangential and lacks clarity regarding its effects on SDH Vgat neurons. The astrocyte calcium signal "dip" after LC optostimulation-induced elevation are presented without any interpretation.

We appreciate the reviewer's careful reading of our paper. According to the reviewer's comments, we have performed new additional experiments and added some discussion in the revised manuscript (please see the point-by-point responses below).

Reviewer #2 (Recommendations for the authors):

The astrocyte-mediated pathway of NA-to-astrocyte (alpha1aRs)-to-adenosine-to-SDH Vgat neurons (A1R) in the context of stress-induced pain hypersensitivity requires more direct evidence. While the data showing that the A1R agonist CPT inhibits stress-induced hypersensitivity and that stress combined with Aβ fiber stimulation increases pERK in the SDH are intriguing, these findings primarily support the involvement of A1R on Vgat neurons and are only behaviorally consistent with SDH-Vgat neuronal A1R knockdown. The role of astrocytes in this pathway in vivo remains indirect. The ex vivo chemogenetic Gq-DREADD stimulation of SDH astrocytes, which reduced sIPSCs in Vgat neurons in a CPT-dependent manner, needs revision with non-DREADD+CNO controls to validate specificity. Furthermore, the ex vivo bath application of NA causing depolarization in Vgat neurons, blocked by CPT, adds complexity to the data leaving me wondering how astrocytes are involved in such processes, and it does not directly connect to stress-induced pain hypersensitivity. These findings are potentially useful but require additional refinement to establish their relevance to the stress model.

We thank the reviewer for the insightful feedback. First, regarding the role of astrocytes in this pathway in vivo, we showed in the initial version that mechanical pain hypersensitivities induced by intrathecal NA injection and by acute restraint stress were attenuated by both pharmacological blockade and Vgat⁺ neuron-specific knockdown of A₁Rs (Figure 4A, B). Given that NA- and stress-induced pain hypersensitivity is mediated by α_1AR-dependent signaling in Hes5⁺ astrocytes (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652); this study), these findings provide in vivo evidence supporting the involvement of the NA → Hes5⁺ astrocyte (via α_1ARs) → adenosine → Vgat⁺ neuron (via A₁Rs) pathway. As noted in the reviewer’s major comment (2), in vivo monitoring of adenosine dynamics in the SDH during stress exposure would further substantiate the astrocyte-to-neuron signaling pathway. However, we did not detect clear signals, potentially due to several technical limitations (see our response below). Acknowledging this limitation, we have now added a new paragraph in the end of Discussion section to address this issue. Second, the specificity of the effect of CNO has now been validated by additional experiments (see our response to major point (4)). Third, the reviewer’s concern regarding the action of NA on Vgat⁺ neurons has also been addressed (see our response to major point (3) below).

Major points:

(1) The in vivo pharmacology using DCK to antagonize D-serine signaling from alpha1a-activated astrocytes is tangential, as there is limited evidence on how Vgat neurons (among many others) respond to D-serine. This aspect requires more focused exploration to substantiate its relevance.

We propose that the site of action of D-serine in our neural circuit model is the NMDA receptors (NMDARs) on excitatory neurons, a notion supported by our previous findings (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652); Kagiyama et al., Mol Brain, 2025 (PMID: 40289116)). However, we cannot exclude the possibility that D-serine also acts on NMDARs expressed by Vgat⁺ inhibitory neurons. Nevertheless, given that intrathecal injection of D-serine in naïve mice induces mechanical pain hypersensitivity (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)), it appears that the pronociceptive effect of D-serine in the SDH is primarily associated with enhanced pain processing and transmission, presumably via NMDARs on excitatory neurons. We have added this point to the Discussion section in the revised manuscript (lines 325-330).

(2) Additionally, employing GRAB-Ado sensors to monitor adenosine dynamics in SDH astrocytes during NA signaling would significantly strengthen conclusions about astrocyte-derived adenosine's role in the stress model.

We agree with the reviewer’s comment. Following this suggestion, we attempted to visualize NA-induced adenosine (and ATP) dynamics using GRAB-ATP and GRAB-Ado sensors (Wu et al., Neuron, 2022 (PMID: 34942116); Peng et al., Science, 2020 (PMID: 32883833)) in acutely isolated spinal cord slices from mice after intra-SDH injection of AAV-hSyn-GRABATP_1.0 and -GRABAdo_1.0. We confirmed expression of these sensors in the SDH (Author response image 2a) and observed increased signals after bath application of ATP (0.1 or 1 µM) or adenosine (1 µM) (Author response image 2b, c). However, we were unable to detect clear signals following NA stimulation (Author response image 2b, c). The reason for this lack of detectable changes remains unclear. If the release of adenosine from astrocytes is a highly localized phenomenon, it may be measurable using high-resolution microscopy capable of detecting adenosine levels at the synaptic level and more sensitive sensors. Further investigation will therefore be required (lines 340-341).

Author response image 2.

Ex vivo imaging of GRAB-ATP and GRAB-Ado sensors.(a) Representative images of GRAB_ATP1.0 (left, green) or GRAB_Ado1.0 (right, green) expression in the SDH at 3 weeks after SDH injection of AAV-hSyn-GRAB_Ado1.0 or AAV-hSyn-GRAB_Ado1.0 in Hes5-CreERT2 mice. Scale bar, 200 µm. (b) Left: Representative fluorescence images showing GRAB_ATP1.0 responses before and after perfusion with NA or ATP. Right: Representative traces showing responses to ATP (0.1 and 1 µM) or NA (10 µM). (c) Left: Representative fluorescence images showing GRABAdo1.0 responses before and after perfusion with NA or adenosine (Ado). Right: Representative traces showing responses to Ado (0.01, 0.1, and 1 µM), NA (10 µM), or no application (negative control).

(3) The interpretation of Figure 3D is challenging. The manuscript implies that 20 μM NA acts on Adra1a receptors on Vgat neurons to depolarize them, but this concentration should also activate Adra1a on astrocytes, leading to adenosine release and potential inhibition of depolarization. The observation of depolarization despite these opposing mechanisms requires explanation, as does the inhibition of depolarization by bath-applied A1R agonist. Of note, 20 μM NA is a high concentration for Adra1a activation, typically responsive at nanomolar levels. The discussion should reconcile this with prior studies indicating dose-dependent effects of NA on pain sensitivity (e.g., Reference 22).

Like the reviewer, we also considered that bath-applied NA could activate α_1ARs expressed on Hes5⁺ astrocytes. To clarify this point, we have performed additional patch-clamp recordings and found that knockdown of A₁Rs in Vgat⁺ neurons tended to increase the proportion of Vgat⁺ neurons with NA-induced depolarizing responses (Figure S8). Therefore, it is conceivable that NA-induced excitation of Vgat⁺ neurons may involve both a direct effect of NA activating α_1ARs in Vgat⁺ neurons and an indirect inhibitory signaling from NA-stimulated Hes5⁺ astrocytes via adenosine (lines 298-300).

The concentration of NA used in our ex vivo experiments is higher than that typically used in vitro with αR-_1Aexpressing cell lines or primary culture cells, but is comparable to concentrations used in other studies employing spinal cord slices (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652); Baba et al., Anesthesiology, 2000 (PMID: 10691236); Lefton et al., Science, 2025 (PMID: 40373122)). In slice experiments, drugs must diffuse through the tissue to reach target cells, resulting in a concentration gradient. Therefore, higher drug concentrations are generally necessary in slice experiments, in contrast to cultured cell experiments, where drugs are directly applied to target cells. Importantly, we have previously shown that the pharmacological effects of 20 μM NA on Vgat⁺ neurons and Hes5⁺ astrocytes are abolished by loss of α_1ARs in these cells (Uchiyama et al., Mol Brain, 2022 (PMID: 34980215); Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)), confirming the specificity of these NA actions.

Regarding the dose-dependent effect of NA on pain sensitivity, NA-induced pain hypersensitivity is abolished in Hes5⁺ astrocyte-specific α_1AR-KO mice (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)), indicating that this behavior is mediated by α_1ARs expressed on Hes5⁺ astrocytes. In contrast, the suppression of pain sensitivity by high doses of NA was unaffected in the KO mice (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)), suggesting that other adrenergic receptors may contribute to this phenomenon. Clarifying the responsible receptors will require future investigation.

(4) In Figure 3K-M, the CNO concentration used (100 μM) is unusually high compared to standard doses (1 to a few μM), raising concerns about potential off-target effects. Including non-hM3Dq controls and using lower CNO concentrations are essential to validate the specificity of the observed effects. Similarly, the study should clarify whether astrocyte hM3Dq stimulation alone (without NA) would induce hyperpolarization in Vgat neurons and how this interacts with NA-induced depolarization.

We acknowledge that the concentration of CNO used in our experiments is relatively high compared to that used in other reports. However, in our experiments, application of CNO at 1, 10, and 100 μM induced Ca²⁺ increases in GCaMP6-expressing astrocytes in spinal cord slices in a concentration-dependent manner (Figure S7). Among these, 100 μM CNO most effectively replicated the NA-induced Ca²⁺ signals in astrocytes. Based on these findings, we selected this concentration for use in both the current and previous studies (Kohro et al., Nat Neurosci., 2020 (PMID: 33020652)). Importantly, to rule out non-specific effects, we conducted control experiments using spinal cord slices from mice that did not express hM3Dq in astrocytes and confirmed that CNO had no effect on Ca²⁺ responses in astrocytes and sIPSCs in substantial gelatinosa (SG) neurons (Figure S7; lines 223-228). Thus, although the CNO concentration used is relatively high, the observed effects of CNO are not non-specific but result from the chemogenetic activation of hM3Dq-expressing astrocytes.

In this study, we used Hes5-CreERT2 and Vgat-Cre mice to manipulate gene expression in Hes5⁺ astrocytes and Vgat⁺ neurons, respectively. In order to fully address the reviewer’s comment, the use of both Cre lines is necessary. However, simultaneous and independent genetic manipulation in each cell type using Cre activity alone is not feasible with the current genetic tools. We have mentioned this as a technical limitation in the Discussion section (lines 382-388).

(5) The role of D-serine released by hM3Dq-stimulated astrocytes in (separately) modulating sub-types of neurons including excitatory neurons and Vgat positives needs more detailed discussion. If no effect of D-serine on Vgat neurons is observed, this should be explicitly stated, and the discussion should address why this might be the case.

As mentioned in our response to Major Point (1) above, we have added a discussion of this point in the revised manuscript (lines 325-330).

(6) Finally, the observed "dip" in astrocyte calcium signals below baseline following the large peaks with LC optostimulation should be discussed further, as understanding this phenomenon could provide valuable insights into astrocytic signaling dynamics in the context of single acute or repetitive chronic stress.

Thank you for your comment. We found that this phenomenon was not affected by pretreatment with the α_1AR-specific antagonist silodosin (Author response image 3), which effectively suppressed Ca²⁺ elevations evoked by stimulation of LC-NA neurons (Figure 2F). This implies that the phenomenon is independent of α_1AR signaling. Elucidating the detailed underlying mechanism remains an important direction for future investigation.

Author response image 3.

The observed "dip" in astrocyte Ca²⁺ signals was not affected by pretreatment with the α_1AR-specific antagonist silodosin. Representative traces of astrocytic GCaMP6m signals in response to optogenetic stimulation of LC-NAe^→SDHrgic axons/terminals in a spinal cord slice. Each trace shows the GCaMP6m signal before and after optogenetic stimulation (625 nm, 1 mW, 10 Hz, 5 ms pulse duration, 10 s). Slices were pretreated with silodosin (40 nM) for 5 min prior to stimulation.

Reviewer #3 (Public review):

Summary:

This is an exciting and timely study addressing the role of descending noradrenergic systems in nocifensive responses. While it is well-established that spinally released noradrenaline (aka norepinephrine) generally acts as an inhibitory factor in spinal sensory processing, this system is highly complex. Descending projections from the A6 (locus coeruleus, LC) and the A5 regions typically modulate spinal sensory processing and reduce pain behaviours, but certain subpopulations of LC neurons have been shown to mediate pronociceptive effects, such as those projecting to the prefrontal cortex (Hirshberg et al., PMID: 29027903).

The study proposes that descending cerulean noradrenergic neurons potentiate touch sensation via alpha-1 adrenoceptors on Hes5+ spinal astrocytes, contributing to mechanical hyperalgesia. This finding is consistent with prior work from the same group (dd et al., PMID:). However, caution is needed when generalising about LC projections, as the locus coeruleus is functionally diverse, with differences in targets, neurotransmitter co-release, and behavioural effects. Specifying the subpopulations of LC neurons involved would significantly enhance the impact and interpretability of the findings.

Strengths:

The study employs state-of-the-art molecular, genetic, and neurophysiological methods, including precise CRISPR and optogenetic targeting, to investigate the role of Hes5+ astrocytes. This approach is elegant and highlights the often-overlooked contribution of astrocytes in spinal sensory gating. The data convincingly support the role of Hes5+ astrocytes as regulators of touch sensation, coordinated by brain-derived noradrenaline in the spinal dorsal horn, opening new avenues for research into pain and touch modulation.

Furthermore, the data support a model in which superficial dorsal horn (SDH) Hes5+ astrocytes act as non-neuronal gating cells for brain-derived noradrenergic (NA) signalling through their interaction with substantia gelatinosa inhibitory interneurons. Locally released adenosine from NA-stimulated Hes5+ astrocytes, following acute restraint stress, may suppress the function of SDH-Vgat+ inhibitory interneurons, resulting in mechanical pain hypersensitivity. However, the spatially restricted neuron-astrocyte communication underlying this mechanism requires further investigation in future studies.

Weaknesses

(1) Specificity of the LC Pathway targeting

The main concern lies with how definitively the LC pathway was targeted. Were other descending noradrenergic nuclei, such as A5 or A7, also labelled in the experiments? The authors must convincingly demonstrate that the observed effects are mediated exclusively by LC noradrenergic terminals to substantiate their claims (i.e. "we identified a circuit, the descending LC→SDH-NA neurons").

(a) For instance, the direct vector injection into the LC likely results in unspecific effects due to the extreme heterogeneity of this nucleus and retrograde labelling of the A5 and A7 nuclei from the LC (i.e., Li et al., PMID: 26903420).

We appreciate the reviewer's valuable comments. To address this point, we performed additional experiments and demonstrated that intra-SDH injection of AAVretro-Cre followed by intra-LC injection of AAV2/9-EF1α-FLEx[DTR-EGFP] specifically results in DTR expression in NA neurons of the LC, but not of the A5 or A7 regions (Figure S4; lines 127-128). These results confirm the specificity of targeting the LC^→SDH-NAergic pathway in our study.

(b) It is difficult to believe that the intersectional approach described in the study successfully targeted LC→SDH-NA neurons using AAVrg vectors. Previous studies (e.g., PMID: 34344259 or PMID: 36625030) demonstrated that similar strategies were ineffective for spinal-LC projections. The authors should provide detailed quantification of the efficiency of retrograde labelling and specificity of transgene expression in LC neurons projecting to the SDH.

Thank you for your comment. As we described in our response to the weakness (5)-e) of Reviewer #1 (Public review), our additional analysis showed that, under our experimental conditions, expression of genes (for example DTR) was observed in 4.4% of NA (TH⁺) neurons in the LC (Figure S4; lines 126-127).

The reasons for this difference between the previous studies and our current study is unclear; however, it is likely attributed to methodological differences, including the type of viral vectors employed, species differences (mouse (PMID: 34344259, our study) vs. rat (PMID: 36625030)), the amount of AAV injected into the SDH (300 nL at three sites (PMID: 34344259), and 300 nL at a single site (our study)) and LC (500 nL at a single site (PMID: 34344259), and 300 nL at a single site (our study)), as well as the depth of AAV injection in the SDH (200–300 µm from the dorsal surface of the spinal cord (PMID: 34344259), and 120–150 µm in depth from the surface of the dorsal root entry zone (our study)).

(c) Furthermore, it is striking that the authors observed a comparably strong phenotypical change in Figure 1K despite fewer neurons being labelled, compared to Figure 1H and 1N with substantially more neurons being targeted. Interestingly, the effect in Figure 1K appears more pronounced but shorter-lasting than in the comparable experiment shown in Figure 1H. This discrepancy requires further explanation.

Although only a representative section of the LC was shown in the initial version, LC^→SDH-NA neurons are distributed rostrocaudally throughout the LC, as previously reported (Llorca-Torralba et al., Brain, 2022 (PMID: 34373893)). Our additional experiments analyzing multiple sections of the anterior and posterior regions of the LC have now revealed that approximately sixty LC^→SDH-NA neurons express DTR, and these neurons are eliminated following DTX treatment (Figure S4; lines 126-128) (it should be noted that these neurons specifically project to the L4 segment of the SDH, and the total number of LC^→SDH-NA neurons is likely much higher). Considering the specificity of LC^→SDH-NAergic pathway targeting demonstrated in our study (as described above), together with the fact that primary afferent sensory fibers from the plantar skin of the hindpaw predominantly project to the L4 segment of the SDH, these data suggest that the observed behavioral changes are attributable to the loss of these neurons and that ablation of even a relatively small number of NA neurons in the LC can have a significant impact on behavior. We have added this hypothesis in the Discussion section (lines 373-382).

Regarding the data in Figures 1H and 1K, as the reviewer pointed out, a statistically significant difference was observed at 90 min in mice with ablation of LC-NA neurons, but not in those with LC^→SDH-NA neuron ablation. This is likely due to a slightly higher threshold in the control group at this time point (Figure 1K), and it remains unclear whether there is a mechanistic difference between the two groups at this specific time point.

(d) A valuable addition would be staining for noradrenergic terminals in the spinal cord for the intersectional approach (Figure 1J), as done in Figures 1F/G. LC projections terminate preferentially in the SDH, whereas A5 projections terminate in the deep dorsal horn (DDH). Staining could clarify whether circuits beyond the LC are being ablated.

As suggested, we performed DTR immunostaining in the SDH; however, we did not detect any DTR immunofluorescence there. A similar result was also observed in the spinal terminals of DTR-expressing primary afferent fibers (our unpublished data). The reason for this is unclear, but to the best of our knowledge, no studies have clearly shown DTR expression at presynaptic terminals, which may be because the action of DTX on the neuronal cell body is necessary for cell ablation. Nevertheless, as described in our response to the weakness (5)-f) by Reviewer 1 (Public review), we have now confirmed the specific expression of DTR in the LC, but not in the A5 and A7 regions (Figure S4; lines 127-128).

(e) Furthermore, different LC neurons often mediate opposite physiological outcomes depending on their projection targets-for example, dorsal LC neurons projecting to the prefrontal cortex PFCx are pronociceptive, while ventral LC neurons projecting to the SC are antinociceptive (PMIDs: 29027903, 34344259, 36625030). Given this functional diversity, direct injection into the LC is likely to result in nonspecific effects.

To avoid behavioral outcomes resulting from a mixture of facilitatory and inhibitory effects caused by activating the entire population of LC-NA neurons, we employed a specific manipulation targeting LC^→SDH-NA neurons using AAV vectors. The specificity of this manipulation was confirmed in our previous study (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)) and in the current study (Figure S4). Using this approach, we previously demonstrated that LC neurons can exert pronociceptive effects via astrocytes in the SDH (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)). This pronociceptive role is further supported by the current study, which uses a more selective manipulation of LC^→SDH-NA neurons through a NET-Cre mouse line. In addition, intrathecal administration of relatively low doses of NA in naïve mice clearly induces mechanical pain hypersensitivity. Nevertheless, we have also acknowledged that several recent studies have reported an inhibitory role of LC^→SDH-NA neurons in spinal nociceptive signaling. The reason for these differing behavioral outcomes remains unclear, but several methodological differences may underlie the discrepancy. First, the degree of LC^→SDH-NA neuronal activity may play a role. Although direct comparisons between studies reporting pro- and anti-nociceptive effects are difficult, our previous studies demonstrated that intrathecal administration of high doses of NA in naïve mice does not induce mechanical pain hypersensitivity (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)). Second, the sensory modality used in behavioral testing may be a contributing factor as the pronociceptive effect of NA appears to be selectively observed in responses to mechanical, but not thermal, stimuli (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)). This sensory modality-selective effect is also evident in mice subjected to acute restraint stress (Table S1). Therefore, the role of LC^→SDH-NA neurons in modulating nociceptive signaling in the SDH is more complex than previously appreciated, and their contribution to pain regulation should be reconsidered in light of factors such as NA levels, sensory modality, and experimental context. In revising the manuscript, we have included some points described above in the Discussion (lines 282-291).

Conclusion on Specificity: The authors are strongly encouraged to address these limitations directly, as they significantly affect the validity of the conclusions regarding the LC pathway. Providing more robust evidence, acknowledging experimental limitations, and incorporating complementary analyses would greatly strengthen the manuscript.

We appreciate the reviewer’s comments. We fully acknowledge the limitations raised and agree that addressing them directly is important for the rigor of our conclusions on the LC pathway. To this end, we have performed additional experiments (e.g., Figure A and S4), which are now included in the revised manuscript. Furthermore, we have also newly added a new paragraph for experimental limitations in the end of Discussion section (lines 373-408). We believe these new data substantially strengthen the validity of our findings and have clarified these points in the Discussion section.

(2) Discrepancies in Data

(a) Figures 1B and 1E: The behavioural effect of stress on PWT (Figure 1E) persists for 120 minutes, whereas Ca2+ imaging changes (Figure 1B) are only observed in the first 20 minutes, with signal attenuation starting at 30 minutes. This discrepancy requires clarification, as it impacts the proposed mechanism.

Thank you for your important comment. As pointed out by the reviewer, there is a difference between the duration of behavioral responses and Ca²⁺ events, although the exact time point at which the PWT begins to decline remains undetermined (as behavioral testing cannot be conducted during stress exposure). A similar temporal difference was also observed following intraplantar injection of capsaicin (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)); while LC^→SDH-NA neuron-mediated astrocytic Ca²⁺ responses in SDH astrocytes last for 5–10 min after injection, behavioral hypersensitivity peaks around 60 min post-injection and gradually returns to baseline over the subsequent 60–120 min. These findings raise the possibility that astrocyte-mediated pain hypersensitivity in the SDH may involve a sustained alteration in spinal neural function, such as central sensitization. We have added this hypothesis to the Discussion section of the revised manuscript (lines 399-408), as it represents an important direction for future investigation.

(b) Figure 4E: The effect is barely visible, and the tissue resembles "Swiss cheese," suggesting poor staining quality. This is insufficient for such an important conclusion. Improved staining and/or complementary staining (e.g., cFOS) are needed. Additionally, no clear difference is observed between Stress+Ab stim. and Stress+Ab stim.+CPT, raising doubts about the robustness of the data.

As suggested, we performed c-FOS immunostaining and obtained clearer results (Figure 4E,F; lines 243-252). We also quantitatively analyzed the number of c-FOS⁺ cells in the superficial laminae, and the results are consistent with those obtained from the pERK experiments.

(c) Discrepancy with Existing Evidence: The claim regarding the pronociceptive effect of LC→SDH-NAergic signalling on mechanical hypersensitivity contrasts with findings by Kucharczyk et al. (PMID: 35245374), who reported no facilitation of spinal convergent (wide-dynamic range) neuron responses to tactile mechanical stimuli, but potent inhibition to noxious mechanical von Frey stimulation. This discrepancy suggests alternative mechanisms may be at play and raises the question of why noxious stimuli were not tested.

In our experiments, ChrimsonR expression was observed in the superficial and deeper laminae of the spinal cord (Figure S6). Due to the technical limitations of the optical fibers used for optogenetics, the light stimulation could only reach the superficial laminae; therefore, it may not have affected the activity of neurons (including WDR neurons) located in the deeper laminae. Furthermore, the study by Kucharczyk et al. (Brain, 2022 (PMID: 35245374)) employed a stimulation protocol that differed from ours, applying continuous stimulation over several minutes. Given that the levels of NA released from LC^→SDH-NAergic terminals in the SDH increase with the duration of terminal stimulation (as shown in Figure 2B), longer stimulation may result in higher levels of NA in the SDH. Considering also our data indicating that the pro- and anti-nociceptive effects of NA are dose dependent (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)), these differences may be related to LC^→SDH-NA neuron activity, NA levels in the SDH, and the differential responses of SDH neurons in the superficial versus deeper laminae (lines 388-395).

(3) Sole reliance on Von Frey testing

The exclusive use of von Frey as a behavioural readout for mechanical sensitisation is a significant limitation. This assay is highly variable, and without additional supporting measures, the conclusions lack robustness. Incorporating other behavioural measures, such as the adhesive tape removal test to evaluate tactile discomfort, the needle floor walk corridor to assess sensitivity to uneven or noxious surfaces, or the kinetic weight-bearing test to measure changes in limb loading during movement, could provide complementary insights. Physiological tests, such as the Randall-Selitto test for noxious pressure thresholds or CatWalk gait analysis to evaluate changes in weight distribution and gait dynamics, would further strengthen the findings and allow for a more comprehensive assessment of mechanical sensitisation.

Thank you for your suggestion. Based on our previous findings that Hes5⁺ astrocytes in the SDH selectively modulate mechanosensory signaling (Kohro et al., Nat Neurosci, 2020 (PMID: 33020652)), the present study focused on behavioral responses to mechanical stimuli using von Frey filaments. As we have not previously conducted most of the behavioral tests suggested by the reviewers, and as we currently lack the necessary equipments for these tests (e.g., Randall–Selitto test, CatWalk gait analysis, and weight-bearing test), we were unable to include them in this study. However, it will be of great interest in future research to investigate whether activation of the LC^→SDH-NA neuron-to-SDH Hes5⁺ astrocyte signaling pathway similarly sensitizes behavioral responses to other types of mechanical stimuli and also to investigate the sensory modality-selective pro- and antinociceptive role of LC^→SDH-NAergic signaling in the SDH (lines 396-399).

Overall Conclusion

This study addresses an important and complex topic with innovative methods and compelling data. However, the conclusions rely on several assumptions that require more robust evidence. Specificity of the LC pathway, experimental discrepancies, and methodological limitations (e.g., sole reliance on von Frey) must be addressed to substantiate the claims. With these issues resolved, this work could significantly advance our understanding of astrocytic and noradrenergic contributions to pain modulation.

We have made every effort to address the reviewer’s concerns through additional experiments and analyses. Based on the new control data presented, we believe that our explanation is reasonable and acceptable. Although additional data cannot be provided on some points due to methodological constraints and limitations of the techniques currently available in our laboratory, we respectfully submit that the evidence presented sufficiently supports our conclusions.

Reviewer #3 (Recommendations for the authors):

A lot of beautiful and challenging-to-collect data is presented. Sincere congratulations to all the authors on this achievement!

Notwithstanding, please carefully reconsider the conclusions regarding the LC pathway, as additional evidence is required to ensure their specificity and robustness.

We thank the reviewer for the kind comments and for raising an important point regarding the LC pathway. The reviewer’s feedback prompted us to conduct additional investigations to further strengthen the validity of our conclusions. We have incorporated these new data and analyses into the revised manuscript, and we believe that these revisions substantially enhance the robustness and reliability of our findings.

Reviewer #1 (Public review):

Summary:

Ewing sarcoma is an aggressive pediatric cancer driven by the EWS-FLI oncogene. Ewing sarcoma cells are addicted to this chimeric transcription factor, which represents a strong therapeutic vulnerability. Unfortunately, targeting EWS-FLI has proven to be very difficult and better understanding how this chimeric transcription factor works is critical to achieving this goal. Towards this perspective, the group had previously identified a DBD-𝛼4 helix (DBD) in FLI that appears to be necessary to mediate EWS-FLI transcriptomic activity. Here, the authors used multi-omic approaches, including CUT&tag, RNAseq, and MicroC to investigate the impact of this DBD domain. Importantly, these experiments were performed in the A673 Ewing sarcoma model where endogenous EWS-FLI was silenced, and EWS-FLI-DBD proficient or deficient isoforms were re-expressed (isogenic context). They found that the DBD domain is key to mediate EWS-FLI cis activity (at msat) and to generate the formation of specific TADs. Furthermore, cells expressing DBD deficient EWS-FLI display very poor colony forming capacity, highlighting that targeting this domain may lead to therapeutic perspectives.

Strengths:

The group has strong expertise in Ewing sarcoma genetics and epigenetics and also in using and analyzing this model (Theisen et al., 2019; Boone et al., 2021; Showpnil et al., 2022).

They aim at better understanding how EWS-FLI mediated its oncogenic activity, which is critical to eventually identifying novel therapies against this aggressive cancer.

They use the most recent state-of-the-art omics methods to investigate transcriptome, epigenetics, and genome conformation methods. In particular, Micro-C enables achieving up to 1kb resolved 3D chromatin structures, making it possible to investigate a large number of TADs and sub-TADs structures where EWS-FLI1 mediates its oncogenic activity.

They performed all their experiments in an Ewing sarcoma genetic background (A673 cells) which circumvents bias from previously reported approaches when working in non-orthologous cell models using similar approaches.

Weaknesses:

The main weakness stems from the poor reproducibility of the Micro-C data. Indeed, the distances and clustering observed between replicates appear to be similar to, or even greater than, those observed between biological conditions. For instance, in Figure 1B, we do not observe any clear clustering among DBD1, DBD2, DBD+1, and DBD+2. Although no further experiments were performed, the authors tempered their claims by rephrasing aspects related to this issue and the reviewer also acknowledged that the transcriptomic data are convincing and support their findings.

Regarding DBD stability and the cycloheximide experiments requested to rule out any half-life bias of DBD (as higher stability of the re-expressed DBD+ could also partially explain the results independently of a 3D conformational change), the reviewer acknowledged that the WB, RNA-seq data and agar assays presented by the authors appear reproducible across experiments.

Author response:

The following is the authors’ response to the previous reviews

Public Review:

Reviewer #1 (Public review):

Ewing sarcoma is an aggressive pediatric cancer driven by the EWS-FLI oncogene. Ewing sarcoma cells are addicted to this chimeric transcription factor, which represents a strong therapeutic vulnerability. Unfortunately, targeting EWS-FLI has proven to be very difficult and better understanding how this chimeric transcription factor works is critical to achieving this goal. Towards this perspective, the group had previously identified a DBD-𝛼4 helix (DBD) in FLI that appears to be necessary to mediate EWS-FLI transcriptomic activity. Here, the authors used multi-omic approaches, including CUT&tag, RNAseq, and MicroC to investigate the impact of this DBD domain. Importantly, these experiments were performed in the A673 Ewing sarcoma model where endogenous EWS-FLI was silenced, and EWS-FLI-DBD proficient or deficient isoforms were re-expressed (isogenic context). They found that the DBD domain is key to mediate EWS-FLI cis activity (at msat) and to generate the formation of specific TADs. Furthermore, cells expressing DBD deficient EWS-FLI display very poor colony forming capacity, highlighting that targeting this domain may lead to therapeutic perspectives.

This new version of the study comprises as requested new data from an additional cell line. The new data has strengthened the manuscript. Nevertheless, some of the arguments of the authors pertaining to the limitations of immunoblots to assess stability of the DBD constructs or the poor reproducibility of the Micro C data remain problematic. While the effort to repeat MicroC in a different cell line is appreciated, the data are as heterogeneous as those in A673 and no real conclusion can be drawn. The authors should tone down their conclusions. If DBD has a strong effect on chromatin organization, it should be reproducible and detectable. The transcriptomic and cut and tag data are more consistent and provide robust evidence for their findings at these levels. 

We agree that the Micro-C data have more apparent heterogeneity within and across cell lines as compared to other analyses such as our included CUT&Tag and RNA-seq. We addressed the possible limitations of the technique as well as inherent biology that might be driving these findings in our previous responses. Despite the poor clustering on the PCA plots, our analysis on differential interacting regions, TADs and loops remain consistent across both cell lines. We are confident that these findings reflect the context of transcriptional regulation by the constructs, therefore the role of the alpha-helix in modulating chromatin organization. To address the concerns raised by the editors and reviewers for the strength of the conclusions we drew from the Micro-C findings we have made changes to the language used to describe them throughout the manuscript. Find these changes outlined below.

• On lines 70-71, "is required to restructure" was changed to "is implicated in restructuring of"

• On line 91, "is required for" was changed to "participates in"

• On line 98, "is required for" changed to "is potentially required for"

• On line 360-361, "is required for restructuring" changed to "participates in restructuring"

Concerning the issue of stability of the DBD and DBD+ constructs, a simple protein half-life assay (e.g. cycloheximide chase assay) could rule out any bias here and satisfactorily address the issue.

While we generally agree that a cycloheximide assay is a relatively simple approach to look at protein half-life, as we discussed last me the assays included in this paper are performed at equilibrium and rely on the concentration of protein at the me of the assay. This is particularly true for assays involving crosslinking, like Micro-C. As discussed in our prior response, western blots are semi quantitative at best, even when normalized to a housekeeping protein. In analyzing the relative protein concentration of DBD vs. DBD+ with relative protein intensities first normalized to tubulin and using the wildtype EWSR1::FLI1 rescue as a reference point, we find that there is no statistical difference in the samples used for micro-C here (Author responseimage 1A) or across all of the samples that we have used for publication (Author response image 1B). This does show that DBD generally has more variable expression levels relative to wildtype EWSR1::FLI1, and this is consistent with our experience in the lab.

Nonetheless, we did attempt to perform the requested cycloheximide chase experiment to determine protein stability. Unfortunately, despite an extensive number of troubleshooting attempts, we have not been able to get good expression of DBD for these experiments. The first author who performed this work has left the lab and we have moved to a new lab space since the benchwork was performed. We continue to try to troubleshoot to get this experimental system for DBD and DBD+ to work again. When we tried to look at stability of DBD+ following cycloheximide treatment, there did appear to be some difference in protein stability (Author response image 2). However, these conditions are not the same conditions as those we published, they do not meet our quality control standards for publication, and we are concerned about being close to the limit of detection for DBD throughout the later timepoints. Additional studies will be needed with more comparable expression levels between DBD and DBD+ to satisfactorily address the reviewer concerns.

Author response image 1.

Expression Levels of DBD and DBD+ Across Experiments. Expression levels of DBD and DBD+ protein based on western blot band intensity normalized by tubulin band intensity. Expression levels are relative to wildtype EWSR1::FLI1 rescue levels and are calculated for (A) A673 samples used for micro-C and (B) all published studies of DBD and DBD+. P-values were calculated with an unpaired t-test.

Author response image 2.

CHX chase assay to determine the stability of DBD and DBD+. (A) Knock-down of endogenous EWSR1::FLI1 detected with FLI1 ab and rescue with DBD and DBD+ detected with FLAG ab. (B) CHX chase assay to determine the stability of DBD and DBD+ in A-673 cells with quantification of the protein levels (n=3). Error bars represent standard deviation. The half-lives (t1/2) of DBD and DBD+ were listed in the table.

Suggestions:

The Reviewing Editor and a referee have considered the revised version and the responses of the referees. While the additional data included in the new version has consolidated many conclusions of the study, the MicroC data in the new cell line are also heterogeneous and as the authors argue, this may be an inherent limitation of the technique. In this situation, the best would be for the authors to avoid drawing robust conclusions from this data and to acknowledge its current limitations.

As discussed above, we have changed the language regarding our conclusions from micro-C data to soften the conclusions we draw per the Editor’s suggestion.

The referee and Reviewing Editor also felt that the arguments of the authors concerning a lack of firm conclusions on the stability of EWS-FLI1 under +/-DBD conditions could be better addressed. We would urge the authors to perform a cycloheximide chase type assay to assess protein half-life. These types of experiments are relatively simple to perform and should address this issue in a satisfactory manner.

As discussed above, we do not feel that differences in protein stability would affect the results here because the assays performed required similar levels of protein at equilibrium. Our additional analyses in this response shows that there are not significant differences between DBD and DBD+ levels in samples that pass quality control and are used in published studies. However, we attempted to address the reviewer and editor comments with a cycloheximide chase assay and were unable to get samples that would have passed our internal quality control standards. These data may suggest differences in protein stability, but it is unclear that these conditions accurately reflect the conditions of the published experiments, or that this would matter with equal protein levels at equilibrium.

What are Ptf1a Cre; Sox9 OE mice?

These are mice that were engineered so that:

Ptf1a-Cre turns on genetic changes specifically in pancreatic acinar cells (the enzyme-producing cells).

Sox9 OE means Sox9 is overexpressed (OE = overexpression), meaning the Sox9 gene is artificially turned on at higher-than-normal levels.

The system likely includes:

An HA-tag (a small detectable protein tag used to track the overexpressed protein)

RFP (red fluorescent protein) as a marker for cells that did not undergo recombination.

🔬 What did they observe?

Sox9 overexpression happened mostly in acinar cells

These cells expressed:

The HA-tag

Extra Sox9

This confirms the genetic system worked where expected.

Duct cells and endocrine cells mostly did NOT change

They remained unrecombined

They still expressed RFP

Meaning the genetic modification did not activate in those cells.

So the gene change was specific to acinar cells, which is what the researchers intended.

🐭 What about the pancreas itself?

In 3-week-old modified mice:

Pancreas weight → normal

Tissue structure (morphology) → normal

Blood glucose levels → normal

When compared to control mice, there were no obvious differences.

📌 What’s the conclusion?

Even though Sox9 was artificially overexpressed in acinar cells, it:

Did not disrupt pancreatic development

Did not change pancreas size

Did not affect blood sugar levels

In short:

For early development (up to 3 weeks), forcing Sox9 expression in acinar cells does not cause obvious problems in the pancreas.

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Author response:

The following is the authors’ response to the original reviews.

Reviewer #1:

Summary:

In their study, the authors investigated the F. graminearum homologue of the Drosophila Misato-Like Protein DML1 for a function in secondary metabolism and sensitivity to fungicides.

Strengths:

Generally, the topic of the study is interesting and timely, and the manuscript is well written, albeit in some cases, details on methods or controls are missing.

Weaknesses:

However, a major problem I see is with the core result of the study, the decrease in the DON content associated with the deletion of FgDML1. Although some growth data are shown in Figure 6, indicating a severe growth defect, the DON production presented in Figure 3 is not related to biomass. Also, the method and conditions for measuring DON are not described. Consequently, it could well be concluded that the decreased amount of DON detected is simply due to decreased growth, and the specific DON production of the mutant remains more or less the same.

To alleviate this concern, it is crucial to show the details on the DON measurement and growth conditions and to relate the biomass formation under the same conditions to the DON amount detected. Only then can a conclusion as to an altered production in the mutant strains be drawn.

We appreciate it very much that you spent much time on my paper and give me good suggestions, we tried our best to revise the manuscript. I have revised my manuscript according to your suggestions. The point to point responds to the reviewer’s comments are listed as following. Our method for DON quantification was based on the amount per unit of mycelium. After obtaining the absorbance value from the ELISA reaction, the concentration of DON was calculated according to a standard curve and a formula, then divided by the dry weight of the mycelium to obtain the DON content per unit of mycelium, with the results finally expressed in µg/g.

(1) Line 139f

... FgDML1 is a critical positive regulator of virulence ....

Clearly, the deletion of FgDML1 impacts virulence, but it is too much of a general effect to say it is a regulator. DML1 acts high up in the cascade, impacting numerous processes, one of which is virulence. Generally, it has to be considered that deletion of DML1 causes a severe growth defect, which in turn is likely to lead to a plethora of effects. Besides discussing this fact, please also revise the manuscript to avoid references to "direct effects" or "regulator".

Thank you very much for your advice. Our method for determining the amount of DON is based on the amount of mycelium per unit. After obtaining the absorbance value through Elisa reaction, we calculate the concentration of DON toxin according to the established standard curve and formula. Then, we divide it by the dry weight of mycelium to obtain the DON toxin content per unit mycelium, and finally present the results in µg/g. In summary, we conclude that the decrease in DON production by ΔFgDML is not due to slower hyphal growth, but rather a decrease in the ability of unit hyphae to produce DON toxins compared to the wild type. Given the decrease in DON toxin synthesis caused by FgDML1 deficiency, we believe that using a regulator is reasonable.

(2) Line 143

Please define "toxin-producing conditions".

Thank you very much for your advice. We have accurately defined the conditions for toxin-producing conditions in the manuscript' toxin-inducing conditions '(28°C, 145 ×g, 7 days incubation)' (in L163-164)

(3) Line 149

A brief intro on toxisomes should be provided in the introduction to better integrate this into the manuscript's results.

Thank you very much for your advice. We have added corresponding content about toxin producing bodies in the introduction section 'The biosynthesis of DON entails a reorganization of the endoplasmic reticulum into a specialized compartment termed the "toxisome" (Tang et al., 2018). The assembly of the toxisome coincides with the aggregation of key biosynthetic enzymes, which in turn enhances the efficiency of DON production. Concurrently, this compartmentalization serves as a self-defense mechanism, protecting the fungus from the autotoxicity of TRI pathway intermediates (Boenisch et al., 2017). The proteins TRI1, TRI4, TRI14, and Hmr1 are confirmed constituents of this structure(Kistler and Broz, 2015; Menke et al., 2013).' (in L86-93)

(4) Line 153

DON production decreases by about 80 %, but not to 0. Consequently, DML1 is important, but NOT essential for DON production.

Thank you very much for your advice. We have made changes to the wording of the corresponding sections based on your suggestions. 'FgDML1 is essential for the biosynthesis of the DON toxin. '(in L161)

(5) Line 168ff

Please provide a reference for FgDnm1 being critical for mitochondrial fission and state whether such an interaction has been shown in other organisms.

Thank you very much for your advice. We have made changes to the wording of the corresponding sections based on your suggestions. 'FgDnm1 is a key dynamin-related protein mediating mitochondrial fission(Griffin et al., 2005; Kang et al., 2023), suggesting that FgDML1 may form a complex with FgDnm1 to regulate mitochondrial fission and fusion processes. To our knowledge, this is the first report documenting an interaction between DML1 and Dnm in any fungal species, including model organisms such as S. cerevisiae. This novel finding provides new insights into the molecular mechanisms underlying mitochondrial dynamics in filamentous fungi. '(in L277-283)

(6) Line 178

Please specify whether Complex III activity was related to biomass and provide a p-value or standard deviation for the value.

Thank you very much for your question. The activity determination of complex III was completed using a complex III enzyme activity kit (Solarbio, Beijing, China) (Li, et al 2022; Wang, et al 2022). Take 0.1 g of standardized mycelium as the sample for the experiment. Given that the mycelium has been homogenized, we believe that there is no necessary correlation between the activity and biomass of complex III. And we also refined the specific measurement steps in the article. ' Briefly, 0.1 g of mycelia was homogenized with 1 mL of extraction buffer in an ice bath. The homogenate was centrifuged at 600 ×g for 10 min at 4°C. The resulting supernatant was then subjected to a second centrifugation at 11,100 ×g for 10 min at 4°C. The pellet was resuspended in 200 μL of extraction buffer and disrupted by ultrasonication (200 W, 5 s pulses with 10 s intervals, 15 cycles). Complex III enzyme activity was finally measured by adding the working solution as per the manufacturer's protocol. Each treatment group contains three biological replicates and three technical replicates. '(in L511-517)

Li C, et al. Amino acid catabolism regulates hematopoietic stem cell proteostasis via a GCN2-eIF2 axis. Cell Stem Cell. 2022 Jul 7; 29(7):1119-1134.e7. doi: 10.1016/j.stem.2022.06.004. PMID: 35803229.

Wang K, et al. Locally organised and activated Fth1hi neutrophils aggravate inflammation of acute lung injury in an IL-10-dependent manner. Nat Commun. 2022 Dec 13;13(1):7703. doi: 10.1038/s41467-022-35492-y. PMID: 36513690; PMCID: PMC9745290

(7) Line 185

Albeit this headline is a reasonable hypothesis, you actually did not show that the conformation is altered. Please reword accordingly.

Please also add references for cyazofamid acting on the QI site versus other fungicides acting on the QO site.

Thank you very much for your advice. We have made changes to the wording of the corresponding sections based on your suggestions. 'Overexpression of FgQCR2, FgQCR8, and FgQCR9 may alters the conformation of the QI site, resulting in reduced sensitivity to cyazofamid. '(in L212-213). For fungicides targeting Qi and QO sites, we have added corresponding descriptions in the respective sections 'Numerous fungicides have been developed to inhibit the Qo site (e.g., pyraclostrobin, azoxystrobin)(Nuwamanya et al., 2022; Peng et al., 2022) and the Qi site (e.g., cyazofamid)(Mitani et al., 2001) of the cytochrome bc1 complex. '(in L327-329)

(8) Line 200

This section on growth should be moved up right after introducing the mutant strain.

Thank you very much for your advice. We have advanced the part of nutritional growth and sexual asexual development before DON toxin to promote better reading and understanding. We arranged the sequence in the previous way to emphasize the new discovery between mitochondria and DON toxin. We found a significant decrease in DON toxin in ΔFgDML1, defects in the formation of toxin producing bodies, and downregulation of FgTRis at both the gene and protein levels. In summary, we believe that the absence of FgDML1 does indeed lead to a decrease in the content of DON toxin, and FgDML1 plays a regulatory role in the synthesis of DON toxin. In addition, our measurements of DON toxin, acetyl CoA, ATP and other indicators are all based on the amount per unit hyphae, excluding differences caused by hyphal biomass or growth. We have further refined the materials and methods to facilitate better reading and understanding.

(9) Line 203

"... significantly reduced growth rates ..."

This is not what was measured here. Figure 6A shows a plate assay that can be used to assess hyphal extension. In the figure, it is also visible that the mycelium of the deletion mutant is much denser, maybe due to increased hyphal branching. Please reword.

Additionally, it is important to include a biomass measurement here under the conditions used for DON assessment. Hyphal extension measurements cannot be used instead of biomass.

Thank you very much for your advice. We have made changes to the wording of the corresponding sections based on your suggestions. 'The ΔFgDML1 strain displayed a distinct growth phenotype characterized by retardation in radial growth and the formation of more compact, denser hyphal networks on all tested media compared to the PH-1 and ΔFgDML-C strains. '(in L136-138).

(10) Line 217

Please include information on how long the cultures were monitored. Given the very slow growth of the mutant, perithecia formation may be considerably delayed beyond 14 days.

Thank you very much for your advice. Based on your suggestion, we have extended the incubation time for sexual reproduction to 21 days to more accurately evaluate its sexual reproduction ability. Our results show that even after 21 days, Δ FgDML1 still cannot produce ascospores and ascospores, which proves that the absence of FgDML1 does indeed cause sexual reproduction defects in F. graminearum.

Author response image 1.

Discussion

(11) Please mention your summary Figure 8 early on in the discussion, and explain conclusions with this figure in mind. Please avoid repetition of the results section as much as possible.

Also, please state clearly what was already known from previous research and is in agreement with your results, and what is new (in fungi or generally).

Thank you very much for your advice. Based on your suggestion, we mentioned Fig8 earlier in the first half of the discussion and provided guidance for the following text. We also conducted a more comprehensive discussion by analyzing our research results and comparing them with previous studies. 'Our study defines a novel mechanism through which FgDML1 governs mitochondrial homeostasis. We demonstrate that FgDML1 directly interacts with the key mitochondrial fission regulator FgDnm1 and positively modulates cellular bioenergetic metabolism, as evidenced by elevated ATP and acetyl-CoA levels (Fig. 8). '(in L250-253). 'The Misato/DML1 protein family is evolutionarily conserved from yeast to humans and plays a critical role in mitochondrial regulation. In S. cerevisiae, DML1 is an essential gene; its deletion is lethal, while its overexpression results in fragmented mitochondrial networks and aberrant cellular morphology, underscoring its necessity for normal mitochondrial function (Gurvitz et al., 2002). Similarly, in Homo sapiens, the homolog Misato localizes to the mitochondrial outer membrane, and both its depletion and overexpression are sufficient to disrupt mitochondrial morphology and distribution (Kimura and Okano, 2007). '(in L241-244).

(12) Line 262ff

Please specify if this interaction was shown previously in other organisms and provide references.

Thank you very much for your advice. We have clearly stated in the corresponding section that the interaction between FgDML and FgDnm is the first reported, and to our knowledge, no relevant reports have been found in other species so far. ' Notably, FgDML1 was found to interact with FgDnm1 (Fig. 5E), FgDnm1 is a key dynamin-related protein mediating mitochondrial fission(Griffin et al., 2005; Kang et al., 2023), suggesting that FgDML1 may form a complex with FgDnm1 to regulate mitochondrial fission and fusion processes. To our knowledge, this is the first report documenting an interaction between DML1 and Dnm in any fungal species, including model organisms such as S. cerevisiae. This novel finding provides new insights into the molecular mechanisms underlying mitochondrial dynamics in filamentous fungi. '(in L276-283)

(13) Line 287ff

There is no result that would justify this speculation. Please remove.

Thank you very much for your advice. We have modified the corresponding wording in the corresponding section. 'In conclusion, our findings suggest that the overexpression of assembly factors FgQCR2, FgQCR7, and FgQCR8 in ΔFgDML1 potentially modifies the conformation of the Qi site, which specifically modulates the sensitivity of F. graminearum to cyazofamid. '(in L352-355)

Materials and methods

(14) A table with all primer sequences used in the study and their purpose is missing. For every experiment, the number of technical and biological replicates needs to be stated.

Thank you very much for your advice. We have presented all the primers used in this study in Supplementary Table 1 (in Table S1) .We added the number of technical and biological replicates in the material and method descriptions for each experiment. 'For each sample, a total of 200 conidia were counted. The experiment included three biological replicates with three technical replicates each.'(in L434-436). 'Each treatment group contains three biological replicates. '(in L444-445). 'Each treatment group contains three biological replicates and three technical replicates. ' (in L463-464). 'Each treatment group contains three biological replicates and three technical replicates. '(in L474-475). 'Each treatment group contains three biological replicates. '(in L483). 'Each treatment group contains three biological replicates and three technical replicates.'(in L501-502). 'Each treatment group contains three biological replicates and three technical replicates. '(in L516-517). 'The experiment was independently repeated three times. '(in L533-534).

(15) Line 369ff

Please provide final concentrations used for assays here.

Thank you very much for your advice. The final concentration has been displayed in the Figure (in Fig6. A, B) (in Fig. S3). And we have provided supplementary Table 2 to reflect the concentration in a more intuitive way.(in Table. S2)

(16) Line 383

Please provide a reference or data on the use of F2du for transformant selection and explain the abbreviation.

Thank you very much for your advice. Based on your suggestion, we have provided the full name and references of F2du. 'Transformants were selected on PDA plates containing either 100 μg/mL Hygromycin B (Yeasen, Shanghai, China) or 0.2 μmol/mL 5-Fluorouracil 2'-deoxyriboside (F2du) (Solarbio, Beijing, China)(Zhao et al., 2022). '(in L405-407).

(17) Line 407

Please provide a reference for the method and at least a brief description.

Thank you very much for your advice. Based on your suggestion, we have added references and provided a brief introduction to the method. 'As previously described (Tang et al., 2020; Wang et al., 2025), Specifically, coleoptiles were inoculated with conidial suspensions and incubated for 14 days, while leaves were inoculated with fresh mycelial plugs and incubated for 5 days, followed by observation and quantification of disease symptoms. DON toxin was measured using a Wise Science ELISA-based kit (Wise Science, Jiangsu, China) (Li et al., 2019; Zheng et al., 2018). '(in L466-471)

(18) Line 414ff

Also, here, the amount of biomass has to be considered for the measurement to be able to distinguish if actually less of the compounds were produced or if the effect seen was merely due to an altered amount of biomass present.

Thank you very much for your advice. We believe that biomass is not within the scope of our measurement indicators, as we have measured and calculated based on unit hyphae. Therefore, we have ruled out experimental bias caused by a decrease in biomass.

RNA and RT-qPCR

(19) Line 461

When the strains were transferred to AEA medium, was the biomass measured, at least wet weight, and in which culture volume was it done? It makes a big difference if the amount of (wet) biomass dilutes a small amount of fungicide-containing culture or if biomass is added in at least roughly equal amounts in sufficient growth medium to ensure equal conditions.

Thank you very much for your question. Our sample processing controlled the wet weight of the samples before dosing, ensuring that the wet weight of the mycelium obtained from each sample before dosing was 0.2g. The mycelium was obtained through AEA with a volume of 100mL. This ensured consistency in the initial biomass between groups before dosing, and also ensured the accuracy of the drug concentration.

(20) Line 466

Please provide the name and supplier of the kit.

Thank you very much for your advice. We have added corresponding content in the corresponding location. 'Mycelium was collected and total RNA was extracted following the instructions provided by the Total RNA Extraction Kit (Tiangen, Beijing, China).' (in L523-524).

(21) All primer sequences must be provided in a table.

Thank you very much for your advice. We have presented all the primers used in this study in Supplementary Table 1. (in Table S1).

(22) For RT qPCR it is essential to check the RNA quality to be sure that the obtained results are not artifacts due to varying quality, which may exceed differences. Please state how quality control was done and which threshold was applied for high-quality RNA to be used in RTqPCR (like RIN factor, etc).

Thank you very much for your question. We performed stringent quality control on the extracted total RNA. First, a micro-spectrophotometer was used to measure RNA concentration and purity, confirming that the A260/A280 ratio was between 1.8 and 2.0 and the A260/A230 ratio was greater than 2.0, indicating good RNA purity without significant protein or organic solvent contamination.Subsequently, verification by agarose gel electrophoresis revealed distinct 28S and 18S rRNA bands, demonstrating good RNA integrity and absence of degradation.

Author response image 2.

(B): Minor Comments:

(1) Please increase the font size of the labels and annotations of the figures; it is hard to read as it is now.

Thank you very much for your advice. We have increased the size of annotations or numerical labels in the corresponding images for better reading.

(2) Throughout the manuscript: Please check that all abbreviations are explained at first use.

Thank you very much for your advice. We have checked the entire text to ensure that abbreviations have their full names when they first appear.

(3) I do hope that the authors can clarify all concerns and provide an amended manuscript of this interesting story.

Thank you very much for your advice. Sincerely thank you for your suggestions and questions, which have been very helpful to us.

Reviewer #2:

The manuscript entitled "Mitochondrial Protein FgDML1 Regulates DON Toxin Biosynthesis and Cyazofamid Sensitivity in Fusarium graminearum by affecting mitochondrial homeostasis" identified the regulatory effect of FgDML1 in DON toxin biosynthesis and sensitivity of Fusarium graminearum to cyazofamid. The manuscript provides a theoretical framework for understanding the regulatory mechanisms of DON toxin biosynthesis in F. graminearum and identifies potential molecular targets for Fusarium head blight control. The paper is innovative, but there are issues in the writing that need to be addressed and corrected.

We appreciate it very much that you spent much time on my paper and give me good suggestions, we tried our best to revise the manuscript. I have revised my manuscript according to your suggestions with red words. In the response comments, to highlight the specific positions of the revised parts in the manuscript with red line number. The point to point responds to the reviewer’s comments are listed as following.

Weaknesses:

(1) The authors speculate that cyazofamid treatment caused upregulation of the assembly factors, leading to a change in the conformation of the Qi protein, thus restoring the enzyme activity of complex III. But no speculation was given in the discussion as to why this would lead to the upregulation of assembly factors, and how the upregulation of assembly factors would change the protein conformation, and is there any literature reporting a similar phenomenon? I would suggest adding this to the discussion.

Thank you very much for your advice. Based on your suggestion, we have added content related to the assembly factor of complex III in the discussion section and made modifications to the corresponding wording. 'Previous studies have reported that mutations in the Complex III assembly factors TTC19, UQCC2, and UQCC3 impair the assembly and activity of Complex III (Feichtinger et al., 2017; Wanschers et al., 2014). '(in L345-347). 'In conclusion, our findings suggest that the overexpression of assembly factors FgQCR2, FgQCR7, and FgQCR8 in ΔFgDML1 potentially modifies the conformation of the Qi site, which specifically modulates the sensitivity of F. graminearum to cyazofamid. '(in L352-355).

(2) Would increased sensitivity of the mutant to cell wall stress be responsible for the excessive curvature of the mycelium?

Thank you very much for your question. We believe that the sensitivity of ΔFgDML1 to osmotic stress is reduced, which may not be related to hyphal bending, as shown in the Author response image 3. During the conidia stage, ΔFgDML1 cannot germinate in YEPD, while the application of 1M Sorbitol promotes its germination. But it is caused by internal unknown mechanisms, which is also the focus of our future research.

Author response image 3.

(3) The vertical coordinates of Figure 7B need to be modified with positive inhibition rates for the mutants.

Thank you very much for your advice. The display in Figure 7B truly reflects its inhibition rate. In the Δ FgDML1 mutant, when subjected to osmotic stress treatment, the inhibition rate becomes negative, indicating that the colony growth is greater than that of the CK. Therefore, the negative inhibition rate is shown in Figure 7B.

(1) In Figure 1B, Figure 3C, and Figure 6C, the scale below the picture is not clear. In Figure 5D, the histogram is unclear, and it is recommended to redraw the graph.

Thank you very much for your advice. The issue with the above images may be due to Word compression. We have changed the settings and enlarged the images as much as possible to better display them.

(2) The full Latin name of the strain should be used in the title of figures and tables.

Thank you very much for your advice. Based on your suggestion, we have used the full names of the strains appearing in the title of figures and tables.

(3) Proteins in line 117 should be abbreviated.

Thank you very much for your advice. Based on your suggestion, we have abbreviated the corresponding positions. 'The DML1 protein from S. cerevisiae was used as a query for a BLAST search against the Fusarium genome database, resulting in the identification of the putative DML1 gene FgDML1 (FGSG_05390) in F. graminearum. '(in L118-120).

(4) The sentence in lines 187-189, which is supposed to introduce why the test is sensitive to the three drugs, is currently illogical.

Thank you very much for your advice. Based on your suggestion, we have made modifications to the corresponding sections. 'Since Complex III is involved in the action of both cyazofamid (targeting the QI site) and pyraclostrobin (targeting the QO site), the sensitivity of ΔFgDML1 to cyazofamid and pyraclostrobin was investigated. ' (in L214-216).

(5) The expression of FgQCR2, FgQCR7, and FgQCR8 was significantly upregulated in ΔFgDML1 at transcription levels. Do FgQCR2, FgQCR8, and FgQCR9 show upregulated expression at the protein level?

Thank you very much for your question. Based on your suggestion, we evaluated the protein expression levels of FgQCR2, FgQCR7, and FgQCR8 in PH-1 and ΔFgDML1, and we found that the protein expression levels of FgQCR2, FgQCR7, and FgQCR8 in ΔFgDML1 were higher than those in PH-1. (in Fig. 6F).

(6) In Figure 7B, it is recommended to adjust the position of the horizontal axis labels in the histogram.

Thank you very much for your advice. Based on your suggestion, we have made modifications to the corresponding sections.(in Fig. 7B)

(7) There are numerous errors in the writing of gene names in the text. Please check the full text and change the writing of gene names and mutant names to italic.

Thank you very much for your advice. We have checked the entire text to ensure that all genes have been italicized.

(8) All acronyms should be spelled out in figure and table captions. e.g., F. graminearum.

Thank you very much for your advice. Based on your suggestion, we have used the full names of the strains appearing in the title of figures and tables.

(9) In line 492, P should be lowercase and italic.

Thank you very much for your advice. Based on your suggestion, we have made adjustments to the corresponding content.

Reviewer #3:

Summary:

The manuscript "Mitochondrial 1 protein FgDML1 regulates DON toxin biosynthesis and cyazofamid sensitivity in Fusarium graminearum by affecting mitochondrial homeostasis" describes the construction of a null mutant for the FgDML1 gene in F. graminearum and assays characterising the effects of this mutation on the pathogen's infection process and lifecycle. While FgDML1 remains underexplored with an unclear role in the biology of filamentous fungi, and although the authors performed several experiments, there are fundamental issues with the experimental design and execution, and interpretation of the results.

Strengths:

FgDML1 is an interesting target, and there are novel aspects in this manuscript. Studies in other organisms have shown that this protein plays important roles in mitochondrial DNA (mtDNA) inheritance, mitochondrial compartmentalisation, chromosome segregation, mitochondrial distribution, mitochondrial fusion, and overall mitochondrial dynamics. Indeed, in Saccharomyces cerevisiae, the mutation is lethal. The authors have carried out multi-faceted experiments to characterise the mutants.

Weaknesses:

However, I have concerns about how the study was conceived. Given the fundamental importance of mitochondrial function in eukaryotic cells and how the absence of this protein impacts these processes, it is unsurprising that deletion of this gene in F. graminearum profoundly affects fungal biology. Therefore, it is misleading to claim a direct link between FgDML1 and DON toxin biosynthesis (and virulence), as the observed effects are likely indirect consequences of compromised mitochondrial function. In fact, it is reasonable to assume that the production of all secondary metabolites is affected to some extent in the mutant strains and that such a strain would not be competitive at all under non-laboratory conditions. The order in which the authors present the results can be misleading, too. The results on vegetative growth rate appeared much later in the manuscript, which should have come first, as the FgDML1 mutant exhibited significant growth defects, and subsequent results should be discussed in that context. Moreover, the methodologies are not described properly, making the manuscript hard to follow and difficult to replicate.

We appreciate it very much that you spent much time on my paper and give me good suggestions, we tried our best to revise the manuscript. I have revised my manuscript according to your suggestions with red words. In the response comments, to highlight the specific positions of the revised parts in the manuscript with red line number. The point to point responds to the reviewer’s comments are listed as following.

For weaknesses,we arranged the sequence in this way to emphasize the novel discovery between mitochondria and DON toxin. We found a significant decrease in DON toxin in Δ FgDML1, defects in the formation of toxin producing bodies, and downregulation of FgTRis at both the gene and protein levels. In summary, we believe that the absence of FgDML1 does indeed lead to a decrease in the content of DON toxin, and FgDML1 plays a regulatory role in the synthesis of DON toxin. In addition, our measurements of DON toxin, acetyl CoA, ATP and other indicators are all based on the amount per unit hyphae, excluding differences caused by hyphal biomass or growth. We have further refined the materials and methods to facilitate better reading and understanding.

(1) Lines 37-39: The disease itself does not produce toxins; it is the fungus that causes the disease that produces toxins. Moreover, the disease symptoms observed are likely caused by the toxins produced by the fungus.

Thank you very much for your advice. We have made modifications to the wording of the corresponding sections. 'Studies have shown that increased DON levels are positively correlated with the pathogenicity rate of F. graminearum.'(in L36-37).

(2) Lines 82-87: While it is challenging to summarise the role of ATP in just a few words, this section needs improvement for clarity and accuracy. Additionally, I do not believe that drawing a direct link between mitochondrial defects and toxin production is an appropriate strategy in this case.

Thank you very much for your advice. Based on your suggestion, we have added corresponding descriptions in the corresponding positions to provide more information on the relationship between ATP and toxins, in order to better prepare for the following text. 'Pathogen-intrinsic ATP homeostasis is recognized as a critical, rate-limiting determinant for toxin biosynthesis. Previous studies indicate that dual-target inhibition of ATP synthase (AtpA) and adenine deaminase (Ade) by a specific small-molecule probe effectively depletes intracellular ATP, consequently suppressing the synthesis of key virulence factors TcdA and TcdB transcriptionally and translationally(Marreddy et al., 2024). The systemic toxicity of Anthrax Edema Toxin (ET) is primarily attributed to its catalytic activity, which depletes the host cell's ATP reservoir, thereby triggering a bioenergetic collapse that culminates in cell lysis and death(Liu et al., 2025). '(in L78-86).

(3) Lines 125-126: The manuscript does not clearly describe how subcellular localisation was determined. This methodology needs to be properly detailed.

Thank you very much for your advice. The subcellular localization was validated through co-localization analysis with MitoTracker Red CMXRos, a mitochondrial-specific dye. The observed overlap between the FgDML1-GFP signal and the mitochondrial marker confirmed mitochondrial localization. Based on these results, we determined that FgDML1 is definitively localized to the mitochondria.We have incorporated this description in the appropriate section of the manuscript. 'Furthermore, subcellular localization studies confirmed that FgDML1 localizes to mitochondria, as demonstrated by colocalization with a mitochondria-specific dye MitoTracker Red CMXRos (Fig. 1B). '(in L125-127).

(4) Regarding the organisation of the Results section, it needs to be revised. While I understand the authors' intention to emphasise the impact on virulence, the results showing how FgDML1 deletion affects vegetative growth, asexual and sexual reproduction, and sensitivity to stressors should be presented before the virulence assays and effects on DON production. Additionally, the authors do not provide any clear evidence that FgDML1 directly interacts with proteins involved in asexual or sexual reproduction, stress responses, or virulence. Therefore, it is misleading to suggest that FgDML1 directly regulates these processes. The observed phenotypes are, rather, a consequence of severely impaired mitochondrial function. Without functional mitochondria, the cell cannot operate properly, leading to widespread physiological defects. In this regard, statements such as those in lines 139-140 and 343-344 are misleading.

Thank you very much for your advice. We have adjusted the order of the images based on your suggestion, placing the characterization of ΔFgDML1 in nutritional growth, sexual reproduction, and other aspects before DON toxin. And we have made adjustments to the corresponding statements. 'These findings demonstrate that FgDML1 is a positive regulator of virulence in F. graminearum. '(in L140-141).

(5) Lines 185-186: The authors do not provide sufficient evidence to support the claim that FgQCR2, FgQCR8, and FgQCR9 overexpression is the main cause of reduced cyazofamid sensitivity. Although expression of these genes is altered, reduced sensitivity may result from changes in other proteins or pathways. To strengthen this claim, overexpression of FgQCR2, 8, and 9 in the wild-type background, followed by assessment of cyazofamid resistance, would be necessary. As it stands, there is no support for the claim presented in lines 329-332.

Thank you very much for your advice. To establish a causal link between the overexpression of FgQCR2, FgQCR7, and FgQCR8 and the observed reduction in cyazofamid sensitivity, we first quantified the protein levels of these assembly factor. Western blot analysis confirmed their elevated expression in the ΔFgDML1 mutant compared to the wild-type PH-1. We further generated individual overexpression strains for FgQCR2, FgQCR7, and FgQCR8 in the wild-type PH-1 background. Fungicide sensitivity assays revealed that all three overexpression mutants displayed significantly reduced sensitivity to cyazofamid compared to the parental strain. These genetic complementation experiments confirm that upregulation of FgQCR2, FgQCR7, and FgQCR8 is sufficient to confer reduced cyazofamid sensitivity.We have incorporated these explanations and provided supporting images in the appropriate section of the manuscript. 'To further clarify whether the upregulated expression of FgQCR2, FgQCR7, and FgQCR8 genes affects their protein expression levels, we measured the protein levels. The results showed that the protein expression levels of FgQCR2, FgQCR7, and FgQCR8 in ΔFgDML1 were higher than those in PH-1(Fig. 6F). Subsequently, we overexpressed FgQCR2, FgQCR7, and FgQCR8 in the wild-type background, and the corresponding overexpression mutants exhibited reduced sensitivity to cyazofamid(Fig. 6E). '(in L205-211)(in Fig. 6E, F)

(6) Lines 187-190: This segment is confusing and difficult to follow. It requires rewriting for clarity.

Thank you very much for your advice. Based on your suggestion, we have made corresponding modifications in the corresponding locations. 'Since Complex III is involved in the action of both cyazofamid (targeting the QI site) and pyraclostrobin (targeting the QO site), the sensitivity of ΔFgDML1 to cyazofamid and pyraclostrobin was investigated. ''(in L214-216)

(7) Lines 345-346: The authors state that in this study, FgDML1 is localised in mitochondria, which implies that in other studies, its localisation was different. Is this accurate? Clarification is needed.

Thank you very much for your question. In previous studies, the localization of this protein was not clearly defined, and its function was only emphasized to be related to mitochondria. Whether in yeast or in Drosophila melanogaster. (Miklos et al., 1997; Gurvitz et al., 2002)

Miklos GLG, Yamamoto M-T, Burns RG, Maleszka R. 1997. An essential cell division gene of drosophila, absent from saccharomyces, encodes an unusual protein with  tubulin-like and myosin-like peptide motifs. Proc Natl Acad Sci 94:5189–5194. doi:10.1073/pnas.94.10.5189

Gurvitz A, Hartig A, Ruis H, Hamilton B, de Couet HG. 2002. Preliminary characterisation of DML1, an essential saccharomyces cerevisiae gene related to misato of drosophila melanogaster. FEMS Yeast Res 2:123–135. doi:10.1016/S1567-1356(02)00083-1

Material and Methods Section

(8) In general, the methods require more detailed descriptions, including the brands and catalog numbers of reagents and kits used. Simply stating that procedures were performed according to manufacturers' instructions is insufficient, particularly when the specific brand or kit is not identified.

Thank you very much for your advice. We have added corresponding content based on your suggestion to more comprehensively display the reagent brand and complete product name. 'Transformants were selected on PDA plates containing either 100 μg/mL Hygromycin B (Yeasen, Shanghai, China) or 0.2 μmol/mL 5-Fluorouracil 2'-deoxyriboside (F2du) (Solarbio, Beijing, China)(Zhao et al., 2022). ' (in L405-407). 'DON toxin was measured using a Wise Science ELISA-based kit (Wise Science, Jiangsu, China) (Li et al., 2019; Zheng et al., 2018) '. (in L469-471)

(9) Line 364: What do CM and MM stand for? Please define.

Thank you very much for your advice. Based on your suggestion, we have made modifications in the corresponding locations. 'To evaluate vegetative growth, complete medium (CM), minimal medium (MM), and V8 Juice Agar (V8) media were prepared as described previously(Tang et al., 2020). '(in L385-387)

Generation of Deletion and Complemented Mutants:

(10) This section lacks detail. For example, were PCR products used directly for PEG-mediated transformation, or were the fragments cloned into a plasmid?

Thank you very much for your question. We directly use the fused fragments for protoplast transformation after sequencing confirmation. We have clearly defined the fragment form used for transformation at the corresponding location. 'The resulting fusion fragment was transformed into the wild-type F. graminearum PH-1 strain via polyethylene glycol (PEG)-mediated protoplast transformation. '(in L403-405).

(11) PCR and Southern blot validation results should be included as supplementary material, along with clear interpretations of these results.

Thank you very much for your advice. In the supplementary material we submitted, Supplementary Figure 2 already includes the results of PCR and Southern blot validation.(in Fig. S2)

(12) There is almost no description of how the mutants mentioned in lines 388-390 were generated.

Thank you very much for your advice. Based on your suggestions, we have added relevant content in the appropriate sections to more comprehensively and clearly reflect the experimental process. 'Specifically, FgDML1, including its native promoter region and open reading frame (ORF) (excluding the stop codon), was amplified.The PCR product was then fused with the XhoI -digested pYF11 vector. After transformation into E. coli and sequence verification, the plasmid was extracted and subsequently introduced into PH-1 protoplasts. For FgDnm1-3×Flag, the 3×Flag tag was added to the C-terminus of FgDnm1 by PCR, fused with the hygromycin resistance gene and the FgDnm1 downstream arm, and then introduced into PH-1 protoplasts. The overexpression mutant was constructed according to a previously described method. Specifically, the ORF of FgDML1 was amplified and the PCR product was ligated into the SacII-digested pSXS overexpression vector. The resulting plasmid was then transformed into PH-1 protoplasts (Shi et al., 2023). For the construction of PH-1::FgTri1+GFP and ΔFgDML1::FgTri1+GFP, the ORF of FgTri1 was amplified and ligated into the XhoI-digested pYF11 vector as described above. The resulting vectors were then transformed into protoplasts of PH-1 or ΔFgDML1, respectively.'(in L413-426).

Vegetative Growth and Conidiation Assays:

(13) There is no information about how long the plates were incubated before photos were taken. Judging by the images, it appears that different incubation times may have been used.

Thank you very much for your advice. Due to the slower growth of ΔFgDML1, we adopted different incubation periods and have supplemented the relevant content in the corresponding section. 'All strains were incubated at 25°C in darkness; however, due to ΔFgDML1 slower growth, the ΔFgDML1 mutant required a 5-day incubation period compared to the 3 days used for PH-1 and ΔFgDML1-C. '(in L490-493).

(14) There is no description of the MBL medium.

Thank you very much for your advice. Based on your suggestion, we have supplemented the corresponding content in the corresponding positions. 'Mung bean liquid (MBL) medium was used for conidial production, while carrot agar (CA) medium was utilized to assess sexual reproduction(Wang et al., 2011). '(in L387-389).

DON Production and Pathogenicity Assays:

(15) Were DON levels normalised to mycelial biomass? The vegetative growth assays show that FgDML1 null mutants exhibit reduced growth on all tested media. If mutant and wild-type strains were incubated for the same period under the same conditions, it is reasonable to assume that the mutants accumulated significantly less biomass. Therefore, results related to DON production, as well as acetyl-CoA and ATP levels, must be normalised to biomass.

Thank you very much for your question. We have taken into account the differences in mycelial biomass. Therefore, when measuring DON, acetyl-CoA, and ATP levels, all data were normalized to mycelial mass and calculated as amounts per unit of mycelium, thereby avoiding discrepancies arising from variations in biomass.

Sensitivity Assays:

(16) While the authors mention that gradient concentrations were used, the specific concentrations and ranges are not provided. Importantly, have the plates shown in Figure 5 been grown for different periods or lengths? Given the significantly reduced growth rate shown in Figure 6A, the mutants should not have grown to the same size as the WT (PH-1) as shown in Figures 5A and 5B unless the pictures have been taken on different days. This needs to be explained.

Thank you very much for your question. Due to the slower growth of ΔFgDML1, we adopted different incubation periods and have supplemented the relevant content in the corresponding section. 'All strains were incubated at 25°C in darkness; however, due to ΔFgDML1 slower growth, the ΔFgDML1 mutant required a 5-day incubation period compared to the 3 days used for PH-1 and ΔFgDML1-C. '(in L490-493).

(17) Additionally, was inhibition measured similarly for both stress agents and fungicides? This should be clarified.

Thank you very much for your question. We have supplemented the specific concentration gradient of fungicides. 'The concentration gradients for each fungicide in the sensitivity assays were set up according to Supplementary Table S2. '(in L493-494)(in Table. S2).

Complex III Enzyme Activity:

(18) A more detailed description of how this assay was performed is needed.

Thank you very much for your advice. We have provided further detailed descriptions of the corresponding sections. 'Briefly, 0.1 g of mycelia was homogenized with 1 mL of extraction buffer in an ice bath. The homogenate was centrifuged at 600 ×g for 10 min at 4°C. The resulting supernatant was then subjected to a second centrifugation at 11,000 ×g for 10 min at 4°C. The pellet was resuspended in 200 μL of extraction buffer and disrupted by ultrasonication (200 W, 5 s pulses with 10 s intervals, 15 cycles). Complex III enzyme activity was finally measured by adding the working solution as per the manufacturer's protocol. '(in L511-517)

(19) Were protein concentrations standardised prior to the assay?

Thank you very much for your question. Protein concentrations for all Western blot samples were quantified using a BCA assay kit to ensure equal loading.

(20) Line 448: Are ΔFgDML1::Tri1+GFP and ΔFgDML1+GFP the same strain? ΔFgDML1::Tri1+GFP has not been previously described.

Thank you very much for your question. These two strains are not the same strain, and we have supplemented their construction process in the corresponding section. 'For the construction of PH-1::FgTri1+GFP and ΔFgDML1::FgTri1+GFP, the ORF of FgTri1 was amplified and ligated into the XhoI-digested pYF11 vector as described above. The resulting vectors were then transformed into protoplasts of PH-1 or ΔFgDML1, respectively. '(in L423-426)

(21) Lines 460 and 468: Please adopt a consistent nomenclature, either RT-qPCR or qRT-PCR.

Thank you very much for your advice. We have unified it and modified the corresponding content in the corresponding sections. 'Reverse Transcription Quantitative Polymerase Chain Reaction (RT-qPCR) was carried out using the QuantStudio 6 Flex real-time PCR system (Thermo, Fisher Scientific, USA) to assess the relative expression of three subunits of Complex III (FgCytb, FgCytc1, FgISP), five assembly factors (FgQCR2, FgQCR6, FgQCR7, FgQCR8, FgQCR9), and DON biosynthesis-related genes (FgTri5 and FgTri6). '(in L526-531)

(22) Lines 472-473: Why was FgCox1 used as a reference for FgCytb? Clarification is needed.

Thank you very much for your question. FgCytb (cytochrome b) and FgCOX1 (cytochrome c oxidase subunit I) are both encoded by the mitochondrial genome and serve as core components of the oxidative phosphorylation system (Complex III and Complex IV, respectively). Their transcription is co-regulated by mitochondrial-specific mechanisms in response to cellular energy status. Consequently, under experimental conditions that perturb energy homeostasis, FgCOX1 expression exhibits relative, context-dependent stability with FgCytb, or at least co-varies directionally, making it a superior reference for normalizing target gene expression. In contrast, FgGapdh operates within a distinct genetic and regulatory system. Using FgCOX1 ensures that both reference and target genes reside within the same mitochondrial compartment and functional module, thereby preventing normalization artifacts arising from independent variation across disparate pathways.

(23) Lines 476-477: This step requires a clearer and more detailed explanation.

Thank you very much for your advice. We provided detailed descriptions of them in their respective positions. 'For FgDnm1-3×Flag, the 3×Flag tag was added to the C-terminus of FgDnm1 by PCR, fused with the hygromycin resistance gene and the FgDnm1 downstream arm, and then introduced into PH-1 protoplasts. '(in L417-419). 'The FgDnm1-3×Flag fragment was introduced into PH-1 and FgDML1+GFP protoplasts, respectively, to obtain single-tagged and double-tagged strains. '(in L541-543)

Western blotting:

(24) Uncropped Western blot images should be provided as supplementary material.

Thank you very much for your advice. All Western blot images will be submitted to the supplementary material package.

(25) Lines 485-489: A more thorough description of the antibodies used (including source, catalogue number, and dilution) is necessary.

Thank you very much for your advice. The antibodies used are clearly stated in terms of brand, catalog number, and dilution. We have added the dilution ratio. 'All antibodies were diluted as follows: primary antibodies at 1:1000 and secondary antibodies at 1:10000. '(in L550-551)

(26) The Western blot shown in Figure 3D appears problematic, particularly the anti-GAPDH band for FgDML1::FgTri1+GFP. Are both anti-GAPDH bands derived from the same gel?

Thank you very much for your advice. We are unequivocally certain that these data derive from the same gel. Therefore, we are providing the original image for your inspection.

Author response image 4.

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 manuscript reports the identification of putative orthologues of mitochondrial contact site and cristae organizing system (MICOS) proteins in Plasmodium falciparum - an organism that unusually shows an acristate mitochondrion during the asexual part of its life cycle and then this develops cristae as it enters the sexual stage of its life cycle and beyond into the mosquito. The authors identify PfMIC60 and PfMIC19 as putative members and study these in detail. The authors at HA tags to both proteins and look for timing of expression during the parasite life cycle and attempt (unsuccessfully) to localise them within the parasite. They also genetically deleted both gene singly and in parallel and phenotyped the effect on parasite development. They show that both proteins are expressed in gametocytes and not asexuals, suggesting they are present at the same time as cristae development. They also show that the proteins are dispensible for the entire parasite life cycle investigated (asexuals through to sporozoites), however there is some reduction in mosquito transmission. Using EM techniques they show that the morphology of gametocyte mitochondria is abnormal in the knock out lines, although there is great variation.

Major comments: The manuscript is interesting and is an intriguing use of a well studied organism of medical importance to answer fundamental biological questions. My main comments are that there should be greater detail in areas around methodology and statistical tests used. Also, the mosquito transmission assays (which are notoriously difficult to perform) show substantial variation between replicates and the statistical tests and data presentation are not clear enough to conclude the reduction in transmission that is claimed. Perhaps this could be improved with clearer text?

We would like to thank the reviewer for taking the time to review our manuscript. We are happy to hear the reviewer thinks the manuscript is interesting and thank the reviewer for their constructive feedback.

To clarify the statistical analyses used, we included a new supplementary dataset with all statistical analyses and p-values indicated per graph. Furthermore, figure legends now include the information on the exact statistical test used in each case.

Regarding mosquito experiments, while we indeed reported a reduction in transmission and oocysts numbers we are aware that this effect might be due to the high variability in mosquito feeding assays. To highlight this point, we deleted the sentence "with the transmission reduction of [numbers]...." and we included the sentence "The high variability encountered in the standard membrane feeding assays, though, partially obstructs a clear conclusion on the biological relevance of the observed reduction in oocyst numbers"

More specific comments to address: Line 101/Fig1E (and figure legend) - What is this heatmap showing. It would be helpful to have a sentence or two linking it to a specific methodology. I could not find details in the M+M section and "specialized, high molecular mass gels" does not adequately explain what experiments were performed. The reference to Supplementary Information 1 also did not provide information.

We added the information "high molecular mass gels with lower acrylamide percentage" to clarify methodology in the text. Furthermore, we extended the figure legend to include all relevant information. Further experimental details can be found in the study cited in this context, where the dataset originates from (Evers et al., 2021).

Line 115 and Supplementary Figure 2C + D - The main text says that the transgenic parasites contained a mitochondrially localized mScarlet for visualization and localization, but in the supplementary figure 2 it shows mitotracker labelling rather than mScarlet. This is very confusing. The figure legend also mentions both mScarlet and MitoTracker. I assume that mScarlet was used to view in regular IFAs (Fig S2C) and the MitoTracker was used for the expansion microscopy (Fig S2D)? Please clarify.

We thank the reviewer for pointing this out - this was indeed incorrectly annotated. We used the endogenous mito-mScarlet signal in IFA and mitoTracker in U-ExM. The figure annotation has now been corrected.

Figure 2C - what is the statistical test being used (the methods say "Mean oocysts per midgut and statistical significance were calculated using a generalized linear mixed effect model with a random experiment effect under a negative binomial distribution." but what test is this?)?

The statistic test is now included in the material and method section with the sentence "The fitted model was used to obtain estimated means and contrasts and were evaluated using Wald Statistics". The test is now also mentioned in the figure legend.

Also the choice of a log10 scale for oocyst intensity is an unusual choice - how are the mosquitoes with 0 oocysts being represented on this graph? It looks like they are being plotted at 10^-1 (which would be 0.1 oocysts in a mosquito which would be impossible).

As the data spans three orders of magnitude with low values being biologically meaningful, we decided that a log scale would best facilitate readability of the graph. As the 0 values are also important to show, we went with a standard approach to handle 0s in log transformed data and substituted the 0s with a small value (0.001). We apologize for not mentioning this transformation in the manuscript. To make this transformation transparent, we added a break at the lower end of the log‑scaled y‑axis and relabelled the lowest tick as '0'. This ensures that mosquitoes with zero oocysts are shown along the x‑axis without being assigned an artificial value on the log scale. We would furthermore like to highlight that for statistics we used the true value 0 and not 0.001.

Figure 2D - it is great that the data from all feeding replicates has been shared, however it is difficult to conclude any meaningful impact in transmission with the knock-out lines when there is so much variation and so few mosquitoes dissected for some datapoints (10 mosquitoes are very small sample sizes). For example, Exp1 shows a clear decrease in mic19- transmission, but then Exp2 does not really show as great effect. Similarly, why does the double knock out have better transmission than the single knockouts? Sure there would be a greater effect?

We agree with the reviewer and with the new sentence added, as per major point, we hope we clarified the concept. Note that original Figure 2D has been moved to the supplementary information, as per minor comment of another reviewer.

Figure 3 legend - Please add which statistical test was used and the number of replicates.

Done

Figure 4 legend - Please add which statistical test was used and the number of replicates.

Done. Regarding replicates, note that while we measured over 100 cristae from over 30 mitochondria, these all stem from the same parasite culture.

Figure 5C - the 3D reconstructions are very nice, but what does the red and yellow coloring show?

Indeed, the information was missing. We added it to the figure legend.

Line 352 - "Still, it is striking that, despite the pronounced morphological phenotype, and the possibly high mitochondrial stress levels, the parasites appeared mostly unaffected in life cycle propagation, raising questions about the functional relevance of mitochondria at these stages." How do the authors reconcile this statement with the proven fact that mitochondria-targeted antimalarials (such as atovaquone) are very potent inhibitors of parasite mosquito transmission?

Our original sentence was reductive. What we wanted to state was related to the functional relevance of crista architecture and overall mitochondrial morphology rather than the general functional relevance of the mitochondria. We changed the sentence accordingly.

Furthermore, even though we do not discuss this in the article, we are aware of mitochondria targeting drugs that are known to block mosquito transmission. We want to point out that it is difficult to discern the disruption of ETC and therefore an impact on energy conversion with the impact on the essential pathway of pyrimidine synthesis, highly relevant in microgamete formation. Still, a recent paper from Sparkes et al. 2024 showed the essentiality of mitochondrial ATP synthesis during gametogenesis so it is very likely that the mitochondrial energy conversion is highly relevant for transmission to the mosquito.

Reviewer #1 (Significance (Required)):

This manuscript is a novel approach to studying mitochondrial biology and does open a lot of unanswered questions for further research directions. Currently there are limitations in the use of statistical tests and detail of methodology, but these could be easily be addressed with a bit more analysis/better explanation in the text. This manuscript could be of interest to readers with a general interest in mitochondrial cell biology and those within the specific field of Plasmodium research. My expertise is in Plasmodium cell biology.

We thank the reviewer for the praise.

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

Major comments: 1) In my opinion, the authors tend to sensationalize or overinterpret their results. The title of the manuscript is very misleading. While MICOS is certainly important for crista formation, it is not the only factor, as ATP synthase dimer rows make a highly significant contribution to crista morphology. Thus, one can argue with equal validity that ATP synthase should be considered the 'architect', as it's the conformation of the dimers and rows modulate positive curvature. Secondly, while cristae are still formed upon mic60/mic19 gene knockout (KO), they are severely deformed, and likely dysfunctional (see below). Thus, I do not agree with the title that MICOS is dispensable for crista formation, because the authors results show that it clearly is essential. So, the title should be changed.

We thank the reviewer for taking the time to review our manuscript.

Based on the reviewers' interpretation we conclude the title does not come across as intended. We have changed the title to: "The role of MICOS in organizing mitochondrial cristae in malaria parasites"

The Discussion section starting from line 373 also suffers from overinterpretation as well as being repetitive and hard to understand. The authors infer that MICOS stability is compromised less in the single KOs (sKO) in compared to the mic60/mic19 double KO (dKO). MICOS stability was never directly addressed here and the composition of the MICOS complex is unaddressed, so it does not make sense to speculate by such tenuous connections. The data suggest to me that mic60 and mic19 are equally important for crista formation and crista junction (CJ) stabilization, and the dKO has a more severe phenotype than either KO, further demonstrating neither is epistatic.

We do agree with the reviewer's notion that we did not address complex stability, and our wording did not make this sufficiently clear. We shortened and rephrased the paragraph in question.

The following paragraphs (line 387 to 422) continues with such unnecessary overinterpretation to the point that it is confusing and contradictory. Line 387 mentions an 'almost complete loss of CJs' and then line 411 mentions an increase in CJ diameter, both upon Mic60 ablation. I do not think this discussion brings any added value to the manuscript and should be shortened. Yes, maybe there are other putative MICOS subunits that may linger in the KOS that are further destabilized in the dKO, or maybe Mic60 remains in the mic19 KO (and vice versa) to somehow salvage more CJs, which is not possible in the dKO. It is impossible to say with confidence how ATP synthase behaves in the KOs with the current data.

We shortened this paragraph.

2) While the authors went through impressive lengths to detect any effect on lifecycle progression, none was found except for a reduction in oocyte count. However, the authors did not address any direct effect on mitochondria, such as OXPHOS complex assembly, respiration, membrane potential. This seems like a missed opportunity, given the team's previous and very nice work mapping these complexes by complexome profiling. However, I think there are some experiments the authors can still do to address any mitochondrial defects using what they have and not resorting to complexome profiling (although this would be definitive if it is feasible):

i) Quantification of MitoTracker Red staining in WT and KOs. The authors used this dye to visualize mitochondria to assay their gross morphology, but unfortunately not to assay membrane potential in the mutants. The authors can compare relative intensities of the different mitochondria types they categorized in Fig. 3A in 20-30 cells to determine if membrane potential is affected when the cristae are deformed in the mutants. One would predict they are affected.

Interesting suggestion. As our staining and imaging conditions are suitable for such analysis (as demonstrated by Sarazin et al., 2025, https://www.biorxiv.org/content/10.1101/2025.11.27.690934v1), we performed the measurements on the same dataset which we collected for Figure 3. We did, however, not detect any difference in mitotracker intensity between the different lines. The result of this analysis is included in the new version of Supplementary figure S6.

ii) Sporozoites are shown in Fig S5. The authors can use the same set up to track their motion, with the hypothesis that they will be slower in the mutants compared to WT due to less ATP. This assumes that sporozoite mitochondria are active as in gametocytes.

While theoretically plausible and informative, we currently do not know the relevance of mitochondrial energy conversion for general sporozoite biology or specifically features of sporozoite movement. Given the required resources and time to set this experiment up and the uncertainty whether it is a relevant proxy for mitochondrial functioning, we argue it is out of scope for this manuscript.

iii) Shotgun proteomics to compare protein levels in mutants compared to WT, with the hypothesis that OXPHOS complex subunits will be destabilized in the mutants with deformed cristae. This could be indirect evidence that OXPHOS assembly is affected, resulting in destabilized subunits that fail to incorporate into their respective complexes.

While this experiment could potentially further our understanding of the interaction between MICOS and levels of OXPHOS complex subunits we argue that the indirect nature of the evidence does not justify the required investments.

To expedite resubmission, the authors can restrict the cell lines to WT and the dKO, as the latter has a stronger phenotype that the individual KOs and conclusions from this cell line are valid for overall conclusions about Plasmodium MICOS.

I will also conclude that complexome/shotgun proteomics may be a useful tool also for identifying other putative MICOS subunits by determining if proteins sharing the same complexome profile as PfMic60 and Mic19 are affected. This would address the overinterpretation problem of point 1.

3) I am aware of the authors previous work in which they were not able to detect cristae in ABS, and thus have concluded that these are truly acristate. This can very well be true, or there can be immature cristae forms that evaded detection at the resolution they used in their volumetric EM acquisitions. The mitochondria and gametocyte cristae are pretty small anyway, so it not unreasonable to assume that putative rudimentary cristae in ABS may be even smaller still. Minute levels of sampled complex III and IV plus complex V dimers in ABS that were detected previously by the authors by complexome profiling would argue for the presence of miniscule and/or very few cristae.

I think that authors should hedge their claim that ABS is acrisate by briefly stating that there still is a possibility that miniscule cristae may have been overlooked previously.

We acknowledge that we cannot demonstrate the absolute absence of any membrane irregularities along the inner mitochondrial membrane. At the same time, if such structures were present, they would be extremely small and unlikely to contain the full set of proteins characteristic of mature cristae. For this reason, we consider it appropriate to classify ABS mitochondria as acristate. To reflect the reviewer's point while maintaining clarity for readers, we have slightly adjusted our wording in the manuscript, changing 'fully acristate' to 'acristate'.

This brings me to the claim that Mic19 and Mic60 proteins are not expressed in ABS. This is based on the lack of signal from the epitope tag; a weak signal is detected in gametocytes. Thus, one can counter that Mic19 and Mic60 are also expressed, but below the expression limits of the assay, as the protein exhibits low expression levels when mitochondrial activity is upregulated.

We agree with the reviewer that the absence of a detectable epitope‑tag signal does not definitively exclude low‑level expression, and we have therefore replaced the term 'absent' with 'undetectable' throughout the manuscript. In context with previous findings of low-level transcripts of the proteins in a study by Lopez-Berragan et al. and Otto et al., we also added the sentence "The apparent absence could indicate that transcripts are not translated in ABS or that the proteins' expression was below detection limits of western blot analysis." to the discussion. _At the same time, we would like to clarify that transcript levels for both genes fall within the

To address this point, the authors should determine of mature mic60 and mic19 mRNAs are detected in ABS in comparison to the dKO, which will lack either transcript. RT-qPCR using polyT primers can be employed to detect these transcripts. If the level of these mRNAs are equivalent to dKO in WT ABS, the authors can make a pretty strong case for the absence of cristae in ABS.

We appreciate the reviewer's suggestion. As noted in the Discussion, existing transcriptomic datasets already show detectable MIC19 and MIC60 mRNAs in ABS. For this reason, we expect RT-qPCR to reveal low (but not absent) levels of both transcripts, unlike the true loss expected to be observed in the dKO. Because such residual signals have been reported previously and their biological relevance remains uncertain, we do not believe transcript levels alone can serve as a definitive indicator of cristae absence in ABS.

They should highlight the twin CX9C motifs that are a hallmark of Mic19 and other proteins that undergo oxidative folding via the MIA pathway. Interestingly, the Mia40 oxidoreductase that is central to MIA in yeast and animals, is absent in apicomplexans (DOI: 10.1080/19420889.2015.1094593).

Searching for the CX9C motifs is a valuable suggestion. In response to the reviewer´s suggestion we analysed the conservation of the motif in PfMIC19 and included this in a new figure panel (Figure 1 F).

Did the authors try to align Plasmodium Mic19 orthologs with conventional Mic19s? This may reveal some conserved residues within and outside of the CHCH domain.

In response to this comment we made Figure 1 F, where we show conserved residues within the CHCH domains of a broad range of MIC19 annotated sequences across the opisthokonts, and show that the Cx9C motifs are conserved also in PfMIC19. Outside the CHCH domain, we did not find any meaningful conservation, as PfMIC19 heavily diverges from opisthokont MIC19.

5) Statistcal significance. Sometimes my eyes see population differences that are considered insignificant by the statistical methods employed by the authors, eg Fig. 4E, mutants compared to WT, especially the dKO. Have the authors considered using other methods such as student t-test for pairwise comparisons?

The graphs in figures 3, 4 and 5 got a makeover, such that they now are in linear scale and violin plots (also following a suggestion from further down in the reviewer's comments). We believe that this improves interpretability. ANOVA was kept as statistical testing to assure the correction for multiple comparisons that cannot be performed with standard t-test. A full overview of statistics and exact p-values can also be found in the newly added supplementary information 2.

Minor comments: Line 33. Anaerobes (eg Giardia) have mitochondria that do produce ATP, unlike aerobic mitochondria

We acknowledge that producing ATP via OXPHOS is not a characteristic of all mitochondria-like organelles (e.g. mitosomes), which is why these are typically classified separately from canonical mitochondria. When not considering mitochondria-like organelles, energy conversion is the function that the mitochondrion is most well-known for and the one associated with cristae.

Line 56: Unclear what authors mean by "canonical model of mitochondria"

To clarify we changed this to "yeast or human" model of mitochondria.

Lines 75-76: This applies to Mic10 only

We removed the "high degree of conservation in other cristate eukaryotes" statement.

Line 80: Cite DOI: 10.1016/j.cub.2020.02.053

Done

Fig 2D: I find this table difficult to read. If authors keep table format, at least get rid of 'mean' column' as this data is better depicted in 2C. I suggest depicted this data either like in 3B depicting portion of infected vs unaffected flies in all experiments, then move modified Table to supplement. Important to point out experiment 5 appears to be an outlier with reduced infectivity across all cell lines, including WT.

To clarify: the mean reported in the table indicates the mean per replicate while the mean reported in figure 2C is the overall mean for a given genotype that corrects for variability within experiments. We agree that moving the table to the supplementary data is a good idea. We decided to not include a graph for infected and non-infected mosquitoes as this information would be partially misleading, highlighting a phenotype we argue to be influenced by the strong variability.

Fig. 3C-G: I feel like these data repeatedly lead to same conclusions. These are all different ways of showing what is depicted in Fig 2B: mitochondria gross morphology is affected upon ablation of MICOS. I suggest that these graphs be moved to supplement and replaced by the beautiful images.

Thank you for the nice comment on our images. We have now moved part of the graphs to supplementary figure 6 and only kept the Relative Frequency, Sphericity and total mitochondria volume per cell in the main figure.

Line 180: Be more specific with which tubulin isoform is used as a male marker and state why this marker was used in supplemental Fig S6.

We have now specified the exact tubulin isoform used as the male gametocyte marker, both in the main text and in Supplementary Fig. S6. This is a commercial antibody previously known to work as an effective male marker, which is why we selected it for this experiment. This is now clearly stated in the manuscript.

Line 196 and Fig 3C: the word 'intensities' in this context is very ambiguous. Please choose a different term (puncta, elements, parts?). This is related to major point 2i above.

To clarify the biological effect that we can conclude form the measurement, we added an explanation about it in the respective section of the results, and we decided to replace the raw results of the plug-in readout with the deduced relative dispersion.

Line 222: Report male/female crista measurements

We added Supplementary information 2, which contains exact statistical test and outcomes on all presented quantifications as well as a per-sex statistical analysis of the data from figure 4. Correspondingly, we extended supplementary information 2 by a per-sex colour code for the thin section TEM data.

Fig. 4B-E: depict data as violin plots or scatter plots like Fig. 2C to get a better grasp of how the crista coverage is distributed. It seems like the data spread is wider in the double KO. This would also solve the problem with the standard deviation extending beyond 0%.

We changed this accordingly.

Lines 331-333: Please clarify that this applies for some, but not all MICOS subunits. Please also see major point 1 above. Also, the authors should point out that despite their structural divergence, trypanosomal cryptic mitofilins Mic34 and Mic40 are essential for parasite growth, in contrast to their findings with PfMic60 (DOI: https://doi.org/10.1101/2025.01.31.635831).

This has been changed accordingly.

Line 320: incorrect citation. Related to point 1above.

Correct citation is now included in the text.

Lines 333-335. This is related to the above. Again, some subunits appear to affect cell growth under lab conditions, and some do not. This and the previous sentence should be rewritten to reflect this.

This has been changed accordingly.

Line 343-345: The sentence and citation 45 are strange. Regarding the former, it is about CHCHD10, whose status as a bona fide MICOS subunit is very tenuous, so I would omit this. About the phenomenon observed, I think it makes more sense to write that Mic60 ablation results in partially fragmented mitochondria in yeast (Rabl et al., 2009 J Cell Biol. 185: 1047-63). A fragmented mitochondria is often a physiological response to stress. I would just rewrite as not to imply that mitochondrial fission (or fusion) is impaired in these KOs, or at least this could be one of several possibilities.

The sentence has been substituted following the indication of the reviewer. Though we still include the data of the human cells as this has also been shown in Stephens et al. 2020.

Line 373: 'This indicates' is too strong. I would say 'may suggest' as you have no proof that any of the KOs disrupts MICOS. This hypothesis can be tested by other means, but not by penetrance of a phenotype.

Done

Line 376-377; 'deplete functionality' does not make sense, especially in the context of talking about MICOS subunit stability. In my opinion, this paragraph overinterprets the KO effects on MICOS stability. None of the experiments address this phenomenon, and thus the authors should not try to interpret their results in this context. See major point 1. Other suggestions for added value

We removed the sentence. Also, the entire paragraph has been shortened, restructured and wording was changed to address major point 1.

1) Does Plasmodium Sam50 co-fractionate with Mic60 and Mic19 in BN PAGE (Fig. 1E)

While we did identify SAMM50 in our BN PAGE, the protein does not co-migrate with the MICOS components but instead comigrates with other components of a putative sorting and assembly machinery (SAM) complex. As SAMM50, the SAM complex and the overarching putative mitochondrial membrane space bridging (MIB) complex are not mentioned in the manuscript, we decided to not include the information in the figure.

Reviewer #2 (Significance (Required)):

The manuscript by Tassan-Lugrezin is predicated on the idea that Plasmodium represents the only system in which de novo crista formation can be studied. They leverage this system to ask the question whether MICOS is essential for this process. They conclude based on their data that the answer is no, which the authors consider unprecedented. But even if their claim is true that ABS is acristate, this supposed advantage does not really bring any meaningful insight into how MICOS works in Plasmodium.

First the positives of this manuscript. As has been the case with this research team, the manuscript is very sophisticated in the experimental approaches that are made. The highlights are the beautiful and often conclusive microscopy performed by the authors. Only the localization of Mic60 and Mic19 was inconclusive due to their very low expression unfortunately.

The examination of the MICOS mutants during in vitro life cycle of Plasmodium falciparum is extremely impressive and yields convincing results. Mitochondrial deformation is tolerated by life cycle stage differentiation, with a modest but significant reduction of oocyte production, being observed.

However, despite the herculean efforts of the authors, the manuscript as it currently stands represents only a minor advance in our understanding of the evolution of MICOS, which from the title and focus of the manuscript, is the main goal of the authors. In its current form, the manuscript reports some potentially important findings:

1) Mic60 is verified to play a role in crista formation, as is predicted by its orthology to other characterized Mic60 orthologs.

2) The discovery of a novel Mic19 analog (since the authors maintain there is no significant sequence homology), which exhibits a similar (or the same?) complexome profile with Mic60. This protein was upregulated in gametocytes like Mic60 and phenocopies Mic60 KO.

3) Both of these MICOS subunits are essential (not dispensable) for proper crista formation

4) Surprisingly, neither MICOS subunit is essential for in vitro growth or differentiation from ABS to sexual stages, and from the latter to sporozoites. This says more about the biology of plasmodium itself than anything about the essentiality of Mic60, ie plasmodium life cycle progression tolerates defects to mitochondrial morphology. But yes, I agree with the authors that Mic60's apparent insignificance for cell growth in examined conditions does differ with its essentiality in other eukaryotes. But fitness costs were not assayed (eg by competition between mutants and WT in infection of mosquitoes)

5) Decreased fitness of the mutants is implied by a reduction of oocyte formation.

While interesting in their own way, collectively they do not represent a major advance in our understanding of MICOS evolution. Furthermore, the findings bifurcate into categories informing MICOS or Plasmodium biology. Both aspects are somewhat underdeveloped in their current form.

This is unfortunate because there seem to be many missed opportunities in the manuscript that could, with additional experiments, lead to a manuscript with much wider impact. For me, what is remarkable about Plasmodium MICOS that sets it apart from other iterations is the apparent absence of the Mic10 subunit. Purification of plasmodium MICOS via the epitope tagged Mic60 and Mic19 could have verified that MICOS is assembled without this core subunit. Perhaps Mic60 and Mic19 are the vestiges of the complex, and thus operate alone in shaping cristae. Such a reduction may also suggest the declining importance of mitochondria in plasmodium.

Another missed opportunity was to assay the impact of MICOS-depletion of OXPHOS in plasmodium. This is a salient issue as maybe crista morphology is decoupled from OXPHOS capacity in Plasmodium, which links to the apparent tolerance of mitochondrial morphology in cell growth and differentiation. I suggested in section A experiments to address this deficit.

Finally, the authors could assay fitness costs of MICOS-ablation and associated phenotypes by assaying whether mosquito infectivity is reduced in the mutants when they are directly competing with WT plasmodium. Like the authors, I am also surprised that MICOS mutants can pass population bottlenecks represented by differentiation events. Perhaps the apparent robustness of differentiation may contribute plasmodium's remarkable ability to adapt.

I realize that the authors put a lot of efforts into their study and again, I am very impressed by the sophistication of the methods employed. Nevertheless, I think there is still better ways to increase the impact of the study aside from overinterpreting the conclusions from the data. But this would require more experiments along the lines I suggest in Section A and here.

We thank the reviewer for their extensive analysis of the significance of our findings, including the compliments on our microscopy images and the sophisticated experimental approaches. We hope we have convincingly argued why we could or could not include some of the additional analyses suggested by the reviewer in section 1 above.

With regard to the significance statement, we want to point out that our finding that PfMICOS is not needed for initial formation of cristae (as opposed to organization thereof), is a confirmation of something that has been assumed by the field, without being the actual focus of studies. We argue that the distinction between formation and organization of cristae is important and deserves some attention within the manuscript. The result of MICOS not being involved in the initial formation of cristae, we argue to be relevant in Plasmodium biology and beyond. As for the insights into how MICOS works in Plasmodium we have confirmed that the previously annotated PfMIC60 is indeed involved in the organization of cristae. Furthermore, we have identified and characterized PfMIC19. These findings, we argue, are indeed meaningful insights into PfMICOS.

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

Summary:

MICOS is a conserved mitochondrial protein complex responsible for organising the mitochondrial inner membrane and the maintenance of cristae junctions. This study sheds first light on the role of two MICOS subunits (Mic60 and the newly annotated Mic19) in the malaria parasite Plasmodium falciparum, which forms cristae de novo during sexual development, as demonstrated by EM of thin section and electron tomography. By generating knockout lines (including a double knockout), the authors demonstrate that knockout of both MICOS subunits leads to defects in cristae morphology and a partial loss of cristae junctions. With a formidable set of parasitological assays, the authors show that despite the metabolically important role of mitochondria for gametocytes, the knockout lines can progress through the life stages and form sporozoites, albeit with diminished infection efficiency.

We thank the reviewer for their time and compliment.

Major comments:

1) The authors should improve to present their findings in the right context, in particular by:

(i) giving a clearer description in the introduction of what is already known about the role of MICOS. This starts in the introduction, where one main finding is missing: loss of MICOS leads to loss of cristae junctions and the detachment of cristae membranes, which are nevertheless formed, but become membrane vesicles. This needs to be clearly stated in the introduction to allow the reader to understand the consistency of the authors' findings in P. falciparum with previous reports in the literature.

We extended the introduction to include this information.

(ii) at the end to the introduction, the motivating hypothesis is formulated ad hoc "conclusive evidence about its involvement in the initial formation of cristae is still lacking" (line 83). If there is evidence in the literature that MICOS is strictly required for cristae formation in any organism, then this should be explained, because the bona fide role of MICOS is maintenance of cristae junctions (the hypothesis is still plausible and its testing important).

To clarify we rephrased the sentence to: "Although MICOS has been described as an organizer of crista junctions, its role during the initial formation of nascent cristae has not been investigated."

2) Line 96-97: "Interestingly, PfMIC60 is much larger than the human MICOS counterpart, with a large, poorly predicted N-terminal extension." This statement is lacking a reference and presumably refers to annotated ORFs. The authors should clarify if the true N-terminus is definitely known - a 120kDa size is shown for the P. falciparum but this is not compared to the expected length or the size in S. cerevisiae.

To solve the reference issue, we added the uniprot IDs we compared to see that the annotated ORF is bigger in Plasmodium. We also changed the comparison to yeast instead of human, because we realized it is confusing to compare to yeast all throughout the figure, but then talk about human in this specific sentence.

Regarding whether the true N-terminus is known. Short answer: No, not exactly.

However, we do know that the Pf version is about double the size of the yeast protein.

As the reviewer correctly states, we show the size of 120kDa for the tagged protein in Figure 1G. Considering that we tagged the protein C-terminally, and observed a 120kDa product on western blot, it is safe to conclude that the true N-terminus does not deviate massively from the annotated ORF, and hence, that there is a considerable extension of the protein beyond a 60kDa protein. We do not directly compare to yeast MIC60 on our western blots, however, that comparison can be drawn from literature: Tarasenko et al., 2017 showed that purified MIC60 running at ~60kDa on SDS-PAGE actively bends membranes, suggesting that in its active form, the monomer of yeast MIC60 is indeed 60kDa in size.

To clarify, we now emphasize that we ran the Alphafold prediction on the annotated open reading frame (annotated and sequenced by Bohme et al. and Chapell et al. now cited in the manuscript), and revised the wording to make clear what we are comparing in which sentence.

3) lines 244-245: "Furthermore, our data indicates the effect size increases with simultaneous ablation of both proteins?". The authors should explain which data they are referring to, as some of the data in Fig 3 and 4 look similar and all significance tests relate to the wild type, not between the different mutants, so it is not clear if any overserved differences are significant. The authors repeat this claim in the discussion in lines 368-369 without referring to a specific significance test. This needs to be clarified.

As a reply to this and other comments from the reviewers we added the multiple testing within all samples. In addition, to clarify statistics used we included a supplementary dataset with all p-values and statistical tests used.

4) lines 304-306: "Though well established as the cristae organizing system, the role of MICOS in initial formation of cristae remains hidden in model organisms that constitutively display cristae.". This sentence is misleading since even in organisms that display numerous cristae throughout their life cycle, new cristae are being formed as the cells proliferate. Thus, failure to produce cristae in MICOS knockout lines would have been observable but has apparently not been reported in the literature. Thus, the concerted process in P. falciparum makes it a great model organism, but not fundamentally different to what has been studied before in other organisms.

We deleted this statement.

5) lines 373-378. "where ablation of just MIC60 is sufficient to deplete functionality of the entire MICOS (11, 15),". The authors' claim appears to be contrary to what is actually stated in ref 15, which they cite:

"MICOS subunits have non-redundant functions as the absence of both MICOS subcomplexes results in more severe morphological and respiratory growth defects than deletion of single MICOS subunits or subcomplexes."

This seems in line with what the authors show, rather than "different".

This sentence has been removed.

6) lines 380-385: "... thus suggesting that membrane invaginations still arise, but are not properly arranged in these knockout lines. This suggests that MICOS either isn't fully depleted,...". These conclusions are incompatible with findings from ref. 15, which the authors cite. In that study, the authors generated a ∆MICOS line which still forms membrane invaginations, showing that MICOS is not required at all for this process in yeast. Hence the authors' implication that MICOS needs to be fully depleted before membrane invaginations cease to occur is not supported by the literature.

This sentence has been deleted in the revised version of the manuscript.

Minor comments:

7) The authors should consider if the first part of their title could be seen as misleading: It suggests that MICOS is "the architect" in cristae formation, but this is not consistent with the literature nor their own findings.

Title is changed accordingly

Minor comments:

• Line 43, of the three seminal papers describing the discovery of MICOS in 2011, the authors only cite two (refs 6 and 7), but miss the third paper, Hoppins et al, PMID: 21987634, which should probably be corrected.

Done, the paper is now cited

• Page 2, line 58: for a more complete picture the authors should also cite the work of others here which shows that although at very low levels, e.g. complex III (a drug target) and ATP synthase do assemble (Nina et al, 2011, JBC).

Done

• Page 3, line 80: "Irrespective of the shape of an organism's cristae, the crista junctions have been described as tubular channels that connect the cristae membrane to the inner boundary membrane (22, 24)." This omits the slit-shaped cristae junctions found in yeast (Davies et al, 2011, PNAS), which the authors should include.

The paper and concept have been added to the manuscript, though the sentence has been moved up in the introduction, when crista junctions are first introduced.

• Line 97: "poorly predicted N-terminal extension", as there is no experimental structure, we don't know if the prediction is poor. Presumably the authors mean either poorly ordered or the absence of secondary structure elements, or the poor confidence score for that region in the prediction? This should be clarified or corrected.

We were referring to the poor confidence score. To address this comment as well as major point 2, we rewrote the respective paragraph. It now clearly states that confidence of the prediction is low, and we mention the tool that was used to identify conserved domains (Topology-based Evolutionary Domains).

• Line 98: "an antiparallel array of ten β-sheets". They are actually two parallel beta-sheets stacked together. The authors could find out the name of this fold, but the confidence of the prediction is marked a low/very low. So, its existence is unknown, not just its "function".

We adapted the domain description to "a stack of two parallel beta-sheets" and replaced the statement on unknown function by the statement "Because this domain is predicted solely from computational analysis, both its actual existence in the native protein and its biological function remain unknown."

Fig 1B: The authors show two alphafold predictions of S. cerevisiae and P. falciparum Mic60 structures. There is however an experimental Mic60/19 (fragment) structure from the former organism (PMID: 36044574), which should be included if possible

We appreciate the reviewer's suggestion and note that the available structural data indeed provides valuable insight into how MIC60 and MIC19 interact. However, these structures represent fusion constructs of limited protein fragments and therefore capture only a small portion of each protein, specifically the interaction interface. Because our aim in Fig. 1B is to compare the overall domain architecture of the full‑length proteins, we believe that including fragment‑based structures would be less informative in this context.

Line: 318-321: "The same trend was observed for PfMIC19 and PfMIC60. Although transcriptomic data suggested that low-level transcripts of PfMIC19 and PfMIC60 are present in ABS (38), we did not detect either of the proteins in ABS by western blot analysis. While this statement is true, the authors should comment on the sensitivity of the respective methods - how well was the antibody working in their hands and how do they interpret the absence of a WB band compared to transcriptomics data?

The HA antibody used in our experiments is a standard commercial reagent that performs reliably in both WB and IFA, although it shows a low background signal in gametocytes. We agree that the sensitivity of the method and the interpretation of weak or absent bands should be addressed explicitly. Transcript levels for both PfMIC19 and PfMIC60 in asexual blood stages fall within the

• Lines 322-323: would the authors not typically have expected an IFA signal given the strength of the band in Western blot? If possible, the authors should comment if the negative fluorescence outcome can indeed be explained with the low abundance or if technical challenges are an equally good explanation.

Considering the nature of the investigated proteins (embedded in the IMM and spread throughout the mitochondria) difficulties in achieving a clear signal in IFA or U-ExM are not very surprizing. While epitopes may remain buried in IFA, U-ExM usually increases accessibility for the antibodies. However, U-ExM comes at the cost of being prone to dotty background signals, therefore potentially hiding low abundance, naturally dotty signals such as the signal of MICOS proteins that localize to distinct foci (at the CJ) along the mitochondrion. Current literature suggests that, in both human and yeast, STED is the preferred method for accurate spatial resolution of MICOS proteins (https://www.ncbi.nlm.nih.gov/pubmed/32567732,https://www.ncbi.nlm.nih.gov/pubmed/32067344). Unfortunately, we do not have experience with, nor access to, this particular technique/method.

Lines 357-365: the authors describe limitations of the applied methods adequately. Perhaps it would be helpful to make a similar statement about the analysis of 3D objects like mitochondria and cristae from 2D sections. E.g. the apparent cristae length depends on whether cristae are straight (e.g. coiled structures do not display long cross sections despite their true length in 3D).

The limitations of other methods are described in the respective results section.

We added a clarifying sentence in the results section of Figure 4:

"Note that such measurements do not indicate the true total length or width of cristae, as the data is two-dimensional. The recorded values are to be considered indicative of possible trends, rather than absolute dimensions of cristae."

This statement refers to the length/width measurements of cristae.

In the context of Figure 4 D we mention the following (see preprint lines 229 - 230): "We expect this effect to translate into the third dimension and thus conclude that the mean crista volume increases with the loss of either PfMIC19,PfMIC60, or both."

For Figure 5, we included a clarifying statement in the results section of the preprint (lines 269 - 273): "Note that these mitochondrial volumes are not full mitochondria, but large segments thereof. As a result of the incompleteness of the mitochondria within the section, and the tomography specific artefact of the missing wedge, we were unable to confirm whether cristae were in fact fully detached from the boundary membrane, or just too long to fit within the observable z-range. "

Line 404: perhaps undetected or similar would be a better description than "hidden"?

The sentence does not exist in the revised manuscript

Reviewer #3 (Significance (Required)):

The main strength of the study is that it provides the first characterisation of the MICOS complex in P. falciparum, a human parasite in which the mitochondrion has been shown to be a drug target. Mic60 and the newly annotated Mic19 are confirmed to be essential for proper cristae formation and morphology, as well as overall mitochondrial morphology. Furthermore, the mutant lines are characterised for their ability to complete the parasite life cycle and defects in infection effectivity are observed. This work is an important first step for deciphering the role of MICOS in the malaria parasite and the composition and function of this complex in this organism. The limitation of the study stems from what is already known about MICOS and its subunits in

great detail in yeast and humans with similar findings regarding loss of cristae and cristae defects. The findings of this study do not provide dramatic new insight on MICOS function or go substantially beyond the vast existing literature in terms of the extent of the study, which focuses on parasitological assays and morphological analysis. Exploring the role of MICOS in an early-divergent organism and human parasite is however important given the divergence found in mitochondrial biology and P. falciparum is a uniquely suited model system. One aspect that would increase the impact of the paper would be if the authors could mechanistically link the observed morphological defects to the decreased infection efficiency, e.g. by probing effects on mitochondrial function. This will likely be challenging as the morphological defects are diverse and the fitness defects appear moderate/mild.

As suggested by Reviewer 2, we examined mitochondrial membrane potential in gametocytes using MitoTracker staining and did not observe any obvious differences associated with the morphological defects. At present, additional assays to probe mitochondrial function in P. falciparum gametocytes are not sufficiently established, and developing and validating such methods would require substantial work before they could be applied to our mutant lines. For these reasons, a more detailed mechanistic link between the observed morphological changes and the reduced infection efficiency is currently beyond reach.

The advance presented in this study is to pioneer the study of MICOS in P. falciparum, thus widening our understanding of the role of this complex to different model organism. This study will likely be mainly of interest for specialised audiences such as basic research parasitologists and mitochondrial biologists. My own field of expertise is mitochondrial biology and structural biology.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #2

Evidence, reproducibility and clarity

Major comments:

1) In my opinion, the authors tend to sensationalize or overinterpret their results. The title of the manuscript is very misleading. While MICOS is certainly important for crista formation, it is not the only factor, as ATP synthase dimer rows make a highly significant contribution to crista morphology. Thus, one can argue with equal validity that ATP synthase should be considered the 'architect', as it's the conformation of the dimers and rows modulate positive curvature. Secondly, while cristae are still formed upon mic60/mic19 gene knockout (KO), they are severely deformed, and likely dysfunctional (see below). Thus, I do not agree with the title that MICOS is dispensable for crista formation, because the authors results show that it clearly is essential. So, the title should be changed.

The Discussion section starting from line 373 also suffers from overinterpretation as well as being repetitive and hard to understand. The authors infer that MICOS stability is compromised less in the single KOs (sKO) in compared to the mic60/mic19 double KO (dKO). MICOS stability was never directly addressed here and the composition of the MICOS complex is unaddressed, so it does not make sense to speculate by such tenuous connections. The data suggest to me that mic60 and mic19 are equally important for crista formation and crista junction (CJ) stabilization, and the dKO has a more severe phenotype than either KO, further demonstrating neither is epistatic.

The following paragraphs (line 387 to 422) continues with such unnecessary overinterpretation to the point that it is confusing and contradictory. Line 387 mentions an 'almost complete loss of CJs' and then line 411 mentions an increase in CJ diameter, both upon Mic60 ablation. I do not think this discussion brings any added value to the manuscript and should be shortened. Yes, maybe there are other putative MICOS subunits that may linger in the KOS that are further destabilized in the dKO, or maybe Mic60 remains in the mic19 KO (and vice versa) to somehow salvage more CJs, which is not possible in the dKO. It is impossible to say with confidence how ATP synthase behaves in the KOs with the current data.

2) While the authors went through impressive lengths to detect any effect on lifecycle progression, none was found except for a reduction in oocyte count. However, the authors did not address any direct effect on mitochondria, such as OXPHOS complex assembly, respiration, membrane potential. This seems like a missed opportunity, given the team's previous and very nice work mapping these complexes by complexome profiling. However, I think there are some experiments the authors can still do to address any mitochondrial defects using what they have and not resorting to complexome profiling (although this would be definitive if it is feasible):

i) Quantification of MitoTracker Red staining in WT and KOs. The authors used this dye to visualize mitochondria to assay their gross morphology, but unfortunately not to assay membrane potential in the mutants. The authors can compare relative intensities of the different mitochondria types they categorized in Fig. 3A in 20-30 cells to determine if membrane potential is affected when the cristae are deformed in the mutants. One would predict they are affected.

ii) Sporozoites are shown in Fig S5. The authors can use the same set up to track their motion, with the hypothesis that they will be slower in the mutants compared to WT due to less ATP. This assumes that sporozoite mitochondria are active as in gametocytes.

iii) Shotgun proteomics to compare protein levels in mutants compared to WT, with the hypothesis that OXPHOS complex subunits will be destabilized in the mutants with deformed cristae. This could be indirect evidence that OXPHOS assembly is affected, resulting in destabilized subunits that fail to incorporate into their respective complexes.

To expedite resubmission, the authors can restrict the cell lines to WT and the dKO, as the latter has a stronger phenotype that the individual KOs and conclusions from this cell line are valid for overall conclusions about Plasmodium MICOS.

I will also conclude that complexome/shotgun proteomics may be a useful tool also for identifying other putative MICOS subunits by determining if proteins sharing the same complexome profile as PfMic60 and Mic19 are affected. This would address the overinterpretation problem of point 1.

3) I am aware of the authors previous work in which they were not able to detect cristae in ABS, and thus have concluded that these are truly acristate. This can very well be true, or there can be immature cristae forms that evaded detection at the resolution they used in their volumetric EM acquisitions. The mitochondria and gametocyte cristae are pretty small anyway, so it not unreasonable to assume that putative rudimentary cristae in ABS may be even smaller still. Minute levels of sampled complex III and IV plus complex V dimers in ABS that were detected previously by the authors by complexome profiling would argue for the presence of miniscule and/or very few cristae.

I think that authors should hedge their claim that ABS is acrisate by briefly stating that there still is a possibility that miniscule cristae may have been overlooked previously.

This brings me to the claim that Mic19 and Mic60 proteins are not expressed in ABS. This is based on the lack of signal from the epitope tag; a weak signal is detected in gametocytes. Thus, one can counter that Mic19 and Mic60 are also expressed, but below the expression limits of the assay, as the protein exhibits low expression levels when mitochondrial activity is upregulated.

To address this point, the authors should determine of mature mic60 and mic19 mRNAs are detected in ABS in comparison to the dKO, which will lack either transcript. RT-qPCR using polyT primers can be employed to detect these transcripts. If the level of these mRNAs are equivalent to dKO in WT ABS, the authors can make a pretty strong case for the absence of cristae in ABS.

4) The major finding of the manuscript is of a Mic19 analog in plasmodium should be highlighted. As far as I know, this manuscript could represent the first instance of Mic19 outside of opisthokonts that was not found by sensitive profile HMM searches and certainly the first time such a Mic19 was functionally analyzed.

They should highlight the twin CX9C motifs that are a hallmark of Mic19 and other proteins that undergo oxidative folding via the MIA pathway. Interestingly, the Mia40 oxidoreductase that is central to MIA in yeast and animals, is absent in apicomplexans (DOI: 10.1080/19420889.2015.1094593).

Did the authors try to align Plasmodium Mic19 orthologs with conventional Mic19s? This may reveal some conserved residues within and outside of the CHCH domain.

5) Statistcal significance. Sometimes my eyes see population differences that are considered insignificant by the statistical methods employed by the authors, eg Fig. 4E, mutants compared to WT, especially the dKO. Have the authors considered using other methods such as student t-test for pairwise comparisons?

Minor comments:

Line 33. Anaerobes (eg Giardia) have mitochondria that do produce ATP, unlike aerobic mitochondria

Line 56: Unclear what authors mean by "canonical model of mitochondria"

Lines 75-76: This applies to Mic10 only

Line 80: Cite DOI: 10.1016/j.cub.2020.02.053

Fig 2D: I find this table difficult to read. If authors keep table format, at least get rid of 'mean' column' as this data is better depicted in 2C. I suggest depicted this data either like in 3B depicting portion of infected vs unaffected flies in all experiments, then move modified Table to supplement. Important to point out experiment 5 appears to be an outlier with reduced infectivity across all cell lines, including WT.

Fig. 3C-G: I feel like these data repeatedly lead to same conclusions. These are all different ways of showing what is depicted in Fig 2B: mitochondria gross morphology is affected upon ablation of MICOS. I suggest that these graphs be moved to supplement and replaced by the beautiful images

Line 180: Be more specific with which tubulin isoform is used as a male marker and state why this marker was used in supplemental Fig S6.

Line 196 and Fig 3C: the word 'intensities' in this context is very ambiguous. Please choose a different term (puncta, elements, parts?). This is related to major point 2i above.

Line 222: Report male/female crista measurements

Fig. 4B-E: depict data as violin plots or scatter plots like Fig. 2C to get a better grasp of how the crista coverage is distributed. It seems like the data spread is wider in the double KO. This would also solve the problem with the standard deviation extending beyond 0%.

Lines 331-333: Please clarify that this applies for some, but not all MICOS subunits. Please also see major point 1 above. Also, the authors should point out that despite their structural divergence, trypanosomal cryptic mitofilins Mic34 and Mic40 are essential for parasite growth, in contrast to their findings with PfMic60 (DOI: https://doi.org/10.1101/2025.01.31.635831).

Line 320: incorrect citation. Related to point 1above.

Lines 333-335. This is related to the above. Again, some subunits appear to affect cell growth under lab conditions, and some do not. This and the previous sentence should be rewritten to reflect this.

Line 343-345: The sentence and citation 45 are strange. Regarding the former, it is about CHCHD10, whose status as a bona fide MICOS subunit is very tenuous, so I would omit this. About the phenomenon observed, I think it makes more sense to write that Mic60 ablation results in partially fragmented mitochondria in yeast (Rabl et al., 2009 J Cell Biol. 185: 1047-63). A fragmented mitochondria is often a physiological response to stress. I would just rewrite as not to imply that mitochondrial fission (or fusion) is impaired in these KOs, or at least this could be one of several possibilities.

Line 373: 'This indicates' is too strong. I would say 'may suggest' as you have no proof that any of the KOs disrupts MICOS. This hypothesis can be tested by other means, but not by penetrance of a phenotype.

Line 376-377; 'deplete functionality' does not make sense, especially in the context of talking about MICOS subunit stability. In my opinion, this paragraph overinterprets the KO effects on MICOS stability. None of the experiments address this phenomenon, and thus the authors should not try to interpret their results in this context. See major point 1.

Other suggestions for added value

1) Does Plasmodium Sam50 co-fractionate with Mic60 and Mic19 in BN PAGE (Fig. 1E)

2) Can Alphafold3 predict a heterotetramer of PfMic60? What about the four Mic19 and Mic60 subunits together. Is this tetramer consistent with the Bock-Bierbaum model. Is this model consistent with the CJ diameter measured in plasmodium, which is perhaps better evidence than that in lines 419-422.

Significance

The manuscript by Tassan-Lugrezin is predicated on the idea that Plasmodium represents the only system in which de novo crista formation can be studied. They leverage this system to ask the question whether MICOS is essential for this process. They conclude based on their data that the answer is no, which the authors consider unprecedented. But even if their claim is true that ABS is acristate, this supposed advantage does not really bring any meaningful insight into how MICOS works in Plasmodium.

First the positives of this manuscript. As has been the case with this research team, the manuscript is very sophisticated in the experimental approaches that are made. The highlights are the beautiful and often conclusive microscopy performed by the authors. Only the localization of Mic60 and Mic19 was inconclusive due to their very low expression unfortunately.

The examination of the MICOS mutants during in vitro life cycle of Plasmodium falciparum is extremely impressive and yields convincing results. Mitochondrial deformation is tolerated by life cycle stage differentiation, with a modest but significant reduction of oocyte production, being observed.

The manuscript by Tassan-Lugrezin is predicated on the idea that Plasmodium represents the only system in which de novo crista formation can be studied. They leverage this system to ask the question whether MICOS is essential for this process. They conclude based on their data that the answer is no, which the authors consider unprecedented. But even if their claim is true that ABS is acristate, this supposed advantage does not really bring any meaningful insight into how MICOS works in Plasmodium.

First the positives of this manuscript. As has been the case with this research team, the manuscript is very sophisticated in the experimental approaches that are made. The highlights are the beautiful and often conclusive microscopy performed by the authors. Only the localization of Mic60 and Mic19 was inconclusive due to their very low expression unfortunately.

The examination of the MICOS mutants during in vitro life cycle of Plasmodium falciparum is extremely impressive and yields convincing results. Mitochondrial deformation is tolerated by life cycle stage differentiation, with a modest but significant reduction of oocyte production, being observed.

However, despite the herculean efforts of the authors, the manuscript as it currently stands represents only a minor advance in our understanding of the evolution of MICOS, which from the title and focus of the manuscript, is the main goal of the authors.

In its current form, the manuscript reports some potentially important findings:

1) Mic60 is verified to play a role in crista formation, as is predicted by its orthology to other characterized Mic60 orthologs.

2) The discovery of a novel Mic19 analog (since the authors maintain there is no significant sequence homology), which exhibits a similar (or the same?) complexome profile with Mic60. This protein was upregulated in gametocytes like Mic60 and phenocopies Mic60 KO.

3) Both of these MICOS subunits are essential (not dispensable) for proper crista formation

4) Surprisingly, neither MICOS subunit is essential for in vitro growth or differentiation from ABS to sexual stages, and from the latter to sporozoites. This says more about the biology of plasmodium itself than anything about the essentiality of Mic60, ie plasmodium life cycle progression tolerates defects to mitochondrial morphology. But yes, I agree with the authors that Mic60's apparent insignificance for cell growth in examined conditions does differ with its essentiality in other eukaryotes. But fitness costs were not assayed (eg by competition between mutants and WT in infection of mosquitoes)

5) Decreased fitness of the mutants is implied by a reduction of oocyte formation.

While interesting in their own way, collectively they do not represent a major advance in our understanding of MICOS evolution. Furthermore, the findings bifurcate into categories informing MICOS or Plasmodium biology. Both aspects are somewhat underdeveloped in their current form.

This is unfortunate because there seem to be many missed opportunities in the manuscript that could, with additional experiments, lead to a manuscript with much wider impact.

For me, what is remarkable about Plasmodium MICOS that sets it apart from other iterations is the apparent absence of the Mic10 subunit. Purification of plasmodium MICOS via the epitope tagged Mic60 and Mic19 could have verified that MICOS is assembled without this core subunit. Perhaps Mic60 and Mic19 are the vestiges of the complex, and thus operate alone in shaping cristae. Such a reduction may also suggest the declining importance of mitochondria in plasmodium.

Another missed opportunity was to assay the impact of MICOS-depletion of OXPHOS in plasmodium. This is a salient issue as maybe crista morphology is decoupled from OXPHOS capacity in Plasmodium, which links to the apparent tolerance of mitochondrial morphology in cell growth and differentiation. I suggested in section A experiments to address this deficit.

Finally, the authors could assay fitness costs of MICOS-ablation and associated phenotypes by assaying whether mosquito infectivity is reduced in the mutants when they are directly competing with WT plasmodium. Like the authors, I am also surprised that MICOS mutants can pass population bottlenecks represented by differentiation events. Perhaps the apparent robustness of differentiation may contribute plasmodium's remarkable ability to adapt.

I realize that the authors put a lot of efforts into their study and again, I am very impressed by the sophistication of the methods employed. Nevertheless, I think there is still better ways to increase the impact of the study aside from overinterpreting the conclusions from the data. But this would require more experiments along the lines I suggest in Section A and here.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This is a well-structured and interesting manuscript that investigates how herbivorous insects, specifically whiteflies and planthoppers, utilize salivary effectors to overcome plant immunity by targeting the RLP4 receptor.

Strengths:

The authors present a strong case for the independent evolution of these effectors and provide compelling evidence for their functional roles.

Weaknesses:

Western blot evidence for effector secretion is weak. The possibility of contamination from insect tissues during the sample preparation should be avoided.

Below are some specific comments and suggestions to strengthen the manuscript.

Thank you very much for your comments. We have carefully revised the MS following your valuable suggestions and comments.

(1) Western blot evidence for effector secretion:

The western blot evidence in Figure 1, which aims to show that the insect protein is secreted into plants, is not fully convincing. The band of the expected size (~30 kDa) in the infested tissues is very weak. Furthermore, the high and low molecular weight bands that appear in the infested tissues do not match the size of the protein in the insects themselves, and a high molecular weight band also appears in the uninfested control tissues. It is difficult to draw a definitive conclusion that this protein is secreted into the plants based on this evidence. The authors should also address the possibility of contamination from insect tissues during the sample preparation and explain how they have excluded this possibility.

Thank you for pointing out this. One or two bands between 25-35kDa were specifically identified in B. tabaci-infested plants, but not the non-infested plants, and the smaller high intensity band is the same size as that of BtRDP in salivary glands. This experiment has been repeated for six times. In the current version, we reperformed this experiment, and provided salivary gland sample as a positive control, which showed the same molecular weight with a specific band in infested sample. It is noteworthily that in the experiment of current version, only the smaller high intensity band appear, while the low intensity band did not appear. The detection of a protein within infested plant tissue is a key criterion for validating the secretion of salivary effectors, an approach supported by numerous studies in this field. Furthermore, our previous LC-MS/MS analysis of B. tabaci watery saliva identified six unique peptides matching BtRDP, providing independent evidence for its presence in saliva. Therefore, as we now state in the manuscript “the detection of BtRDP in infested plants (Fig. 1a) and in watery saliva (Fig. S1) collectively indicates that BtRDP is a salivary protein”.

Regarding the higher molecular weight band that present in both infested and non-infested samples, we agree that it most likely represents a non-specific band, which is a common occurrence in Western blot assays. Such bands are sometimes used to indicate comparable sample loading. To address the possibility of contamination by insect tissues, we wish to clarify that all insects and deposited eggs were carefully removed from the infested leaves prior to sample processing. Moreover, BtRDP is undetectable at the egg stage, and no BtRDP-associated band can be detected even in egg contamination. We have revised the Methods section to explicitly state this procedure:

“After feeding, the eggs deposited on the infested tobacco leaves were removed. The leaves showing no visible insect contamination were immediately frozen in liquid nitrogen and ground to a fine powder.”

(2) Inconsistent conclusion (Line 156 and Figure 3c):

The statement in line 156 is inconsistent with the data presented in Figure 3c. The figure clearly shows that the LRR domain of the protein is the one responsible for the interaction with BtRDP, not the region mentioned in the text. This is a critical misrepresentation of the experimental findings and must be corrected. The conclusion in the text should accurately reflect the data from the figure.

We apologize for any confusion caused by the original phrasing. In our previous manuscript, the description “NtRLP4 without signal peptides and transmembrane domains” referred specifically to the truncated construct NtRLP4_(23-541) used in the experiment. To prevent any misunderstanding, we have revised the sentence in the updated version to state explicitly: “Point-to-point Y2H assays reveal that NtRLP4_(23-541) (a truncated version lacking the signal peptide and transmembrane domains) interacts with BtRDP^-sp”.

(3) Role of SOBIR1 in the RLP4/SOBIR1 Complex:

The authors demonstrate that the salivary effectors destabilize the RLP4 receptor, leading to a decrease in its protein levels and a reduction in the RLP4/SOBIR1 complex. A key question remains regarding the fate of SOBIR1 within this complex. The authors should clarify what happens to the SOBIR1 protein after the destabilization of RLP4. Does SOBIR1 become unbound, targeted for degradation itself, or does it simply lose its function without RLP4? This would provide further insight into the mechanism of action of the effectors.

Thank you for suggestion. In the current version, we assessed the impact of BtRDP on NtSOBIR1 following NtRLP4 destabilization. The results showed that while the NtRLP4-myc accumulation was markedly reduced, NtSOBIR1-flag levels remained unchanged, suggesting that destabilization of NtRLP4 did not affect NtSOBIR1 accumulation.

(4) Clarification on specificity and evolutionary claims:

The paper's most significant claim is that the effectors from both whiteflies and planthoppers "independently evolved" to target RLP4. While the functional data is compelling, this evolutionary claim would be more convincing with stronger evidence. Showing that two different effector proteins target the same host protein is a fascinating finding but without a robust phylogenetic analysis, the claim of independent evolution is not fully supported. It would be valuable to provide a more detailed evolutionary analysis, such as a phylogenetic tree of the effector proteins, showing their relationship to other known insect proteins, to definitively rule out a shared, but highly divergent, common ancestor.

We appreciate the reviewer’s valuable suggestion to investigate a potential evolutionary link between BtRDP and NlSP104. Our initial analysis already indicated no detectable sequence similarity. To address this point more thoroughly, we attempted a phylogenetic analysis. However, we were unable to generate a meaningful alignment due to a complete lack of conserved amino acid sequences. Therefore, we conducted a comparative genomics analysis by blasting both proteins against the genomic or transcriptomic data of 30 diverse insect species. This analysis revealed that RDP is exclusively present in Aleyrodidae species, and SP104 is exclusively present in Delphacidae species (Table S1). Taken together, the absence of sequence similarity, their distinct protein structure, and their lineage-specific distributions, we conclude that BtRDP and NlSP104 are highly unlikely to be homologous and thus did not originate from a common ancestor.

(5) Role of SOBIR1 in the interaction:

The results suggest that the effectors disrupt the RLP4/SOBIR1 complex. It is not entirely clear if the effectors are specifically targeting RLP4, SOBIR1, or both. Further experiments, such as a co-immunoprecipitation assay with just RLP4 and the effector, could clarify if the effector can bind to RLP4 in the absence of SOBIR1. This would help to definitively place RLP4 as the primary target.

We appreciate the reviewer’s insightful comments regarding whether the effector preferentially targets RLP4, SOBIR1, or both. In our study, we conducted reciprocal co-immunoprecipitation assays using RLP4 and BtRDP as controls. These assays showed that BtRDP interacts with RLP4 but does not interact with SOBIR1, supporting the conclusion that SOBIR1 is unlikely to be a direct target of BtRDP. We fully agree that testing the interaction between RLP4 and BtRDP in the absence of SOBIR1 would further strengthen the conclusion. However, we were unable to obtain N. tabacum SOBIR1 knockout mutants, and therefore could not experimentally assess whether the RLP4–BtRDP interaction persists in planta without SOBIR1. Nevertheless, our yeast two-hybrid assays demonstrate that RLP4 and BtRDP can directly interact, indicating that their association does not strictly depend on SOBIR1. Together, these results support the interpretation that RLP4 is the primary target of BtRDP, while SOBIR1 is not directly engaged by the effector.

(6) Transcriptome analysis (Lines 130-143):

The transcriptome analysis section feels disconnected from the rest of the manuscript. The findings, or lack thereof, from this analysis do not seem to be directly linked to the other major conclusions of the paper. This section could be removed to improve the manuscript's overall focus and flow. If the authors believe this data is critical, they should more clearly and explicitly connect the conclusions of the transcriptome analysis to the core findings about the effector-RLP4 interaction.

Thank you for suggestion. As you and Reviewer #2 pointed, the transcriptomic analysis did not closely link to the major conclusions of the paper, and we got little information from the transcriptomic analysis. Therefore, we remove these analyses to improve the manuscript’s overall focus and flow.

(7) Signal peptide experiments (Lines 145 and beyond):

The experiments conducted with the signal peptide (SP) are questionable. The SP is typically cleaved before the protein reaches its final destination. As such, conducting experiments with the SP attached to the protein may have produced biased observations and could lead to unjustified conclusions about the protein's function within the plant cell. We suggest the authors remove the experiments that include the signal peptide.

Thank you for pointing out this. The SP was retained to direct the target proteins to the extracellular space of plant cells. Theoretically, the SP is cleaved in the mature protein. This methodology is widely used in effector biology. For example, the SP directs Meloidogyne graminicola Mg01965 to the apoplast, where it functions in immune suppression, whereas Mg01965 without the SP fails to exert this function (10.1111/mpp.12759). In our study, the SP of BtRDP was expected to guide the target protein to the extracellular space, facilitating its interaction with RLP4. Moreover, the observed protein sizes of BtRDP with and without the SP in transgenic plants were identical, suggesting successful SP cleavage. Therefore, we have retained the experiments involving the SP in the current version.

(8) Overly strong conclusion and unclear evidence (Line 176):

The use of the word "must" on line 176 is very strong and presents a definitive conclusion without sufficient evidence. The authors state that the proteins must interact with SOBIR1, but they do not provide a clear justification for this claim. Is SOBIR1 the only interaction partner for NtRLP4? The authors should provide a specific reason for focusing on SOBIR1 instead of demonstrating an interaction with NtRLP4 first. Additionally, do BtRDP or NlSP694 also interact with SOBIR1 directly? The authors should either tone down their language to reflect the evidence or provide a clearer justification for this strong claim.

Thank you for pointing this out. In the current version, the word “must” has been toned down to “may” due to insufficient supporting evidence. In this study, SOBIR1 was chosen because it has been widely reported to be required for the function of several RLPs involved in innate immunity. However, it remains unclear whether SOBIR1 is the only interaction partner of NtRLP4. In the current version, we have clarified the rationale for focusing on SOBIR1 prior to the experiments “The receptor-like kinase SOBIR1, which contains a kinase domain, has been widely reported to be required for the function of RLPs involved in innate immunity (Gust & Felix, 2014)” and discussed that “Although NtRLP4 interacts with SOBIR1, this alone does not confirm that it operates strictly through this canonical module. Evidence from other RLPs shows that co-receptor usage can be flexible, and some RLPs function partly or conditionally independent of SOBIR1. Therefore, a more definitive assessment of NtRLP4 signaling will therefore require genetic dissection of its co-receptor dependencies, including but not limited to SOBIR1.”. In addition, the direct interaction between BtRDP and SOBIR1 was experimentally tested, and the results showed that BtRDP failed to interact with SOBIR1.

Minor Comments

(9) The statement in the abstract, "However, it remains unclear how these invaders are able to overcome receptor perception and disable the plant signaling pathways," is not entirely accurate. The fields of effector biology and host-pathogen interactions have provided significant insight into how pathogens and pests manipulate both Pattern-Triggered Immunity (PTI) and Effector-Triggered Immunity (ETI). While the specific mechanism described in this paper is novel, the broader claim that the field is unclear on these processes weakens the initial hook of the paper. A more precise framing of the problem would be beneficial, perhaps by stating that the specific mechanisms used by these particular herbivores to target RLP4 were previously unknown.

Thank you for this insightful comment. We agree that the original statement in the abstract overstated the lack of understanding in the field. In the current version, we have refined the sentence to more accurately reflect the current state of knowledge, emphasizing that while microbial suppression of plant immunity has been extensively studied, the strategies used by herbivorous insects to overcome receptor-mediated defenses remain less understood. The revised sentence now reads as follows: “Although the mechanisms used by microbial pathogens to suppress plant immunity are well studied, how herbivorous insects overcome receptor-mediated defenses remains unclear”.

(10) The introduction is heavily focused on Pattern Recognition Receptors (PRRs), which, while central to the paper's findings, gives a somewhat narrow view of the plant's defense against herbivores. It would be beneficial to briefly acknowledge the broader context of plant defenses, such as physical barriers, direct chemical toxicity, and indirect defenses, before narrowing the focus to the specific molecular interactions of PRRs that are the core of this study. This would provide a more complete picture of the "arms race" between plants and herbivores.

Thank you for this valuable suggestion. We agree that the original introduction focused too narrowly on pattern-recognition receptors (PRRs). In the current version, we have expanded the introductory section to provide a broader overview of plant defense mechanisms. Specifically, we now acknowledge the multiple layers of plant defenses, including physical barriers (e.g., cuticle and cell wall), chemical defenses (e.g., toxic secondary metabolites and anti-nutritive compounds), and indirect defenses mediated by herbivore-induced volatiles. This addition provides a more complete context for understanding the molecular interactions discussed in this study. The revised paragraph now reads as follows: “Plants have evolved sophisticated defense systems to survive constant attacks from pathogens and herbivorous insects. These defenses operate at multiple levels, including physical barriers such as the cuticle and cell wall, chemical defenses involving toxic secondary metabolites and anti-nutritive compounds, and indirect defenses that attract natural enemies of herbivores through the emission of herbivore-induced volatiles. Beyond these general strategies, plants also rely on highly specialized molecular immune responses that allow them to detect and respond rapidly to invaders.”

(11) The figure legends are generally clear, but some could be more detailed. For instance, in Figure 2, it would be helpful to explicitly state what each bar represents in the graph and to include the statistical test used. Please ensure all panels in all figures have clear labels.

Thank you for this helpful suggestion. We have revised the legend of Fig. 2 and other figures to provide more detailed information for each panel. Specifically, we now explicitly describe what each bar represents in the graphs and specify the statistical test used. In addition, we ensured that all panels are clearly labeled. These changes improve clarity and allow readers to better interpret the data.

(12) The methods section is comprehensive, but it would be helpful to include more specifics on the statistical analyses used. For example, the type of statistical test (e.g., t-test, ANOVA) and the software used should be mentioned for each experiment.

Thank you for your suggestion. We have revised the Methods section (Statistical analysis) to provide more detailed information on the statistical analysis used for each experiment.

(13) The manuscript's overall impact is weakened by the inclusion of unnecessary words and a few grammatical issues. A focused revision to tighten the language would make the major findings stand out more clearly. For example, on page 2, line 18, "in whitefly Bemisia tabaci, BtRDP is an Aleyrod..." seems to have an incomplete sentence. A thorough proofreading for typos and grammatical errors is highly recommended to improve the overall readability.

Thank you for your suggestion. We have carefully revised the abstract and the manuscript to improve clarity, readability, and grammatical correctness. In addition, we sought the assistance of a professional English editor to thoroughly proofread and polish the manuscript, ensuring that the language meets high academic standards.

(14) The discussion section is strong, but it could benefit from a more explicit connection between the findings and the broader ecological implications. For instance, how might the independent evolution of these effectors in different insect species impact plant-insect co-evolutionary dynamics?

We thank the reviewer for the valuable suggestion. In the current version, we have added a paragraph in the Discussion section highlighting the broader ecological and evolutionary implications of our findings. Specifically, we discuss how the independent evolution of RLP4-targeting effectors in different insect lineages may drive plant-insect co-evolution, influence selection pressures on both plants and herbivores, and potentially shape defense diversification across plant communities. This addition helps to link our molecular findings to ecological outcomes and co-evolutionary dynamics.

(15) The sentence on line 98, which reads " A few salivary proteins have been reported to attach to salivary sheath after secretion" seems to serve an unclear purpose in the introduction. It would be helpful for the authors to clarify its relevance to the surrounding context or to the paper's overall argument. Its inclusion currently disrupts the flow of the introduction and makes it difficult for the reader to understand its intended purpose.

We thank the reviewer for the comment. We have revised the paragraph to clarify the relevance of salivary sheath localization to the study. Specifically, we now introduce the role of the salivary sheath as a potential scaffold for effector delivery and explicitly link previous reports of sheath-associated salivary proteins to our observation that BtRDP localizes to the salivary sheath after secretion.

(16) The writing in lines 104-106 is both grammatically inconsistent and overly wordy. The authors switch between present and past tense ("is" and "was"), and the sentences could be made more concise to improve the clarity and flow of the text. Also check entire paper.

We thank the reviewer for pointing this out. We have revised the sentence to improve grammatical consistency and clarity, and also checked the manuscript for similar issues. The sentence is now split into two concise statements. In addition, we have thoroughly checked the entire manuscript for similar tense inconsistencies and overly wordy sentences, and have made revisions throughout to ensure consistent past tense usage and improved readability.

(16) The sentences on lines 111-113 are quite wordy. The core conclusion, which is that the protein affects the insect's feeding probe, could be expressed more simply and directly to improve clarity and flow. I suggest rephrasing this section to be more concise and to highlight the primary finding without the added language.

We thank the reviewer for the helpful suggestion. We have revised the sentences to make them more concise and to emphasize the main finding that BtRDP influences the whitefly’s feeding behavior as follow: “Compared with the dsGFP control, dsBtRDP-treated B. tabaci showed a marked reduction in phloem ingestion and a longer pathway duration, indicating that BtRDP is required for efficient feeding (Fig. 2c).”

(17) On line 118, the authors mention "subcellular location." It is not clear where the protein is localized. The authors should explicitly state the specific subcellular compartment of the protein, as this is crucial for understanding its function and interaction with other proteins.

We thank the reviewer for this valuable comment. To clarify the subcellular localization of BtRDP, we have revised the manuscript accordingly. The transgenic line overexpressing the full-length BtRDP including the signal peptide (oeBtRDP) is expected to localize in the apoplast (extracellular space), whereas the line expressing BtRDP without the signal peptide (oeBtRDP^-sp) is likely retained in the cytoplasm.

(18) Lines 121-128, the description of the fecundity and choice assays in this section is overly wordy. The authors should present the main conclusion of these experiments more directly and concisely. The key finding is that the protein affects feeding behavior; this central point is somewhat lost in the detailed, and sometimes repetitive, phrasing.

We thank the reviewer for this suggestion. In the revised manuscript, we have simplified the description of the fecundity and two-choice assays to highlight the main conclusion as follow: “Fecundity and two-choice assays showed that BtRDP, whether localized in the apoplast (oeBtRDP) or cytoplasm (oeBtRDP^-sp), enhanced whitefly settling and oviposition compared with EV controls (Fig. 2d-i; Fig. S10), indicating that BtRDP promotes whitefly feeding behavior regardless of its subcellular location.”

(19) Line 148, the manuscript mentions experiments involving transformation, but the transformation efficiency is not provided. Please include the transformation efficiency for all transformation experiments, as this is crucial for the reproducibility of the results.

We thank the reviewer for raising this point. We would like to clarify that no transformation experiments were performed in this section. The experiments described involved Y2H screening using BtRDP^-sp as a bait to identify interacting proteins from a N. benthamiana cDNA library. Therefore, there is no transformation efficiency to report.

(20) Line 159, the manuscript refers to a sequence similarity around line 159 but does not provide the specific data. It is important to show the actual sequence similarity, perhaps in a supplementary figure or table, to support the claims being made.

We thank the reviewer for this suggestion. To support our statement regarding sequence similarity, we have added the corresponding alignment figure in the Fig. S11.

(21) Line 159, the manuscript refers to "three randomly selected salivary proteins." It is unclear from where these proteins were selected. The authors should clarify the source of this selection (e.g., a specific database or a previous study) to ensure the methodology is transparent and the results are reproducible.

We thank the reviewer for raising this point. These proteins were selected based on previously reports (10.1093/molbev/msad221; 10.1111/1744-7917.12856). In the current version, we provide the accession of these proteins in the MS.

(22) Line 160, the description "NtcCf9 without signal peptide and transmembrane domains" is difficult to understand. It would be clearer and more consistent to use a term like "truncated NtcCf9" and then specify which domains were removed, as this is a standard practice in molecular biology for describing protein constructs.

We thank the reviewer for this suggestion. We have revised the manuscript to describe the construct as “truncated NtCf9” and specified that the signal peptide and transmembrane domains were removed

(23) The phrase "incubated with anti-flag beads" on line 172 is a detail of a routine method. Such details are more appropriate for the Methods section rather than the main text, which should focus on the results and their implications. Please remove such descriptions from the main text to improve readability and flow.

We thank the reviewer for this suggestion. We have removed the methodological detail from the main text to improve readability. We also check this throughout the MS.

I am excited about the potential of this work and look forward to seeing the current version.

We sincerely thank the reviewer for the positive feedback and encouragement. We appreciate your time and thoughtful comments.

Reviewer #2 (Public review):

Summary:

The authors tested an interesting hypothesis that white flies and planthoppers independently evolved salivary proteins to dampen plant immunity by targeting a receptor-like protein.

Strengths:

The authors used a wide range of methods to dissect the function of the white fly protein BtRDP and identify its host target NtRLP4.

Thank you very much for your comments. We have carefully revised the MS following your valuable suggestions and comments.

Weaknesses:

(1) Serious concerns about protein work.

I did not find the indicated protein bands for anti-BtRDP in Figures 1a and 1b in the original blot pictures shown in Figure S30. In Figure 1a, I can't get the point of showing an unspecific protein band with a size of ~190 kD as a loading control for a protein of ~ 30 kD.

The data discrepancy led me to check other Western blot pictures. Similarly, Figures 2d, 3b, 3d, and S15b (anti-Myc) do not correspond to the original blots shown. In addition, the anti-Myc blot in Figure 4i, all blot pictures in Figures 5b, 5h, and S19a appeared to be compressed vertically. These data raised concerns about the quality of the manuscript.

Blots shown in Figure 3d, 4f, 4g, and 4h appeared to be done at a different exposure rate compared to the complete blot shown in Figure S30. The undesirable connection between Western blot pictures shown in the figures and the original data might be due to the reduced quality of compressed figures during submission. Nevertheless, clarification will be necessary to support the strength of the data provided.

We sincerely thank the reviewer for carefully examining our Western blot data and for pointing out these inconsistencies. The discrepancy between the figures in the main text and the original blots (Figure S30) resulted from an oversight during manuscript revision. This manuscript had undergone multiple rounds of revision after submission to another journal. During this process, the main figures and supplementary figures were updated separately, and we mistakenly failed to replace the original blot files with the corresponding current versions.

For the different exposure rate, the blots shown in the main text were adjusted for overall contrast and brightness to enhance band visibility and presentation clarity, whereas the original images in Figure S30 were raw, unprocessed scans directly from the imaging system. For example, in the Author response image 1 below, to visualize the loading of the input sample, the output figure was adjusted for overall contrast and brightness. This was acceptable for image processing (https://www.nature.com/nature-portfolio/editorial-policies/image-integrity)

Author response image 1.

The same figure with brightness and contrast changes across the entire image.

For the vertical compression, in the previous version, some images were vertically compressed for layout purposes to make the composite figures appear more visually balanced. However, after consulting relevant publication guidelines, we realized that such one-dimensional compression is not encouraged by certain journals as it may alter the original aspect ratio of the image. Therefore, in the manuscript, we have avoided any non-proportional scaling and retained the original aspect ratio of all images.

We have now carefully rechecked all Western blot data, replaced the outdated raw blot images with the correct corresponding ones, avoid vertical compression, and ensured that the processed figures in the main text match their original data. The revised supplementary figures now accurately reflect the raw experimental results.

(2) Misinterpretation of data.

I am afraid the authors misunderstood pattern-triggered immunity through receptor-like proteins. It is true that several LRR-type RLPs constitutively associate with SOBIR1, and further recruit BAK1 or other SERKs upon ligand binding. One should not take it for granted that every RLP works this way. To test the hypothesis that NtRLP4 confers resistance to B.tabaci infestation, the author compared transcriptional profiles between an EV plant line and an RLP4 overexpression line. If I understood the methods and figure legends correctly, this was done without B. tabaci treatment. This experimental design is seriously flawed. To provide convincing genetic evidence, independent mutant lines (optionally independent overexpression lines) in combination with different treatments will be necessary. Otherwise, one can only conclude that overexpressing the RLP4 protein generated a nervous plant. In addition, ROS burst, but not H2O2 accumulation, is a common immune response in pattern-triggered immunity.

We agree with the reviewer that not every RLP functions through the same mechanism as the canonical SOBIR1–BAK1 pathway. In the current version, we further examined the interaction between the whitefly salivary protein and SOBIR1, and found that they do not interact. However, our interaction assays clearly demonstrated that NtRLP4 does interact with SOBIR1. Whether NtRLP4 functions through, or exclusively through, SOBIR1 remains uncertain, and we have emphasized this limitation in the Discussion section as follow: “Although NtRLP4 interacts with SOBIR1, this alone does not confirm that it operates strictly through this canonical module. Evidence from other RLPs shows that co-receptor usage can be flexible, and some RLPs function partly or conditionally independent of SOBIR1 [39]. Therefore, a more definitive assessment of NtRLP4 signaling will therefore require genetic dissection of its co-receptor dependencies, including but not limited to SOBIR1.”

Regarding the transcriptome analysis, our original aim was to explore why B. tabacishowed such a pronounced preference among tobacco plants. As this preference was assessed using uninfested plants, we also performed transcriptome sequencing using plants without B. tabaci treatment. The enrichment analysis demonstrated that the majority of up-regulated DEGs were associated with plant–pathogen interaction, environmental adaptation, MAPK signaling, and signal transduction pathways, while down-regulated DEGs were enriched in glutathione, carbohydrate, and amino acid metabolism. Notably, many DEGs were annotated as RLK/RLPs or WRKY transcription factors, most of which were upregulated, suggesting an enhanced defense state in the NtRLP4-overexpressing plants. The altered expression of JA- and SA-related genes (e.g., upregulation of FAD7 and downregulation of PAL and NPR1) further supported this enhanced defense and hormonal crosstalk. We agree that combining overexpression or knockout lines with insect infestation treatments would provide more direct genetic evidence for NtRLP4-mediated resistance, and we have acknowledged this as an important future direction. Nevertheless, our current data are consistent with the conclusion that NtRLP4 overexpression confers increased resistance to B. tabaci infestation.

Finally, DAB staining for H₂O₂ accumulation is also a well-established indicator of PTI responses, and many studies have shown that overexpression of salivary elicitors can trigger such accumulation.

(3) Lack of logic coherence.

The written language needs substantial improvement. This impeded the readability of the work. More importantly, the logic throughout the manuscript appeared scattered. The choice of testing protein domains for protein-protein interactions, using plants overexpressing an insect protein to study its subcellular localization, switching back and forth between using proteins with signal peptides and without signal peptides, among others, lacks a clear explanation.

We appreciate the reviewer’s careful reading and valuable comments regarding the logical coherence of our manuscript.

(1) To improve the English quality, the entire manuscript has been professionally edited by a certified language-editing service.

(2) Regarding the rationale for testing protein domains in the protein–protein interaction assays: NtRLP4 is a membrane-anchored receptor-like protein composed of extracellular, transmembrane, and short intracellular domains. We aimed to determine which region of NtRLP4 is responsible for interacting with the salivary protein, as this would help infer the likely site of interaction in planta. In addition, not all RLPs contain a malectin-like domain, and we sought to verify whether the BtRDP–NtRLP4 interaction depends on this domain. To enhance the logical flow, we introduced a brief statement explaining the experimental purpose before presenting the interaction assays in the current version as follow: “These findings raised the question of which domain of NtRLP4 is responsible for binding BtRDP, as identifying the interacting domain could help infer where the salivary protein contacts the receptor in planta. We therefore dissected the NtRLP4 domains accordingly.”

(3) With respect to using plants overexpressing an insect protein to examine subcellular localization: since both the brown planthopper and the whitefly are non-model species for which stable genetic transformation is technically unfeasible, many previous studies have used Agrobacterium-mediated transient expression or transgenic plant systems to investigate the subcellular localization of insect salivary proteins within host cells. Following these precedents, our study also employed plant systems to determine the localization of the insect protein and to assess how different localizations affect plant defense responses.

(4) As for switching between constructs with or without signal peptides: the subcellular localization of effectors can influence their biological activity and interactions. Previous studies have used the presence or absence of signal peptides, or replacement with a PR1 signal peptide, to direct protein targeting (for example, Frontiers in Plant Science, 2022, 13:813181). Because salivary sheaths are generally considered to localize in the apoplastic space, we generated two transgenic N. tabacum lines overexpressing BtRDP: one carrying the full-length coding sequence including the signal peptide (oeBtRDP), expected to be secreted into the apoplast, and another lacking the signal peptide (oeBtRDP-sp), likely retained in the cytoplasm. In the current version, we clarified this rationale and added references to similar studies to improve the manuscript’s logic and readability. Details are as follow: “To investigate the role of BtRDP in different subcellular location of host plants, we constructed two transgenic N. tabacum lines overexpressing BtRDP: one carrying the full-length coding sequence including the signal peptide (oeBtRDP), which is expected to be secreted into the apoplast (extracellular space), and the other lacking the signal peptide (oeBtRDP^-sp), which is likely retained in the cytoplasm.”

Reviewer #3 (Public review):

Summary:

In this study, Wang et al. investigate how herbivorous insects overcome plant receptor-mediated immunity by targeting plant receptor-like proteins. The authors identify two independently evolved salivary effectors, BtRDP in whiteflies and NlSP694 in brown planthoppers, that promote the degradation of plant RLP4 through the ubiquitin-dependent proteasome pathway. NtRLP4 from tobacco and OsRLP4 from rice are shown to confer resistance against herbivores by activating defense signaling, while BtRDP and NlSP694 suppress these defenses by destabilizing RLP4 proteins.

Strengths:

This work highlights a convergent evolutionary strategy in distinct insect lineages and advances our understanding of insect-plant coevolution at the molecular level.

Thank you very much for your comments. We have carefully revised the MS following your valuable suggestions and comments.

Weaknesses:

(1) I found the naming of BtRDP and NlSP694 somewhat confusing. The authors defined BtRDP as "B. tabaci RLP-degrading protein," whereas NlSP694 appears to have been named after the last three digits of its GenBank accession number (MF278694, presumably). Is there a standard convention for naming newly identified proteins, for example, based on functional motifs or sequence characteristics? As it stands, the inconsistency makes it difficult for readers to clearly distinguish these proteins from those reported in other studies.

Thank you for your comment. These are species-specific salivary proteins that have not been reported or annotated in previous studies. Because no homologous genes could be identified in other species, there are no existing names or annotations for these proteins. For such lineage-specific salivary proteins, it is common in recent studies to name them according to their experimentally identified functions. For example, a recently reported salivary protein was named SR45-interacting salivary protein (SISP) based on its function (10.1111/nph.70668). Following this convention, we adopted a similar functional naming strategy in this study. We acknowledge that there may not yet be a standardized rule for naming such proteins, and we would be glad to follow a more authoritative naming guideline if possible.

(2) Figure 2 and other figures. Transgenic experiments require at least two independent lines, because results from a single line may be confounded by position effects or unintended genomic alterations, and multiple lines provide stronger evidence for reproducibility and reliability.

We appreciate the reviewer’s suggestion. In our study, two independent transgenic lines were used to ensure the reproducibility and reliability of the results. One representative line was presented in the main figures, while data from the second independent line were included in the supplementary figures. To make this clearer, we have emphasized in the manuscript that bioassays were conducted using two independent transgenic lines.

(3) Figure 3e. Quantitative analysis of NtRLP4 was required. Additionally, since only one band was observed in oeRLP, were any tags included in the construct?

Thank you for your comment. In the current version, quantitative analysis of NtRLP4 expression has been performed and is now presented in Figure 3. For the oeRLP plants, no tag was fused to NtRLP4; thus, anti-RLP serum was used to detect the target bands. In contrast, oeBtRDP and oeBtRDP-sp were fused with C-terminal FLAG tags, and their detection was carried out using anti-FLAG serum. This information has been clarified in the revised Methods section as follows: “The oeBtRDP and oeBtRDP^-sp were fused with C-terminal FLAG tags, while no tag was fused to oeNtRLP4.”

(4) Figure 4a. The RNAi effect appears to be well rescued in Line 1 but poorly in Line 2. Could the authors clarify the reason for this difference?

Thank you for pointing this out. We also noticed that the RNAi effect appeared to be better rescued in Line 2 than in Line 1. Based on our measurements, the silencing efficiency of NtRLP4 in RNAi-RLP4 Line 1 was markedly weaker than in Line 2, which likely explains the difference in rescue efficiency. In the current version, we have clarified this point as follows: “Both RNAi-RLP lines showed reduced NtRLP4 levels compared with EV plants, with RNAi-RLP#2 exhibiting a stronger silencing effect (Fig. S19a).” “The differential rescue effect between the two RNAi lines likely resulted from their different NtRLP4 silencing efficiencies, with the lower NtRLP4 level in RNAi-RLP#2 leading to a more complete rescue phenotype.”

(5) ROS accumulation is shown for only a single leaf. A quantitative analysis of ROS accumulation across multiple samples would be necessary to support the conclusion. The same applies to Figure 16f.

Thank you for pointing this out. The H₂O₂ accumulation experiments have been repeated for 5 times in Figure 4 and Figure S16f. In the current version, we addressed that “the experiment is repeated five times with similar results” in the figure legends.

(6) Figure 4f: NtRLP4 abundance was significantly reduced in oeBtRDP plants but not in oeBtRDP-SP. Although coexpression analysis suggests that BtRDP promotes NtRLP4 degradation in an ubiquitin-dependent manner, the reduced NtRLP4 levels may not result from a direct interaction between BtRDP and NtRLP4. It is possible that BtRDP influences other factors that indirectly affect NtRLP4 abundance. The authors should discuss this possibility.

Thank you for your valuable suggestion. We agree that the reduced NtRLP4 abundance may not necessarily result from a direct interaction between BtRDP and NtRLP4. In the manuscript, we have further discussed this possibility as follows: “Notably, BtRDP and NlSP104 shared no sequence or structural similarity and lack resemblance to known eukaryotic ubiquitin-ligase domains. Their interaction with RLP4s occurs in the extracellular space (Fig. 3d; Fig. 5c), whereas the ubiquitin-proteasome system primarily functions in the cytosol and nucleus [46]. Furthermore, NtRLP4 reduction is observed only in oeBtRDP transgenic plants, not in oeBtRDP-sp plants (Fig. 4f), suggesting that BtRDP exerts its influence on NtRLP4 in the extracellular space. These observations collectively argue against the possibility that BtRDP or NlSP694 possesses intrinsic E3 ligase activity capable of directly ubiquitinating RLP4s within plant cells. Importantly, the reduced NtRLP4 levels may not result from a direct physical interaction between BtRDP and NtRLP4. Instead, BtRDP may indirectly affect RLP4 post-translational modification, thereby accelerating its degradation, which warrants further investigation”

(7) The statement in lines 335-336 that 'Overexpression of NtRLP4 or NtSOBIR1 enhances insect feeding, while silencing of either gene exerts the opposite effect' is not supported by the results shown in Figures S16-S19. The authors should revise this description to accurately reflect the data.

Thank you for pointing this out. We agree that our original statement was not precise, as we measured the insect settling preference and oviposition on transgenic plants, but did not directly assess the feeding behavior of B. tabaci. Therefore, we have revised the description in the manuscript to more accurately reflect our data as follows: “Overexpression of NtRLP4 or NtSOBIR1 in N. tabacum is attractive to B. tabaci and promotes insect reproduction, whereas silencing of either gene exerts the opposite effect.”

(8) BtRDP is reported to attach to the salivary sheath. Does the planthopper NlSP694 exhibit a similar secretion localization (e.g., attachment to the salivary sheath)? The authors should supplement this information or discuss the potential implications of any differences in secretion localization between BtRDP and NlSP694 for their respective modes of action.

Thank you for your insightful suggestion. We agree that determining the secretion localization of NlSP694 would provide valuable information for understanding its potential mode of action. Immunohistochemical (IHC) staining is indeed a critical approach for such analysis. However, in this study, we were unable to express NlSP694 in Escherichia coli, and the antibody generated using a synthesized peptide did not show sufficient specificity or sensitivity for IHC detection. Consequently, we were unable to determine whether NlSP694 is attached to the salivary sheath. Therefore, whether BtRDP and NlSP694 acted in different mode require further investigation.

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

(1) Figure 1e. The BtRDP-labeled fluorescent signal is difficult to discern. An enlarged view of the target region would be helpful for clarity.

Thank you for your suggestion. In the current version, an enlarged view of the target region was provided below the figure.

(2) The finding that BtRDP accumulates in the salivary sheath secreted by Bemisia tabaci is important for understanding the subcellular localization of this protein during actual insect feeding. I suggest moving Figure S5 to the main text.

Thank you for your suggestion. Figure S5 has been moved to Fig. 1f in the current version.

(3) Please carefully cross-check the figure numbering to ensure that all in-text citations correspond to the correct figures and panels. i.e., lines 136,188,192, and 194.

Thank you for pointing this out. We corrected them in the current version.

Reviewer #1 (Public review):

The current manuscript investigates a regulatory axis containing Prmt1, which methylates RNA binding proteins and alters intron splicing outcomes and expression of matrix genes. Authors test the effects of deficient Prmt1, Sfpq, and various other factors, using a combination of bioinformatic analyses and wet-lab validation approaches. Authors show that intron retention often triggers NMD, contributing to aberrant gene expression regulation and craniofacial development. The revised manuscript introduces several complementary experiments that help to strengthen conclusions. For example, authors directly investigate NMD-mediated transcript turnover to better understand how retention contributes to expression changes in genes of interest, and they assess several additional factors downstream of Prmt1 to justify a centralized interested in the PRMT1/SFPQ axis.

Weaknesses:

However, some points remain unaddressed or unexplored, which could bolster conclusions. For example, the transcriptome data from knockdown experiments indicate robust exon skipping, suggesting that analysis of these patterns in parallel with intron retention could provide additional insights into the responsive gene programs. Given that SFPQ is known to have multiple regulatory roles, a more thorough investigation of its possible mechanisms of action during craniofacial development would allow for definitive conclusions about the isolated impact of SFPQ-dependent splicing. Although authors employ CUT&Tag analysis of Pol II binding at the promoters and across the gene body, at the current scope, no change in Pol II association (i.e., absence of transcriptional repression) does not directly indicate a lack of transcriptional regulation by other means (pause release, elongation rate or processivity, transcription termination, etc.). Without a more thorough investigation of these mechanisms, this confounds definitive claims about their relative contributions to the gene expression landscape.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 ( Public review):

The strength of the current study lies in their establishing the molecular mechanism through which PRMT1 could alter craniofacial development through regulation of the transcriptome, but the data presented to support the claim that a PRMT1-SFPQ axis directly regulates intron retention of the relevant gene networks should be robust and with multiple forms of clear validation. For example, elevated intron retention findings are based on the intron retention index, and according to the manuscript, are assessed considering the relative expression of exons and introns from a given transcript. However, delineating between intron retention and other forms of alternative splicing (i.e., cryptic splice site recognition) requires a more comprehensive consideration of the intron splicing defects that could be represented in data. A certain threshold of intron read coverage (i.e., the percent of an intron that is covered by mapped reads) is needed to ascertain if those that are proximal to exons could represent alternative introns ends rather than full intron retention events. In other words, intron retention is a type of alternative splicing that can be difficult to analyze in isolation given the confounding influence of cryptic splicing and cryptic exon inclusion. If other forms of alternative splicing were assessed and not detected, more confident retention calls can be made.

This manuscript is a mechanistic exploration that follows previous work we published on the role of Prmt1 in craniofacial development, in which genetic deletion of Prmt1 in CNCCs leads to cleft palate and mandibular hypoplasia (PMID: 29986157).

As the reviewer pointed out, a certain threshold of intron read coverage is needed to assess intron retention events. We employed IRTools to assess the collective changes of intron retention between cell-states associated with certain biological function or pathway. IRTools incorporated considerations for intron read coverage by checking the evenness of read distribution in an intron. Specifically, every constitutive intronic regions (CIR) is divided into 10 equally sized bins and the proportion of reads that map to each bin is calculated. CIRs are then ranked according to their imbalance in bin-wise reads distribution, represented by the proportion of reads in its most populated bin. Those among top 1% are considered to contain potentially false IR events and excluded. We further addressed this question by developing another measure of intron retention, intron retention coefficient (IRC), which assesses IR events using the junction reads (Supplemental Figure-S8). Junction reads that straddle two exons are called exon-exon junction reads (spliced reads), and those that straddle an exon and a neighboring intron are called exon-intron junction reads (retained reads). The IRC of an intron is defined as the fraction of junction reads that are exon-intron junction reads: IRC = exon-intron read-count / (exon-exon read-count + exon-intron read-count), where exon-intron read-count = (5’ exon-intron read-count + 3’ exon-intron read-count) / 2. The IRC of a gene is defined as the exon-intron fraction of all junction reads overlapping or over the constitutive introns of this gene. In the calculation of the IRC, only exon-intron junction reads that cover the junction point and overlap both of each side for at least 8 bps were counted, and only exon-exon junction reads that jump over the relevant junction points and overlap each of the respective exons for at least 8 bps were counted. In this process, evenness of the proportion of exon-intron junction reads that are 5’ or 3’ exon-intron junction reads are taken into account. As shown in the Supplemental Figure S7A and S7B, IRC analysis generated consistent results with those obtained from using IRI (Figure 3A and 3I).

In addition, as the reviewer pointed out, intron retention can be difficult to analyze in isolation. We followed the reviewer’s suggestion that “If other forms of alternative splicing were assessed and not detected, more confident retention calls can be made“ and analyzed other forms of alternative splicing for all ECM and GAG genes with significant IRI increase (genes highlighted in Figure-3A and 3I) using rMATS (Supplemental Figure-S9). Among these genes, only 5 genes (Cthcr1, Mmp23, Adamts10, Ccdc80 and Col25a1) showed statistically significant changes in skipped exon, 1 gene (Bmp7) showed significant changes in mutually exclusive exons, and none showed significant changes in alternative 5’ or 3’ splicing. SE and MXE changes detected were marginal (Supplemental figure S8), while the majority of matrix genes with significant intron retention didn’t exhibit other forms of alternative splicing, further supporting the confidence of intron retention calls.

While data presented to support the PRMT1-SFPQ activation axis is quite compelling, that this is directly responsible for the elevated intron retention remains enigmatic. First, in characterizing their PRMT1 knockout model, it is unclear whether the elevated intron retention events directly correspond to downregulated genes.

In the revised manuscript, we demonstrate IR-triggered NMD as a mechanism for transcript decay and downregulation of matrix genes. When IR-triggered NMD was blocked by chemical inhibitor NMDI14, the intron-retaining transcripts showed significant accumulation (new Figure-4). NMD is the RNA surveillance system to degrade aberrant RNAs. Intron retention-triggered NMD in cancer has both promotive and suppressive roles and NMD inhibitors has been tested for cancer therapy including immunotherapy. During embryonic development, the functional significance of NMD machinery is suggested by human genetic findings and mouse genetic models. NMD is driven by a protein complex composed of SMG and UPF proteins. Smg6, Upf1, Upf2 and Upf3a knockout mouse die at early embryonic stages (E5.5-E9.5), and Smg1 gene trap mutant mice die at E12.5 (PMID: 29272451). SMG9 mutation in human patients causes malformation in the face, hand, heart and brain (PMID: 27018474).

We show that in CNCCs NMD functions both as a physiological mechanism and invoked by molecular insult. Blocking NMD in CNCCs caused significant accumulation of intron-retaining Adamts2, Alpl, Eln, Matn2, Loxl1 and Bgn transcripts, suggesting a basal role for NMD to degrade intron-retaining transcripts (Figure-4Ba-4Bf). We further demonstrated the accumulation of Adamts2 and Fbln5 using semi-quantitative PCR with the detection of a longer product from Adamts2 intron 19 and Fbln5 intron 7 (Figure-4Ca-4Ch). In CNCCs and ST2 cells, NMD is further invoked by Prmt1 and Sfpq deficiency. In Prmt1 deficient CNCCs, NMD blockage led to higher accumulation of intron-retaining Adamts2 and Alpl transcripts, suggesting that Prmt1 deficiency triggers NMD to reduce intron-containing transcripts (Figure-4Aa, 4Ab). In Sfpq-depleted ST2 cells, blocking NMD caused accumulation of intron-retaining transcripts Col4a2, St6galnac3 and Ptk7 (Figure-9B, 9C).

Moreover, intron splicing is a well-documented node for gene regulation during embryogenesis and in other proliferation models, and craniofacial defects are known to be associated with 'spliceosomopathies'. However, reproduction of this phenotype does not suggest that the targets of interest are inherently splicing factors, and a more robust assessment is needed to determine the exact nature of alternative splicing in this system. Because there are several known splicing factors downstream of PRMT1 and presented in the supplemental data, the specific attribution of retention to SFPQ would be additionally served by separating its splicing footprint from that of other factors that are primed to cause alternative splicing.

We have previously shown that a group of splicing factors depends on Prmt1 for arginine methylation, including SFPQ (PMID: 31451547). We tested additional splicing factors that are highly expressed in CNCCs and depends on PRMT1 for arginine methylation: SRSF1, EWSR1, TAF15, TRA2B and G3BP1 (Figure-5, 6 and 10). Among these factors, EWSR1 and TRA2B are both methylated in CNCCs and depend on PRMT1 for methylation (Fig. 5 and Supplemental Figure-S3B, S3C). We weren’t able to assess TAF15 methylation because of lack of efficient antibody for the PLA assay. We also demonstrated that their protein expression or subcellular localization was not altered by Prmt1 deletion in CNCCs, unlike SFPQ (Supplemental Figure-S4). To define their splicing footprint, we performed siRNA-mediated knockdown in ST2 cells, followed by RNA-seq and IRI analysis to define differentially regulated genes and introns, which revealed distinct biological pathways regulated by SFPQ, EWSR1, TRA2B and TAF15, but minimal roles of EWSR1, TRA2B and TAF15 on intron retention when compared to SFPQ (Fig. 10F-10S, Supplemental Figure S7A-S7F, Supplemental Tables S4-S6). ECM genes are significantly downregulated by all four splicing factors (Fig. 10F-10I), but EWSR1, TRA2B and TAF15 function through IR-independent mechanisms, such as exon skipping, as exemplified by Postn (Fig. 10J-10S).

Clarifying the relationship between SFPQ and splicing regulation is important given that the observed splicing defects are incongruous with published data presented by Takeuchi et al., (2018) regarding SFPQ control of neuronal apoptosis in mice. In this system, SFPQ was more specifically attributed to the regulation of transcription elongation over long introns and its knockout did not result in significant splicing changes. Thus, to establish the specificity for the SFPQ in regulating these retention events, authors would need to show that the same phenotype is not achieved by mis-regulation of other splicing factors. That the authors chose SFPQ based on its binding profile is understandable but potentially confounding given its mechanism of action in transcription of long introns (Takeuchi 2018). Because mechanisms and rates of transcription can influence splicing and exon definition interactions, the role of SFPQ as a transcription elongation factor versus a splicing factor is inadequately disentangled by authors.

To test whether SFPQ acts as a transcription elongation factor, we performed Pol II Cut&Tag in ST2 cells and demonstrated that depletion of SFPQ only caused marginal changes in either the promoter region or gene body of ECM genes, suggesting that the role of SFPQ as a transcriptional activator or elongation factor is minimal (Fig. 7G, 7H). This finding is distinct from SFPQ function in neurons (PMID: 29719248), suggesting that the activation or recruitment of SFPQ in transcriptional regulation may involve tissue-specific factors in neurons.

Reviewer #2 (Public review):

Summary:

The manuscript by Lima et al examines the role of Prmt1 and SFPQ in craniofacial development. Specifically, the authors test the idea that Prmt1 directly methylates specific proteins that results in intron retention in matrix proteins. The protein SFPQ is methylated by Prmt1 and functions downstream to mediate Prmt1 activity. The genes with retained introns activate the NMD pathway to reduce the RNA levels. This paper describes an interesting mechanism for the regulation of RNA levels during development.

Strengths:

The phenotypes support what the authors claim that Prmt1 is involved in craniofacial development and splicing. The use of state-of-the-art sequencing to determine the specific genes that have intron retention and changes in gene expression is a strength.

Weaknesses:

Some of the data seems to contradict the conclusions. And it is unclear how direct the relationships are between Prmt1 and SFPQ.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

First, the claims regarding the effect of PRMT1 loss on splicing are unclear by the section title. In other words, does loss PRMT1 change the incidence of baseline alternative splicing events, or does it introduce new retention events that are responsible for underwriting the craniofacial phenotype? Consistent with this idea, the narrative could benefit from more cellular and/or histological validations of the transcriptomic defects discovered in the RNAseq, which could help contextualize the bioinformatics data with the developmental defects. Moreover, the conclusions drawn about intron retention could be clarified in terms of how applicable the mechanism is likely to be outside of this tissue-specific set of responsive introns.

Loss of Prmt1 did not cause a global shift in intron retention, as shown in Supplemental Figure S2. Instead, Prmt1 deletion caused increase of intron retention specifically in genes enriched in cartilage development, glycosaminoglycan biology, dendrite and axon, and decreased intron retention in mitochondria and metabolism genes (Table. S1). We also tested matrix protein expression by histology to confirm that transcriptomic defects revealed at the RNA level resulted in lower protein production. The new data are in Figure 3E-3H.

Additionally, invoking NMD to align splicing and differential gene expression data understandable but lacking sufficient controls to be conclusive, such as positive control genes to confirm inhibition of NMD.

To validate the blockage of NMD, glutathione peroxidase 1 (Gpx1) intron 1, a well-documented substrate for NMD, is tested as positive control (Fig 4Ac, 4Ad, 9B).

Additionally, it should be clarified whether NMD is a basal mechanism for the regulation of these introns or whether it is an induced mechanism that is invoked by the molecular insult.

In CNCCs, NMD functions both as a physiological mechanism and invoked by molecular insult. Please refer to responses to Reviewer 1’s public review for detailed explanations.

Further, authors present data downstream of two siRNAs for the same gene target, but it remains unclear how siRNAs for the same gene target produce different effects. It may be helpful for authors to clarify how many of the transcriptomic defects are shared versus unique between the siRNAs.

To address this question, we used bioinformatic analysis of the whole genome data to the similarity in changes caused by the two SFPQ-targeting siRNAs. As shown in the new Fig. 7Ba & 7Bb, transcriptomic and intron changes are consistent between the two siRNAs, suggesting that genes targeted by the two siRNA predominantly overlap. This overlap is illustrated by scatter plot analysis of RNAseq DEG and IRI data from each siRNA against SFPQ.

Finally, we stress the importance of presenting the full conceptual basis for SFPQ's potential role in splicing and gene expression. It is significant to note that SFPQ has been previously studied as a splicing factor and was instead determined to function in support of the transcription elongation rather than in splicing. Thus, if authors are confident that the SFPQ manifests directly in splicing changes they encumber the burden of proof to show that its role in transcription, nor another splicing factor, are driving splicing changes.

We demonstrated that depletion of SFPQ only caused marginal changes in either the promoter region or gene body of ECM genes, suggesting that the role of SFPQ as a transcriptional activator or elongation factor is minimal (Fig. 7G, 7H). Please refer to responses to Reviewer 1’s public review for detailed explanations.

Reviewer #2 (Recommendations for the authors):

(1) It is not clear why the authors focused on intron retention targets vs the other possibilities. Skipped Exon is much higher in terms of the number of changes, please clarify. For the intron retention how is this quantified? The traces are nice, but it is hard to tell which part is retained at this magnification. Also, because the focus is on extracellular matrix (ECM) and NMD it would be nice to show some of those targets here. In the tbx1 trace, some are up and some are down. What does that mean for the gene expression?

We have investigated SE initially and found that genes with significant changes in Prmt1 CKO CNCCs fall into diverse functional pathways. Among them, a few genes are critical for skeletal formation, including Postn and Fn, and the function of their exon skipping has been documented. For example, the two exons that are skipped in Postn, Exon17 and 21, have been shown to regulate craniofacial skeleton shape and mandibular condyle hypertrophic zone thickness using transgenic mouse models (PMID: 36859617). As illustrated by Figure 10, the skipped exon of Postn is regulated by multiple splicing factors that may perform overlapping functions in vivo.

Intron retention of each gene is quantified by the ratio of the overall read density of its constitutive intronic regions (CIRs) to the overall read density of its constitutive exonic regions (CERs) and defined as the intron retention index (IRI). In the first section of Response to Reviewer 1’s comments, we explained additional bioinformatic analysis that was performed to address reviewers’ questions, support the confidence of intron event calls and rule out the possibility of other alternative splicing mechanisms, such as by SE, MXE, A5SS or A3SS (Supplemental Figure S5, S6, Table S7).

(2) RNA-Sequencing of Prmt1 mutants nicely shows gene expression changes, including in ECM and GAG genes. While validation of the sequencing results is not necessarily required, it would be very interesting to show the expression in situ. In addition, the heat map shows both downregulated but also upregulated transcripts. This is expected since this protein regulates many genes. However, the volcano plot shows a significant number of genes upregulated. It would be interesting to show what the upregulated genes are. And what is the proposed mechanism for Prmt1 regulation of upregulated genes?

Validation for the transcriptomic changes is shown in Fig. 3E-3H using immunostaining.

As for upregulated genes in Prmt1 mutant, top pathways include cytokine-mediated signaling pathway, signal transduction by p53 signaling pathway and cell morphogenesis (Figure 2E), which are consistent with our previous reports that Prmt1 deletion induces cytokine production in oral epithelium and leads to p53 accumulation in embryonic epicardium (PMID: 32521264, 29420098). Besides these pathways, Prmt1 deletion also caused upregulation of genes involved in adult behavior, postsynaptic organization and apoptotic process, which is consistent with findings from other labs on PRMT1 function in neuronal and cancer cells (PMID: 34619150, 33127433).

(3) Specific transcripts were shown to have elevated intron retention involved in the ECM and GAG pathway. However in Figure 3D it seems to show the opposite with intronic expression decreased and exonic increases and intronic decrease. This is very important to the final conclusion of the paper. In addition, is there a direct relationship between increased intron and downregulation of this specific gene expression? It seems a bit correlational as it could also be an indirect mechanism. One way to test this is to do in vitro translation with and without the specific intron to test if it results in lower expression.

We apologize for the mis-labeling in previous version of Figure 3D, which is now corrected. We also tried to test the direct relationship between intron and downregulation of matrix genes such as Adamts2 using in vitro experiments, however, the introns of matrix genes with high retention tends to be long, many 10 to 50kb in length, making it challenging to generate mini-gene constructs for molecular analysis. We used a different approach and demonstrated that inhibition of NMD with a chemical inhibitor NMDI14 caused dramatic accumulation of the Adamts2, Alpl, Eln, Matn2, Loxl1 and Bgn transcripts, suggesting that retained introns triggered NMD to regulate gene expression and this mechanism acts as a physiological level in CNCCs (Fig. 4). We also blocked NMD in control and Prmt1 null CNCCs, where NMD blockage led to higher accumulation of Adamts2 and Alpl transcripts, suggesting that upon Prmt1 deficiency, NMD is further utilized to degrade intron-containing transcripts (Fig. 4). Similarly, in Sfpq-depleted ST2 cells, blocking NMD caused accumulation of intron-retaining transcripts Col4a2, St6galnac3 and Ptk7 (Fig. 9A, 9B).

(4) While Figure 4 nicely shows the methylation of SFPQ is reduced in Prmt1 CKO cells, it is unclear which reside this methylation occurs. Also the overall expression of SFPQ is also down so it is possible that the methylation is indirect ie Prmt1 regulates some other methyltransferase that regulates SFPQ. Or that because the overall level of SFPQ is down, there is no protein to methylate. How do the authors differentiate between these possibilities?

Previously, arginine methylation of SFPQ has been characterized using in vitro reaction and cell lines with biochemical assays by Snijders., et al in 2015 (PMID: 25605962). Among all PRMTs that catalyze asymmetric arginine dimethylation (ADMA), SFPQ is methylated by only PRMT1 and PRMT3, with PRMT1 showing higher efficiency while PRMT3 showing a lower efficiency. However, PRMT3 is mainly cytosolic. Its expression in CNCCs is about 100-fold lower than PRMT1 (Fig. 1). Based on these knowledges, PRMT1 is the primary arginine methyltransferase for SFPQ, a nuclear protein in CNCCs. We and others have shown in a previous publication that SFPQ methylation on arginine 7 and 9 depends on PRMT1 (PMID: 31451547).

To investigate SFPQ protein degradation in CNCCs, we used MG132 to block proteasomal degradation and observed a partial rescue of SFPQ protein degradation in Prmt1 mutant embryos, suggesting that SFPQ is degraded through proteasomal-mediated mechanism. To address the relationship between SFPQ methylation and protein expression, we assessed arginine methylation of SFPQ that accumulated after MG132 treatment. The accumulated SFPQ was not methylated, confirming the absence of methylation even when SFPQ protein expression is restored.

Snijders., et al, also shown that citrullination induced by PADI4 regulate SFPQ stability (Snijders 2015). We considered this possibility and assessed the expression levels of PADIs. In E13.5 and E15.5 CNCCs, PADI1-4 mRNA expression levels are very low (TPM<5), suggesting that PADIs may not regulate SFPQ stability in CNCCs. A detailed mechanism as to how PRMT1-mediated SFPQ methylation controls stability awaits further investigation.

(5) For the Sfpq deleted experiment, it seems that the two knockdowns are not similar in the gene targets and GO terms different except Wnt signaling. This makes this data difficult to interpret. The genes identified as intron retention are different than the ones identified in Prmt1 deletion and not reduced as much. How does this fit in with the Prmt1 story? If working through Sfpq, it assumes that the targets will be similar and more the 8% would be in common.

To address the first concern, we used bioinformatic analysis of the whole genome data to the similarity in changes caused by the two SFPQ-targeting siRNAs. As shown in the new Fig. 7Ba & 7Bb, transcriptomic and intron changes are consistent between the two siRNAs, suggesting that genes targeted by the two siRNA predominantly overlap. This overlap is illustrated by scatter plot analysis of RNAseq DEG and IRI data from each siRNA against SFPQ.

We have previously identified a group of splicing factors that depends on PRMT1 for arginine methylation, including SFPQ (PMID: 31451547). In the new data in Figures 5, 6 and 10, we tested an additional five PRMT1-dependent splicing factors that are highly expressed in CNCCs: SRSF1, EWSR1, TAF15, TRA2B and G3BP1 (Fig. 5, 6 and 10). Among these factors, SRSF1 and G3BP1 are predominantly expressed in the cytosol of NCCs at E13.5. As splicing activity in the nucleus is needed for pre-mRNA splicing, we excluded these two and focused on the other three proteins. EWSR1 and TRA2B are both methylated in CNCCs and depend on PRMT1 for methylation (Fig. 5). We weren’t able to assess TAF15 methylation because of lack of efficient antibody for the PLA assay. We also demonstrated that their protein expression or subcellular localization was not altered by Prmt1 deletion in CNCCs, unlike SFPQ (Fig. S2). To define their splicing footprint, we performed siRNA-mediated knockdown in ST2 cells, followed by RNA-seq and IRI analysis to define differentially regulated genes and introns, which revealed distinct biological pathways regulated by SFPQ, EWSR1, TRA2B and TAF15, but minimal roles of EWSR1, TRA2B and TAF15 on intron retention when compared to SFPQ (Fig. 10F-10I, Supplemental Figure S7A-S7F). ECM genes are significantly downregulated by all four splicing factors (Fig. 10J-10M), but EWSR1, TRA2B and TAF15 regulate transcription or exon skipping instead of IR, as exemplified by Alpl and Postn (Fig. 10N-10T).

(6) The addition of an NMD mechanism is interesting but not surprising that when inhibiting the pathway broadly, there is an increase in gene expression in the mesoderm cell line. How specific is this to craniofacial development?

NMD is driven by a protein complex composed of SMG and UPF proteins. We show in the revised manuscript that NMD is both a physiological mechanism in CNCCs and triggered by genetic disturbance (Fig. 4). These data are in line with human patient reports where SMG9 mutation in human causes malformation in the face, hand, heart and brain (PMID: 27018474). Mouse genetic studies also demonstrated roles of NMD components during embryonic development.Smg6, Upf1, Upf2 and Upf3a knockout mouse die at early embryonic stages (E5.5-E9.5), and Smg1 gene trap mutant mice die at E12.5 (Han 2018). Additionally, intron retention-triggered NMD in cancer has both promotive and suppressive roles and NMD inhibitors has been tested for cancer therapy and recently cancer immunotherapy. Our findings highlight matrix genes as one of the key targets for NMD during craniofacial development.

Minor:

(1) The supplemental figures are difficult to understand. In the first upload there are many figures and tables, some excel files that are separate uploads and some not. Please upload as separate files so it is clear. And also put them in order that they are in the manuscript.

(2) For the heat map in figure 2B, it would be good to show all the genes or none at all. It seems a bit like cherry-picking to highly only a few. And they are not labeled where they are located in the graph. Are these the top lines if so please label.

(3) Gene names in Figure 3A are difficult to read. I would also not consider BMP7 an ECM gene.

(4) A summary diagram of the interactions proposed will help to make this more understandable.

The supplemental figures are reorganized and uploaded as separate word and excel documents. For Heat map in Fig. 2B, we have removed the gene names. For Fig. 3A, only the most significantly changed gene are labeled in red dots with names. We didn’t label all the genes because of the large number of genes. For the new Figure 3B, we have replaced BMP7. A schematic summary is also added to Supplemental Fig. S9 to illustrate the PRMT1-SFPQ pathway.

Reviewer #1 (Public review):

Summary:

In this study, the authors investigated the detailed structural mechanism of activation of ABHD5 upon interaction with lipid structures (bilayer and LD). The authors used an elaborate multiscale computational workflow, incorporating coarse-grained, all-atom, and enhanced-sampling molecular dynamics simulations, to propose a structural mechanism for the interaction and activation of ABHD5, as well as its specific interaction with TAG in LD. The authors then corroborated these observations with experimental studies involving hydrogen-deuterium exchange coupled with mass spectrometry of wild-type ABHD5 to assess the structural and conformational changes in ABHD5 upon binding, as well as mutagenesis with cell-based and in vitro assays monitoring membrane association, defining specific interactions that infer ABHD5 to localize LD.

Strengths:

The manuscript is well-written, and the data are reported in high-quality figures. The experimental design and data analysis are rigorous and support the conclusion. One major strength is the multiscale computational work that reveals a mechanism for the insertion of ABHD5 into lipid bilayers and LD involving the insertion of the N-term portion and the lid helix motif. The design of the computational workflow was very elaborate, and the undertaking was quite extensive, with multiple strategies to (GC, all-atom MD and GaMD). The authors then elegantly generate a hypothesis from these observations to experimentally corroborate the proposed mechanism. Particularly, the HDX-MS data support the engagement of the two regions upon binding, and the fluorescence microscopy data show the role of specific residues in localization/specificity to LD.

Weaknesses:

The following limitation is noted. Central to this manuscript is the model, as observed computationally, that initial lipid interaction by the N-term insertion is followed by the insertion of lid-helix in the membrane, which undergoes a conformational switch in the process. However, HDX-MS reveals that, in the unbound form, the lid helix region displays a bimodal isotopic envelope, revealing two species, one with low uptake, suggesting a structured species and one with high uptake, suggesting a less structured species. It is unclear from the manuscript whether the authors think the bimodality fits EX1 regime kinetics or not. Regardless, the model of unbound ABHD5 shows a lid-helix region devoid of secondary structure (Figure 5A), which is more consistent with the unprotected species. The authors also mention that previous modeling had pointed to the high flexibility of the insertion domain. Upon binding, the lid-helix region seems to be ordered from computational observations and loses bimodality by HDX-MS with a deuterium uptake consistent with the protected species of the bimodal envelop in the unbound form. The authors fall short of interpreting or even discussing what the bimodality of the lid-helix represents in the unbound form. What does the protected species in the bimodal envelope represent? Is it a transition representing lid-helix formation and unfolding? Does it imply that interaction and insertion into the lipid structures are governed by conformational selection? This issue should be at the very least acknowledged and discussed, or optimally investigated by performing more integrative studies of the HDX-MS data with the extensive computational data at hand, using existing protection factor calculations or HDX-guided ensemble refinement methods.

Reviewer #2 (Public review):

Summary:

The manuscript describes a combined computational and experimental approach to investigate the ABHD5 binding to and insertion into membranes.

Strengths:

Mutational experiments support computational findings obtained on ABHD5 membrane insertion with enhanced-sampling atomistic simulations.

Weaknesses:

While the addressed problem is interesting, I have several concerns, which fall into two categories:

(A) I see statements throughout the manuscript, e.g. on PNPLA activation, that are not supported by the results.

(B) The presentation of the computational and experimental results lacks in part clarity and detail.

Comments and questions on (A):

(1) I think the following statements in the abstract, which go beyond ABHD5 membrane binding, are not supported by the presented data:

the addition "to control lipolytic activation" in the 3rd sentence of the abstract.

further below ".... transforming ABHD5 into an active and membrane-localized regulator".

(2) The authors state in the Introduction (page numbers and line numbers are missing to be more specific):

"We hypothesize that binding of ABHD5 alters the nanoscale chemical and biophysical properties of the LD monolayer, which, combined with direct protein-protein interactions, enables PNPLA paralogs to access membrane-restricted substrates. This regulatory mechanism represents a paradigm shift from conventional enzyme-substrate interactions to sophisticated allosteric control systems that operate at membrane interfaces."

This hypothesis and the suggested paradigm shift are not supported by the data. Protein-protein interactions are not considered. What is meant by "sophisticated allosteric control"?

(3) The authors state in the Results section:

"We hypothesize that this TAG nanodomain is critical for ABHD5-activated TAG hydrolysis by PNPLA2." In previous pages, the authors state the location of the nanodomain: "TAG nanodomain under ABHD5".

If the nanodomain is located under ABHD5, how can it be accessible to PNPLA2? To my understanding, ABHD5 then sterically blocks access of PNPLA2 to the TAG nandomain.

(4) Another statement: "Our findings suggest that ABHD5-mediated membrane remodeling regulates lipolysis in part by regulating PNPLA2 access to its TAG substrate."

I don't see how the reported results support this statement (see point 3 above).

Comments and questions on (B):

(1) The authors state that the GaMD simulations started "from varying conformations observed during CGMD".

What is missing is a clear description of the CGMD simulation conformations, and the CG simulations as a whole, prior to the results section on GaMD. The authors use standard secondary and tertiary constraints in the Martini CG simulations. Do the authors observe some (constrained) conformational changes of ABHD5 already in the CG simulations (depending on the strength of the constraints)? Or do the conformational changes occur exclusively in the GaMD simulations? Both are fine, but this needs to be described.

(2) The authors write: "Three replicas of GaMD were performed."

Do these replicas lead to similar, or statistically identical, membrane-bound ABHD5 conformations? Is this information, i.e. a statistical analysis of differences in the replica runs, already included in the manuscript?

(3) The authors state on the hydrogen exchange results:

"HDX-MS provided orthogonal experimental evidence for the dynamics of the lid. In solution, a peptide (residues 200-226) spanning the lid helix displayed a bimodal isotopic distribution (Fig. S4), indicating the coexistence of different conformations. Upon LD binding, this distribution shifted to a single, low-exchange peak, demonstrating stabilization of the membrane-bound conformation with reduced solvent accessibility. These experimental observations corroborate our MD simulations."

I find this far too short to be understandable. Also, there are no computational results of ABHD5 in solution that show a bimodal conformational distribution of the lid helix, which is observed in the hydrogen exchange experiments. Which aspects of the MD simulations are corroborated?

This information is important because it clearly explains the consequences of late submissions, helps students manage their time effectively, and ensures fairness by applying consistent grading penalties to all students.

hold

Author response

Public Reviews:

Reviewer #1 (Public review):

This study presents evidence that the addition of the two GTPases EngA and ObgE to reactions comprised of rRNAs and total ribosomal proteins purified from native bacterial ribosomes can bypass the requirements for non-physiological temperature shifts and Mg⁺² ion concentrations for in vitro reconstitution of functional E. coli ribosomes.

Strengths:

This advance allows ribosome reconstitution in a fully reconstituted protein synthesis system containing individually purified recombinant translation factors, with the reconstituted ribosomes substituting for native purified ribosomes to support protein synthesis. This work potentially represents an important development in the long-term effort to produce synthetic cells.

Weaknesses:

While much of the evidence is solid, the analysis is incomplete in certain respects that detract from the scientific quality and significance of the findings:

(1) The authors do not describe how the native ribosomal proteins (RPs) were purified, and it is unclear whether all subassemblies of RPs have been disrupted in the purification procedure. If not, additional chaperones might be required beyond the two GTPases described here for functional ribosome assembly from individual RPs.

Native ribosomal proteins (RPs) were prepared from native ribosomes, according to the well-established protocol described by Dr. Knud H. Nierhaus [Nierhaus, K. H. Reconstitution of ribosomes in Ribosomes and protein synthesis: A Practical Approach (Spedding G. eds.) 161-189, IRL Press at Oxford University Press, New York (1990)]. In this method, ribosome proteins are subjected to dialysis in 6 M urea buffer, a strong denaturing condition that may completely disrupt ribosomal structure and dissociate all ribosomal protein subassemblies. To make this point clear, we will describe the ribosomal protein (RP) preparation procedure in the manuscript, rather than merely referring to the book.

In addition, we would like to clarify one point related to this comment. The focus of the present study is to show that the presence of two factors is required for single-step ribosome reconstitution under translation-compatible, cell-free conditions. We do not intend to claim that these two factors are absolutely sufficient for ribosome reconstitution. Hence, we will revise the manuscript to more explicitly state what this work does and does not conclude.

(2) Reconstitution studies in the past have succeeded by using all recombinant, individually purified RPs, which would clearly address the issue in the preceding comment and also eliminate the possibility that an unknown ribosome assembly factor that co-purifies with native ribosomes has been added to the reconstitution reactions along with the RPs.

As noted in the response to the Comment (1), the focus of the present study is the requirement of the two factors for functional ribosome assembly. Therefore, we consider that it is not necessary to completely exclude the possibility that unknown ribosome assembly factors are present in the RP preparation. Nevertheless, we agree that it is important to clarify what factors, if any, are co-present in the RP fraction. To address this, we plan to add proteomic analysis results of the TP70 preparation.

We also agree that additional, as-yet-unidentified components, including factors involved in rRNA modification, could plausibly further improve assembly efficiency. We will explicitly note this possibility in the Discussion.

Finally, extending the system to the use of in vitro-transcribed rRNA and fully recombinant ribosomal proteins could be essentially a next step of this study, and we are currently exploring these directions in our laboratory. However, we consider them beyond the scope of the present study and will provide them as future perspectives of this study in the Discussion.

(3) They never compared the efficiency of the reconstituted ribosomes to native ribosomes added to the "PURE" in vitro protein synthesis system, making it unclear what proportion of the reconstituted ribosomes are functional, and how protein yield per mRNA molecule compares to that given by the PURE system programmed with purified native ribosomes.

We consider that it is feasible to estimate the GFP synthesis rate from the increase in fluorescence over time under conditions where the template mRNA is in excess, and to compare this rate directly between reconstituted and native ribosomes. We will therefore consider performing this experiment. This comparison should provide insight into what fraction of ribosomes reconstituted in our system are functionally active.

By contrast, quantifying protein yield per mRNA molecule is substantially more challenging. The translation system is complex, and the apparent yield per mRNA can vary depending on factors such as differences in polysome formation efficiency. In addition, the PURE system is a coupled transcription–translation setup that starts from DNA templates, which further complicates rigorous normalization on a per-mRNA basis. Because the main focus of this study is to determine how many functionally active ribosomes can be reconstituted under translation-compatible conditions, we plan to address this comment by carrying out the former experiment.

(4) They also have not examined the synthesized GFP protein by SDS-PAGE to determine what proportion is full-length.

Because we can add an affinity tag to the GFP reporter, it should be feasible to selectively purify the synthesized protein from the reaction mixture and analyze it by SDS–PAGE. We therefore plan to perform this experiment.

(5) The previous development of the PURE system included examinations of the synthesis of multiple proteins, one of which was an enzyme whose specific activity could be compared to that of the native enzyme. This would be a significant improvement to the current study. They could also have programmed the translation reactions containing reconstituted ribosomes with (i) total native mRNA and compared the products in SDS-PAGE to those obtained with the control PURE system containing native ribosomes; (ii) with specifc reporter mRNAs designed to examine dependence on a Shine-Dalgarno sequence and the impact of an in-frame stop codon in prematurely terminating translation to assess the fidelity of initiation and termination events; and (iii) an mRNA with a programmed frameshift site to assess elongation fidelity displayed by their reconstituted ribosomes.

Following the recommendation, we plan to test the synthesis of at least one additional protein with enzymatic activity, in addition to GFP, so that the activity of the translated product can be assessed.

We agree that comparing translation products using total mRNA, testing dependence on the Shine–Dalgarno sequence, and performing dedicated assays to evaluate initiation/elongation/termination fidelity are all attractive and valuable studies. However, we consider these to be beyond the scope of the present manuscript. We will therefore describe them explicitly as future directions in the Discussion.

At the same time, we anticipate that mass spectrometric (MS) analysis of GFP and the enzyme product(s) that we attempt to synthesize could partially address concerns related to product integrity (e.g., truncations) and, to some extent, translational fidelity. We therefore plan to carry out MS analysis of these translated products.

Reviewer #2 (Public review):

This study presents a significant advance in the field of in vitro ribosome assembly by demonstrating that the bacterial GTPases EngA and ObgE enable single-step reconstitution of functional 50S ribosomal subunits under near-physiological conditions-specifically at 37 {degree sign}C and with total Mg²⁺ concentrations below 10 mM.

This achievement directly addresses a long-standing limitation of the traditional two-step in vitro assembly protocol (Nierhaus & Dohme, PNAS 1974), which requires non-physiological temperatures (44-50 {degree sign}C), and high Mg²⁺ concentrations (~20 mM). Inspired by the integrated Synthesis, Assembly, and Translation (iSAT) platform (Jewett et al., Mol Syst Biol 2013), leveraging E. coli S150 crude extract, which supplies essential assembly factors, the authors hypothesize that specific ribosome biogenesis factors-particularly GTPases present in such extracts-may be responsible for enabling assembly under mild conditions. Through systematic screening, they identify EngA and ObgE as the minimal pair sufficient to replace the need for temperature and Mg²⁺ shifts when using phenol-extracted (i.e., mature, modified) rRNA and purified TP70 proteins.

However, several important concerns remain:

(1) Dependence on Native rRNA Limits Generalizability

The current system relies on rRNA extracted from native ribosomes via phenol, which retains natural post-transcriptional modifications. As the authors note (lines 302-304), attempts to assemble active 50S subunits using in vitro transcribed rRNA, even in the presence of EngA and ObgE, failed. This contrasts with iSAT, where in vitro transcribed rRNA can yield functional (though reduced-activity, ~20% of native) ribosomes, presumably due to the presence of rRNA modification enzymes and additional chaperones in the S150 extract. Thus, while this study successfully isolates two key GTPase factors that mimic part of iSAT's functionality, it does not fully recapitulate iSAT's capacity for de novo assembly from unmodified RNA. The manuscript should clarify that the in vitro assembly demonstrated here is contingent on using native rRNA and does not yet achieve true bottom-up reconstruction from synthetic parts. Moreover, given iSAT's success with transcribed rRNA, could a similar systematic omission approach (e.g., adding individual factors) help identify the additional components required to support unmodified rRNA folding?

We fully recognize the reviewer’s point that our current system has not yet achieved a true bottom-up reconstruction. Although we intended to state this clearly in the manuscript, the fact that this concern remains indicates that our description was not sufficiently explicit. We will therefore revisit the organization and wording of the manuscript and revise it to ensure that this limitation is clearly communicated to readers.

(2) Imprecise Use of "Physiological Mg²⁺ Concentration"

The abstract states that assembly occurs at "physiological Mg²⁺ concentration" (<10 mM). However, while this total Mg²⁺ level aligns with optimized in vitro translation buffers (e.g., in PURE or iSAT systems), it exceeds estimates of free cytosolic [Mg²⁺] in E. coli (~1-2 mM). The authors should clarify that they refer to total Mg²⁺ concentrations compatible with cell-free protein synthesis, not necessarily intracellular free ion levels, to avoid misleading readers about true physiological relevance.

We agree that this is a very reasonable point. We will therefore revise the manuscript to clarify that we are referring to the total Mg²⁺ concentration compatible with cell-free protein synthesis, rather than the intracellular free Mg²⁺ level under physiological conditions.

In summary, this work elegantly bridges the gap between the two-step method and the extract-dependent iSAT system by identifying two defined GTPases that capture a core functionality of cellular extracts: enabling ribosome assembly under translation-compatible conditions. However, the reliance on native rRNA underscores that additional factors - likely present in iSAT's S150 extract - are still needed for full de novo reconstitution from unmodified transcripts. Future work combining the precision of this defined system with the completeness of iSAT may ultimately realize truly autonomous synthetic ribosome biogenesis.

This is the full workflow diagram. First, each molecule has a universal adapter + sample barcode ligated to each 5' end. Then, only 1 strand of each molecule is amplified using GSP1 (which is pretty nonspecific amplification) and a universal adapter primer over 10 PCR cycles. The resulting molecules should have a PCR multiplexing tag on the end, I guess. Then, only 1 strand of each amplified molecule is amplified using GSP2 (which is super selective) and a universal adapter primer over 10-14 PCR cycles. The resulting molecules should have a second adapter sequence by the end. An indexing primer is then attached to the second adapter sequence of each molecule.

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Reply to the reviewers

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

Summary:

Damaris et al. perform what is effectively an eQTL analysis on microbial pangenomes of E. coli and P. aeruginosa. Specifically, they leverage a large dataset of paired DNA/RNA-seq information for hundreds of strains of these microbes to establish correlations between genetic variants and changes in gene expression. Ultimately, their claim is that this approach identifies non-coding variants that affect expression of genes in a predictable manner and explain differences in phenotypes. They attempt to reinforce these claims through use of a widely regarded promoter calculator to quantify promoter effects, as well as some validation studies in living cells. Lastly, they show that these non-coding variations can explain some cases of antibiotic resistance in these microbes.

Major comments

Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

The authors convincingly demonstrate that they can identify non-coding variation in pangenomes of bacteria and associate these with phenotypes of interest. What is unclear is the extent by which they account for covariation of genetic variation? Are the SNPs they implicate truly responsible for the changes in expression they observe? Or are they merely genetically linked to the true causal variants. This has been solved by other GWAS studies but isn't discussed as far as I can tell here.

We thank the reviewer for their effective summary of our study. Regarding our ability to identify variants that are causal for gene expression changes versus those that only “tag” the causal ones, here we have to again offer our apologies for not spelling out the limitation of GWAS approaches, namely the difficulty in separating associated with causal variants. This inherent difficulty is the main reason why we added the in-silico and in-vitro validation experiments; while they each have their own limitations, we argue that they all point towards providing a causal link between some of our associations and measured gene expression changes. We have amended the discussion (e.g. at L548) section to spell our intention out better and provide better context for readers that are not familiar with the pitfalls of (bacterial) GWAS.

They need to justify why they consider the 30bp downstream of the start codon as non-coding. While this region certainly has regulatory impact, it is also definitely coding. To what extent could this confound results and how many significant associations to expression are in this region vs upstream?

We agree with the reviewer that defining this region as “non-coding” is formally not correct, as it includes the first 10 codons of the focal gene. We have amended the text to change the definition to “cis regulatory region” and avoided using the term “non-coding” throughout the manuscript. Regarding the relevance of this including the early coding region, we have looked at the distribution of associated hits in the cis regulatory regions we have defined; the results are shown in Supplementary Figure 3.

We quantified the distribution of cis associated variants and compared them to a 2,000 permutations restricted to the -200bp and +30bp window in both E. coli * (panel A) and P. aeruginosa* (panel B). As it can be seen, the associated variants that we have identified are mostly present in the 200bp region and the +30bp region shows a mild depletion relative to the random expectation, which we derived through a variant position shuffling approach (2,000 replicates). Therefore, we believe that the inclusion of the early coding region results in an appreciable number of associations, and in our opinion justify its inclusion as a putative “cis regulatory region”.

The claim that promoter variation correlates with changes in measured gene expression is not convincingly demonstrated (although, yes, very intuitive). Figure 3 is a convoluted way of demonstrating that predicted transcription rates correlate with measured gene expression. For each variant, can you do the basic analysis of just comparing differences in promoter calculator predictions and actual gene expression? I.e. correlation between (promoter activity variant X)-(promoter activity variant Y) vs (measured gene expression variant X)-(measured gene expression variant Y). You'll probably have to

We realize that we may not have failed to properly explain how we carried out this analysis, which we did exactly in the way the reviewer suggests here. We had in fact provided four example scatterplots of the kind the reviewer was requesting as part of Figure 4. We have added a mention of their presence in the caption of Figure 3.

Figure 7 it is unclear what this experiment was. How were they tested? Did you generate the data themselves? Did you do RNA-seq (which is what is described in the methods) or just test and compare known genomic data?

We apologize for the lack of clarity here; we have amended the figure’s caption and the corresponding section of the results (i.e. L411 and L418) to better highlight how the underlying drug susceptibility data and genomes came from previously published studies.

Are the data and the methods presented in such a way that they can be reproduced?

No, this is the biggest flaw of the work. The RNA-Seq experiment to start this project is not described at all as well as other key experiments. Descriptions of methods in the text are far too vague to understand the approach or rationale at many points in the text. The scripts are available on github but there is no description of what they correspond to outside of the file names and none of the data files are found to replicate the plots.

We have taken this critique to heart, and have given more details about the experimental setup for the generation of the RNA-seq data in the methods as well as the results sections. We have also thoroughly reviewed any description of the methods we have employed to make sure they are more clearly presented to the readers. We have also updated our code repository in order to provide more information about the meaning of each script provided, although we would like to point out that we have not made the code to be general purpose, but rather as an open documentation on how the data was analyzed.

Figure 8B is intended to show that the WaaQ operon is connected to known Abx resistance genes but uses the STRING method. This requires a list of genes but how did they build this list? Why look at these known ABx genes in particular? STRING does not really show evidence, these need to be substantiated or at least need to justify why this analysis was performed.

We have amended the Methods section (“Gene interaction analysis”, L799) to better clarify how the network shown in this panel was obtained. In short, we have filtered the STRING database to identify genes connected to members of the waa operon with an interaction score of at least 0.4 (“moderate confidence”), excluding the “text mining” field. Antimicrobial resistance genes were identified according to the CARD database. We believe these changes will help the readers to better understand how we derived this interaction.

Are the experiments adequately replicated and statistical analysis adequate?

An important claim on MIC of variants for supplementary table 8 has no raw data and no clear replicates available. Only figure 6, the in vitro testing of variant expression, mentions any replicates.

We have expanded the relevant section in the Methods (“Antibiotic exposure and RNA extraction”, L778) to provide more information on the way these assays were carried out. In short, we carried out three biological replicates, the average MIC of two replicates in closest agreement was the representative MIC for the strain. We believe that we have followed standard practice in the field of microbiology, but we agree that more details were needed to be provided in order for readers to appreciate this.

Minor comments

Specific experimental issues that are easily addressable..

Are prior studies referenced appropriately?

There should be a discussion of eQTLs in this. Although these have mostly been in eukaryotes a. https://doi.org/10.1038/s41588-024-01769-9 ; https://doi.org/10.1038/nrg3891.

We have added these two references, which provide a broader context to our study and methodology, in the introduction.

Line 67. Missing important citation for Ireland et al. 2020 https://doi.org/10.7554/eLife.55308

Line 69. Should mention Johns et al. 2018 (https://doi.org/10.1038/nmeth.4633) where they study promoter sequences outside of E. coli

Line 90 - replace 'hypothesis-free' with unbiased

We have implemented these changes.

Line 102 - state % of DEGs relative to the entire pan-genome

Given that the study is focused on identifying variants that were associated with changes in expression for reference genes (i.e. those present in the reference genome), we think that providing this percentage would give the false impression that our analysis include accessory genes that are not encoded by the reference isolate, which is not what we have done.

Figure 1A is not discussed in the text

We have added an explicit mention of the panels in the relevant section of the results.

Line 111: it is unclear what enrichment was being compared between, FIgures 1C/D have 'Gene counts' but is of the total DEGs? How is the p-value derived? Comparing and what statistical test was performed? Comparing DEG enrichment vs the pangenome? K12 genome?

We have amended the results and methods section, as well as Figure 1’s caption to provide more details on how this analysis was carried out.

Line 122-123: State what letters correspond to these COG categories here

We have implemented the clarifications and edits suggested above

Line 155: Need to clarify how you use k-mers in this and how they are different than SNPs. are you looking at k-mer content of these regions? K-mers up to hexamers or what? How are these compared. You can't just say we used k-mers.

We have amended that line in the results section to more explicitly refer to the actual encoding of the k-mer variants, which were presence/absence patterns for k-mers extracted from each target gene’s promoter region separately, using our own developed method, called panfeed. We note that more details were already given in the methods section, but we do recognize that it’s better to clarify things in the results section, so that more distracted readers get the proper information about this class of genetic variants.

Line 172: It would be VERY helpful to have a supplementary figure describing these types of variants, perhaps a multiple-sequence alignment containing each example

We thank the reviewer for this suggestion. We have now added Supplementary Figure 3, which shows the sequence alignments of the cis-regulatory regions underlying each class of the genetic marker for both E. coli and P. aeruginosa.

Figure 4: THis figure is too small. Why are WaaQ and UlaE being used as examples here when you are supposed to be explicitly showing variants with strong positive correlations?

We rearranged the figure’s layout to improve its readability. We agree that the correlation for waaQ and ulaE is weaker than for yfgJ and kgtP, but our intention was to not simply cherry-pick strong examples, but also those for which the link between predicted promoter strength and recorded gene expression was less obvious.

Figure 4: Why is there variation between variants present and variant absent? Is this due to other changes in the variant? Should mention this in the text somewhere

Variability in the predicted transcription rate for isolates encoding for the same variant is due to the presence of other (different) variants in the region surrounding the target variant. PromoterCalculator uses nucleotide regions of variable length (78 to 83bp) to make its predictions, while the variants we are focusing on are typically shorter (as shown in Figure 4). This results in other variants being included in the calculation and therefore slightly different predicted transcription rates for each strain. We have amended the caption of Figure 4 to provide a succinct explanation of these differences.

Line 359: Need to talk about each supplementary figure 4 to 9 and how they demonstrate your point.

We have expanded this section to more explicitly mention the contents of these supplementary figures and why they are relevant for the findings of this section (L425).

Are the text and figures clear and accurate?

Figure 4 too small

We have fixed the figure, as described above

Acronyms are defined multiple times in the manuscript, sometimes not the first time they are used (e.g. SNP, InDel)

Figure 8A - Remove red box, increase label size

Figure 8B - Low resolution, grey text is unreadable and should be darker and higher resolution

Line 35 - be more specific about types of carbon metabolism and catabolite repression

Line 67 - include citation for ireland et al. 2020 https://doi.org/10.7554/eLife.55308

Line 74 - You talk about looking in cis but don't specify how mar away cis is

Line 75 - we encoded genetic variants..... It is unclear what you mean here

Line 104 - 'were apart of operons' should clarify you mean polycistronic or multi-gene operons. Single genes may be considered operonic units as well.

We have addressed all the issues indicated above.

Figure 2: THere is no axis for the percents and the percents don't make sense relative to the bars they represent??

We realize that this visualization might not have been the most clear for readers, and have made the following improvement: we have added the number of genes with at least one association before the percentage. We note that the x-axis is in log scale, which may make it seem like the light-colored bars are off. With the addition of the actual number of associated genes we think that this confusion has been removed.

Figure 2: Figure 2B legend should clarify that these are individual examples of Differential expression between variants

Line 198-199: This sentence doesn't make sense, 'encoded using kmers' is not descriptive enough

Line 205: Should be upfront about that you're using the Promoter Calculator that models biophysical properties of promoter sequences to predict activity.

Line 251: 'Scanned the non-coding sequences of the DEGs'. This is far too vague of a description of an approach. Need to clarify how you did this and I didn't see in the method. Is this an HMM? Perfect sequence match to consensus sequence? Some type of alignment?

Line 257-259: This sentence lacks clarity

We have implemented all the suggested changes and clarified the points that the reviewer has highlighted above.

Line346: How were the E. coli isolates tested? Was this an experiment you did? This is a massive undertaking (1600 isolates * 12 conditions) if so so should be clearly defined

While we have indicated in the previous paragraph that the genomes and antimicrobial susceptibility data were obtained from previously published studies, we have now modified this paragraph (e.g. L411 and L418) slightly to make this point even clearer.

Figure 6A: The tile plot on the right side is not clearly labeled and it is unclear what it is showing and how that relates to the bar plots.

In the revised figure, we have clarified the labeling of the heatmap to now read “Log2(Fold Change) (measured expression)” to indicate that it represents each gene’s fold changes obtained from our initial transcriptomic analysis. We have also included this information in the caption of the figure, making the relationship between the measured gene expression (heatmap) and the reporter assay data (bar plots) clear to the reader.

FIgure 6B: typo in legend 'Downreglation'

We thank the review for pointing this out. The typo has been corrected to “Down regulation” in the revised figure.

Line 398: Need to state rationale for why Waaq operon is being investigated here. WHy did you look into individual example?

We thank the reviewer for asking for a clarification here. Our decision to investigate the waaQ gene was one of both biological relevance and empirical evidence. In our analysis associating non-coding variants with antimicrobial resistance using the Moradigaravand et al. dataset, we identified a T>C variant at position 3808241 that was associated with resistance to Tobramycin. We also observed this variant in our strain collection, where it was associated with expression changes of the gene, suggesting a possible functional impact. The waa operon is involved in LPS synthesis, a central determinant of the bacteria’s outer membrane integrity and a well established virulence factor. This provided a plausible biological mechanism through which variation could influence antimicrobial susceptibility. As its role in resistance has not been extensively characterized, this represents a good candidate for our experimental validation. We have now included this rationale in our revised manuscript (i.e. L476).

Figure 8: Can get rid of red box

We have now removed the red box from Figure 8 in the revised version.

Line 463 - 'account for all kinds' is too informal

Mix of font styles throughout document

We have implemented all the suggestions and formatting changes indicated above.

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

In their manuscript "Cis non-coding genetic variation drives gene expression changes in the E. coli and P. aeruginosa pangenomes", Damaris and co-authors present an extensive meta-analysis, plus some useful follow up experiments, attempting to apply GWAS principles to identify the extent to which differences in gene expression between different strains within a given species can be directly assigned to cis-regulatory mutations. The overall principle, and the question raised by the study, is one of substantial interest, and the manuscript here represents a careful and fascinating effort at unravelling these important questions. I want to preface my review below (which may otherwise sound more harsh than I intend) with the acknowledgment that this is an EXTREMELY difficult and challenging problem that the authors are approaching, and they have clearly put in a substantial amount of high quality work in their efforts to address it. I applaud the work done here, I think it presents some very interesting findings, and I acknowledge fully that there is no one perfect approach to addressing these challenges, and while I will object to some of the decisions made by the authors below, I readily admit that others might challenge my own suggestions and approaches here. With that said, however, there is one fundamental decision that the authors made which I simply cannot agree with, and which in my view undermines much of the analysis and utility of the study: that decision is to treat both gene expression and the identification of cis-regulatory regions at the level of individual genes, rather than transcriptional units. Below I will expand on why I find this problematic, how it might be addressed, and what other areas for improvement I see in the manuscript:

We thank the reviewer for their praise of our work. A careful set of replies to the major and minor critiques are reported below each point.

In the entire discussion from lines roughly 100-130, the authors frequently dissect out apparently differentially expressed genes from non differentially expressed genes within the same operons... I honestly wonder whether this is a useful distinction. I understand that by the criteria set forth by the authors it is technically correct, and yet, I wonder if this is more due to thresholding artifacts (i.e., some genes passing the authors' reasonable-yet-arbitrary thresholds whereas others in the same operon do not), and in the process causing a distraction from an operon that is in fact largely moving in the same direction. The authors might wish to either aggregate data in some way across known transcriptional units for the purposes of their analysis, and/or consider a more lenient 'rescue' set of significance thresholds for genes that are in the same operons as differentially expressed genes. I would favor the former approach, performing virtually all of their analysis at the level of transcriptional units rather than individual genes, as much of their analysis in any case relies upon proper assignment of genes to promoters, and this way they could focus on the most important signals rather than get lots sometimes in the weeds of looking at every single gene when really what they seem to be looking at in this paper is a property OF THE PROMOTERS, not the genes. (of course there are phenomena, such as rho dependent termination specifically titrating expression of late genes in operons, but I think on the balance the operon-level analysis might provide more insights and a cleaner analysis and discussion).

We agree with the reviewer that the peculiar nature of transcription in bacteria has to be taken into account in order to properly quantify the influence of cis variants in gene expression changes. We therefore added the exact analysis the reviewer suggested; that is, we ran associations between the variants in cis to the first gene of each operon and a phenotype that considered the fold-change of all genes in the operon, via a weighted average (see Methods for more details). As reported in the results section (L223), we found a similar trend as with the original analysis: we found the highest proportion of associations when encoding cis variants using k-mers (42% for E. coli and 45% for P. aeruginosa). More importantly, we found a high degree of overlap between this new “operon-level” association analysis and the original one (only including the first gene in each operon). We found a range of 90%-94% of associations overlapping for E. coli and between 75% and 91% for P. aeruginosa, depending on the variant type. We note that operon definitions are less precise for P. aeruginosa, which might explain the higher variability in the level of overlap. We have added the results of this analysis in the results section.

This also leads to a more general point, however, which I think is potentially more deeply problematic. At the end of the day, all of the analysis being done here centers on the cis regulatory logic upstream of each individual open reading frame, even though in many cases (i.e., genes after the first one in multi-gene operons), this is not where the relevant promoter is. This problem, in turn, raises potentially misattributions of causality running in both directions, where the causal impact on a bona fide promoter mutation on many genes in an operon may only be associated with the first gene, or on the other side, where a mutation that co-occurs with, but is causally independent from, an actual promoter mutation may be flagged as the one driving an expression change. This becomes an especially serious issue in cases like ulaE, for genes that are not the first gene in an operon (at least according to standard annotations, the UlaE transcript should be part of a polycistronic mRNA beginning from the ulaA promoter, and the role played by cis-regulatory logic immediately upstream of ulaE is uncertain and certainly merits deeper consideration. I suspect that many other similar cases likewise lurk in the dataset used here (perhaps even moreso for the Pseudomonas data, where the operon definitions are likely less robust). Of course there are many possible explanations, such as a separate ulaE promoter only in some strains, but this should perhaps be carefully stated and explored, and seems likely to be the exception rather than the rule.

While we again agree with the reviewer that some of our associations might not result in a direct causal link because the focal variant may not belong to an actual promoter element, we also want to point out how the ability to identify the composition of transcriptional units in bacteria is far from a solved problem (see references at the bottom of this comment, two in general terms, and one characterizing a specific example), even for a well-studied species such as E. coli. Therefore, even if carrying out associations at the operon level (e.g. by focusing exclusively on variants in cis for the first gene in the operon) might be theoretically correct, a number of the associations we find further down the putative operons might be the result of a true biological signal.

1. Conway, T., Creecy, J. P., Maddox, S. M., Grissom, J. E., Conkle, T. L., Shadid, T. M., Teramoto, J., San Miguel, P., Shimada, T., Ishihama, A., Mori, H., & Wanner, B. L. (2014). Unprecedented High-Resolution View of Bacterial Operon Architecture Revealed by RNA Sequencing. mBio, 5(4), 10.1128/mbio.01442-14. https://doi.org/10.1128/mbio.01442-14

2. Sáenz-Lahoya, S., Bitarte, N., García, B., Burgui, S., Vergara-Irigaray, M., Valle, J., Solano, C., Toledo-Arana, A., & Lasa, I. (2019). Noncontiguous operon is a genetic organization for coordinating bacterial gene expression. Proceedings of the National Academy of Sciences, 116(5), 1733–1738. https://doi.org/10.1073/pnas.1812746116

3. Zehentner, B., Scherer, S., & Neuhaus, K. (2023). Non-canonical transcriptional start sites in E. coli O157:H7 EDL933 are regulated and appear in surprisingly high numbers. BMC Microbiology, 23(1), 243. https://doi.org/10.1186/s12866-023-02988-6

Another issue with the current definition of regulatory regions, which should perhaps also be accounted for, is that it is likely that for many operons, the 'regulatory regions' of one gene might overlap the ORF of the previous gene, and in some cases actual coding mutations in an upstream gene may contaminate the set of potential regulatory mutations identified in this dataset.

We agree that defining regulatory regions might be challenging, and that those regions might overlap with coding regions, either for the focal gene or the one immediately upstream. For these reasons we have defined a wide region to identify putative regulatory variants (-200 to +30 bp around the start codon of the focal gene). We believe this relatively wide region allows us to capture the most cis genetic variation.

Taken together, I feel that all of the above concerns need to be addressed in some way. At the absolute barest minimum, the authors need to acknowledge the weaknesses that I have pointed out in the definition of cis-regulatory logic at a gene level. I think it would be far BETTER if they performed a re-analysis at the level of transcriptional units, which I think might substantially strengthen the work as a whole, but I recognize that this would also constitute a substantial amount of additional effort.

As indicated above, we have added a section in the results section to report on the analysis carried out at the level of operons as individual units, with more details provided in the methods section. We believe these results, which largely overlap with the original analysis, are a good way to recognize the limitation of our approach and to acknowledge the importance of gaining a better knowledge on the number and composition of transcriptional units in bacteria, for which, as the reference above indicates, we still have an incomplete understanding.

Having reached the end of the paper, and considering the evidence and arguments of the authors in their totality, I find myself wondering how much local x background interactions - that is, the effects of cis regulatory mutations (like those being considered here, with or without the modified definitions that I proposed above) IN THE CONTEXT OF A PARTICULAR STRAIN BACKGROUND, might matter more than the effects of the cis regulatory mutations per se. This is a particularly tricky problem to address because it would require a moderate number of targeted experiments with a moderate number of promoters in a moderate number of strains (which of course makes it maximally annoying since one can't simply scale up hugely on either axis individually and really expect to tease things out). I think that trying to address this question experimentally is FAR beyond the scope of the current paper, but I think perhaps the authors could at least begin to address it by acknowledging it as a challenge in their discussion section, and possibly even identify candidate promoters that might show the largest divergence of activities across strains when there IS no detectable cis regulatory mutation (which might be indicative of local x background interactions), or those with the largest divergences of effect for a given mutation across strains. A differential expression model incorporating shrinkage is essential in such analysis to avoid putting too much weight on low expression genes with a lot of Poisson noise.

We again thank the reviewer for their thoughtful comments on the limitations of correlative studies in general, and microbial GWAS in particular. In regards to microbial GWAS we feel we may have failed to properly explain how the implementation we have used allows to, at least partially, correct for population structure effects. That is, the linear mixed model we have used relies on population structure to remove the part of the association signal that is due to the genetic background and thus focus the analysis on the specific loci. Obviously examples in which strong epistatic interactions are present would not be accounted for, but those would be extremely challenging to measure or predict at scale, as the reviewer rightfully suggests. We have added a brief recap of the ability of microbial GWAS to account for population structure in the results section (“A large fraction of gene expression changes can be attributed to genetic variations in cis regulatory regions”, e.g. L195).

I also have some more minor concerns and suggestions, which I outline below:

It seems that the differential expression analysis treats the lab reference strains as the 'centerpoint' against which everything else is compared, and yet I wonder if this is the best approach... it might be interesting to see how the results differ if the authors instead take a more 'average' strain (either chosen based on genetics or transcriptomics) as a reference and compared everything else to that.

While we don’t necessarily disagree with the reviewer that a “wild” strain would be better to compare against, we think that our choice to go for the reference isolates is still justified on two grounds. First, while it is true that comparing against a reference introduces biases in the analysis, this concern would not be removed had we chosen another strain as reference; which strain would then be best as a reference to compare against? We think that the second point provides an answer to this question; the “traditional” reference isolates have a rich ecosystem of annotations, experimental data, and computational predictions. These can in turn be used for validation and hypothesis generation, which we have done extensively in the manuscript. Had we chosen a different reference isolate we would have had to still map associations to the traditional reference, resulting in a probable reduction in precision. An example that will likely resonate with this reviewer is that we have used experimentally-validated and high quality computational operon predictions to look into likely associations between cis-variants and “operon DEGs”. This analysis would have likely been of worse quality had we used another strain as reference, for which operon definitions would have had to come from lower-quality predictions or be “lifted” from the traditional reference.

Line 104 - the statement about the differentially expressed genes being "part of operons with diverse biological functions" seems unclear - it is not apparent whether the authors are referring to diversity of function within each operon, or between the different operons, and in any case one should consider whether the observation reflects any useful information or is just an apparently random collection of operons.

We agree that this formulation could create confusion and we have elected to remove the expression “with diverse biological functions”, given that we discuss those functions immediately after that sentence.

Line 292 - I find the argument here somewhat unconvincing, for two reasons. First, the fact that only half of the observed changes went in the same direction as the GWAS results would indicate, which is trivially a result that would be expected by random chance, does not lend much confidence to the overall premise of the study that there are meaningful cis regulatory changes being detected (in fact, it seems to argue that the background in which a variant occurs may matter a great deal, at least as much as the cis regulatory logic itself). Second, in order to even assess whether the GWAS is useful to "find the genetic determinants of gene expression changes" as the authors indicate, it would be necessary to compare to a reasonable, non-straw-man, null approach simply identifying common sequence variants that are predicted to cause major changes in sigma 70 binding at known promoters; such a test would be especially important given the lack of directional accuracy observed here. Along these same lines, it is perhaps worth noting, in the discussion beginning on line 329, that the comparison is perhaps biased in favor of the GWAS study, since the validation targets here were prioritized based on (presumably strong) GWAS data.

We thank the reviewer for prompting us into reasoning about the results of the in-vitro validation experiments. We agree that the agreement between the measured gene expression changes agree only partly with those measured with the reporter system, and that this discrepancy could likely be attributed to regulatory elements that are not in cis, and thus that were not present in the in-vitro reporter system. We have noted this possibility in the discussion. Additionally, we have amended the results section to note that even though the prediction in the direction of gene expression change was not as accurate as it could be expected, the prediction of whether a change would be present (thus ignoring directionality) was much higher.

I don't find the Venn diagrams in Fig 7C-D useful or clear given the large number of zero-overlap regions, and would strongly advocate that the authors find another way to show these data.

While we are aware that alternative ways to show overlap between sets, such as upset plots, we don’t actually find them that much easier to parse. We actually think that the simple and direct Venn diagrams we have drawn convey the clear message that overlaps only exist between certain drug classes in E. coli, and virtually none for P. aeruginosa. We have added a comment on the lack of overlap between all drug classes and the differences between the two species in the results section (i.e. L436 and L465).

In the analysis of waa operon gene expression beginning on line 400, it is perhaps important to note that most of the waa operon doesn't do anything in laboratory K12 strains due to the lack of complete O-antigen... the same is not true, however, for many wild/clinical isolates. It would be interesting to see how those results compare, and also how the absolute TPMs (rather than just LFCs) of genes in this operon vary across the strains being investigated during TOB treatment.

We thank the reviewer for this helpful suggestion. We examined the absolute expression (TPMs) of waa operon genes under the baseline (A) and following exposure to Tobramycin (B). The representative TPMs per strain were obtained by averaging across biological replicates. We observed a constitutive expression of the genes in the reference strain (MG1655) and the other isolates containing the variant of interest (MC4100, BW25113). In contrast, strains lacking the variants of interest (IAI76 and IAI78), showed lower expression of these operon genes under both conditions. Strain IAI77, on the other hand, displayed increased expression of a subset of waa genes post Tobramycin exposure, indicating strain-specific variation in transcriptional response. While the reference isolate might not have the O-antigen, it certainly expresses the waa operon, both constitutively and under TOB exposure.

I don't think that the second conclusion on lines 479-480 is fully justified by the data, given both the disparity in available annotation information between the two species, AND the fact that only two species were considered.

While we feel that the “Discussion” section of a research paper allows for speculative statements, we have to concede that we have perhaps overreached here. We have amended this sentence to be more cautious and not mislead readers.

Line 118: "Double of DEGs"

Line 288 - presumably these are LOG fold changes

Fig 6b - legend contains typos

Line 661 - please report the read count (more relevant for RNA-seq analysis) rather than Gb

We thank the reviewer for pointing out the need to make these edits. We have implemented them all.

Source code - I appreciate that the authors provide their source code on github, but it is very poorly documented - both a license and some top-level documentation about which code goes with each major operation/conclusion/figure should be provided. Also, ipython notebooks are in general a poor way in my view to distribute code, due to their encouragement of nonlinear development practices; while they are fine for software development, actual complete python programs along with accompanying source data would be preferrable.

We agree with the reviewer that a software license and some documentation about what each notebook is about is warranted, and we have added them both. While we agree that for “consumer-grade” software jupyter notebooks are not the most ergonomic format, we believe that as a documentation of how one-time analyses were carried out they are actually one of the best formats we could think of. They in fact allow for code and outputs to be presented alongside each other, which greatly helped us to iterate on our research and to ensure that what was presented in the manuscript matched the analyses we reported in the code. This is of course up for debate and ultimately specific to someone’s taste, and so we will keep the reviewer’s critique in mind for our next manuscript. And, if we ever decide to package the analyses presented in the manuscript as a “consumer-grade” application for others to use, we would follow higher standards of documentation and design.

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

In this manuscript, Damaris et al. collected genome sequences and transcriptomes from isolates from two bacterial species. Data for E. coli were produced for this paper, while data for P. aeruginosa had been measured earlier. The authors integrated these data to detect genes with differential expression (DE) among isolates as well as cis-expression quantitative trait loci (cis-eQTLs). The authors used sample sizes that were adequate for an initial exploration of gene regulatory variation (n=117 for E. coli and n=413 for P. aeruginosa) and were able to discover cis eQTLs at about 39% of genes. In a creative addition, the authors compared their results to transcription rates predicted from a biophysical promoter model as well as to annotated transcription factor binding sites. They also attempted to validate some of their associations experimentally using GFP-reporter assays. Finally, the paper presents a mapping of antibiotic resistance traits. Many of the detected associations for this important trait group were in non-coding genome regions, suggesting a role of regulatory variation in antibiotic resistance.

A major strength of the paper is that it covers an impressive range of distinct analyses, some of which in two different species. Weaknesses include the fact that this breadth comes at the expense of depth and detail. Some sections are underdeveloped, not fully explained and/or thought-through enough. Important methodological details are missing, as detailed below.

We thank the reviewer for highlighting the strengths of our study. We hope that our replies to their comments and the other two reviewers will address some of the limitations.

Major comments:

1. An interesting aspect of the paper is that genetic variation is represented in different ways (SNPs & indels, IRG presence/absence, and k-mers). However, it is not entirely clear how these three different encodings relate to each other. Specifically, more information should be given on these two points:

2. it is not clear how "presence/absence of intergenic regions" are different from larger indels.

In order to better guide readers through the different kinds of genetic variants we considered, we have added a brief explanation about what “promoter switches” are in the introduction (“meaning that the entire promoter region may differ between isolates due to recombination events”, L56). We believe this clarifies how they are very different in character from a large deletion. We have kept the reference to the original study (10.1073/pnas.1413272111) describing how widespread these switches are in E. coli as a way for readers to discover more about them.

• I recommend providing more narration on how the k-mers compare to the more traditional genetic variants (SNPs and indels). It seems like the k-mers include the SNPs and indels somehow? More explanation would be good here, as k-mer based mapping is not usually done in other species and is not standard practice in the field. Likewise, how is multiple testing handled for association mapping with k-mers, since presumably each gene region harbors a large number of k-mers, potentially hugely increasing the multiple testing burden?

We indeed agree with the reviewer in thinking that representing genetic variants as k-mers would encompass short variants (SNP/InDels) as well as larger variants and promoters presence/absence patterns. We believe that this assumption is validated by the fact that we identify the highest proportion of DEGs with a significant association when using this representation of variants (Figure 2A, 39% for both species). We have added a reference to a recent review on the advantages of k-mer methods for population genetics (10.1093/molbev/msaf047) in the introduction. Regarding the issue of multiple testing correction, we have employed a commonly recognized approach that, unlike a crude Bonferroni correction using the number of tested variants, allows for a realistic correction of association p-values. We used the number of unique presence/absence patterns, which can be shared between multiple genetic variants, and applied a Bonferroni correction using this number rather than the number of variants tested. We have expanded the corresponding section in the methods (e.g. L697) to better explain this point for readers not familiar with this approach.

1. What was the distribution of association effect sizes for the three types of variants? Did IRGs have larger effects than SNPs as may be expected if they are indeed larger events that involve more DNA differences? What were their relative allele frequencies?

We appreciate the suggestion made by the reviewer to look into the distribution of effect sizes divided by variant type. We have now evaluated the distribution of the effect sizes and allele frequencies for the genetic markers (SNPs/InDels, IGRs, and k-mers) for both species (Supplementary Figure 2). In E. coli, IGR variants showed somewhat larger median effect sizes (|β| = 4.5) than SNPs (|β| = 3.8), whereas k-mers displayed the widest distribution (median |β| = 5.2). In P. aeruginosa, the trend differed with IGRs exhibiting smaller effects (median |β| = 3.2), compared to SNPs/InDels (median |β| =5.1) and k-mers (median |β| = 6.2). With respect to allele frequencies, SNPs/InDels generally occured at lower frequencies (median AF = 0.34 for E.coli, median AF = 0.33 for P. aeruginosa), whereas IGRs (median AF = 0.65 for E. coli and 0.75 for P. aeruginosa) and k-mers (median AF = 0.71 for E. coli and 0.65 for P. aeruginosa) were more often at the intermediate to higher frequencies respectively. We have added a visualization for the distribution of effect sizes (Supplementary Figure 2).

1. The GFP-based experiments attempting to validate the promoter effects for 18 genes are laudable, and the fact that 16 of them showed differences is nice. However, the fact that half of the validation attempts yielded effects in the opposite direction of what was expected is quite alarming. I am not sure this really "further validates" the GWAS in the way the authors state in line 292 - in fact, quite the opposite in that the validations appear random with regards to what was predicted from the computational analyses. How do the authors interpret this result? Given the higher concordance between GWAS, promoter prediction, and DE, are the GFP assays just not relevant for what is going on in the genome? If not, what are these assays missing? Overall, more interpretation of this result would be helpful.

We thanks the reviewer for their comment, which is similar in nature to that raised by reviewer #2 above. As noted in our reply above we have amended the results and discussion to indicate that although the direction of gene expression change was not highly accurate, focusing on the magnitude (or rather whether there would be a change in gene expression, regardless of the direction), resulted in a higher accuracy. We postulate that the cases in which the direction of the change was not correctly identified could be due to the influence of other genetic elements in trans with the gene of interest.

1. On the same note, it would be really interesting to expand the GFP experiments to promoters that did not show association in the GWAS. Based on Figure 6, effects of promoter differences on GFP reporters seem to be very common (all but three were significant). Is this a higher rate than for the average promoter with sequence variation but without detected association? A handful of extra reporter experiments might address this. My larger question here is: what is the null expectation for how much functional promoter variation there is?

We thank the reviewer for this comment. We agree that estimating the null expectation for the functional promoter would require testing promoter alleles with sequence variation that are not associated in the GWAS. Such experiments, which would directly address if the observed effects in our study exceeds background, would have required us to prepare multiple constructs, which was unfortunately not possible for us due to staff constraints. We therefore elected to clarify the scope of our GFP reporter assays instead. These experiments were designed as a paired comparison of the wild-type and the GWAS-associated variant alleles of the same promoter in an identical reporter background, with the aim of testing allele-specific functional effects for GWAS hits (Supplementary Figure 6). We also included a comparison in GFP fluorescence between the promoterless vector (pOT2) and promoter-containing constructs; we observed higher GFP signals in all but four (yfgJ, fimI, agaI, and yfdQ) variant-containing promoter constructs, which indicates that for most of the construct we cloned active promoter elements. We have revised the manuscript text accordingly to reflect this clarification and included the control in the supplementary information as Supplementary Figure 6.

1. Were the fold-changes in the GFP experiments statistically significant? Based on Figure 6 it certainly looks like they are, but this should be spelled out, along with the test used.

We thank the reviewer for pointing this out. We have reviewed Figure 6 to indicate significant differences between the test and control reporter constructs. We used the paired student’s t-test to match the matched plate/time point measurements. We also corrected for multiple testing using the Benhamini-Hochberg correction. As seen in the updated Figure 6A, 16 out of the 18 reporter constructs displayed significant differences (adjusted p-value

1. What was the overall correlation between GWAS-based fold changes and those from the GFP-based validation? What does Figure 6A look like as a scatter plot comparing these two sets of values?

We thank the reviewer for this helpful suggestion, which allows us to more closely look into the results of our in-vitro validation. We performed a direct comparison of RNAseq fold changes from the GWAS (x-axis) with the GFP reporter measurements (y-axis) as depicted in the figure above. The overall correlation between the two was weak (Pearson r = 0.17), reflecting the lack of thorough agreement between the associations and the reporter construct. We however note that the two metrics are not directly comparable in our opinion, since on the x-axis we are measuring changes in gene expression and on the y-axis changes in fluorescence expression, which is downstream from it. As mentioned above and in reply to a comment from reviewer 2, the agreement between measured gene expression and all other in-silico and in-vitro techniques increases when ignoring the direction of the change. Overall, we believe that these results partly validate our associations and predictions, while indicating that other factors in trans with the regulatory region contribute to changes in gene expression, which is to be expected. The scatter plot has been included as a new supplementary figure (Supplementary Figure 7).

1. Was the SNP analyzed in the last Results section significant in the gene expression GWAS? Did the DE results reported in this final section correspond to that GWAS in some way?

The T>C SNP upstream of waaQ did not show significant association with gene expression in our cis GWAS analysis. Instead, this variant was associated with resistance to tobramycin when referencing data from Danesh et al, and we observed the variant in our strain collection. We subsequently investigated whether this variant also influenced expression of the waa operon under sub-inhibitory tobramycin exposure. The differential expression results shown in the final section therefore represent a functional follow-up experiment, and not a direct replication of the GWAS presented in the first part of the manuscript.

1. Line 470: "Consistent with the differences in the genetic structure of the two species" It is not clear what differences in genetic structure this refers to. Population structure? Genome architecture? Differences in the biology of regulatory regions?

The awkwardness of that sentence is perhaps the consequence of our assumption that readers would be aware of the differences in population genetics differences between the two species. We however have realized that not much literature is available (if at all!) about these differences, which we have observed during the course of this and other studies we have carried out. As a result, we agree that we cannot assume that the reader is similarly familiar with these differences, and have changed that sentence (i.e. L548) to more directly address the differences between the two species, which will presumably result in a diverse population structure. We thank the reviewer for letting us be aware of a gap in the literature concerning the comparison of pangenome structures across relevant species.

1. Line 480: the reference to "adaption" is not warranted, as the paper contains no analyses of evolutionary patterns or processes. Genetic variation is not the same as adaptation.

We have amended this sentence to be more adherent to what we can conclude from our analyses.

1. There is insufficient information on how the E. coli RNA-seq data was generated. How was RNA extracted? Which QC was done on the RNA; what was its quality? Which library kits were used? Which sequencing technology? How many reads? What QC was done on the RNA-seq data? For this section, the Methods are seriously deficient in their current form and need to be greatly expanded.

We thank the reviewer for highlighting the need for clearer methodological detail. We have expanded this section (i.e. L608) to fully describe the generation and quality control of the E. coli RNA-seq data including RNA extraction and sequencing platform.

1. How were the DEG p-values adjusted for multiple testing?

As indicated in the methods section (“Differential gene expression and functional enrichment analysis”), we have used DEseq2 for E. coli, and LPEseq for P. aeruginosa. Both methods use the statistical framework of the False Discovery Rate (FDR) to compute an adjusted p-value for each gene. We have added a brief mention of us following the standard practice indicated by both software packages in the methods.

1. Were there replicates for the E. coli strains? The methods do not say, but there is a hint there might have been replicates given their absence was noted for the other species.

In the context of providing more information about the transcriptomics experiments for E. coli, we have also more clearly indicated that we have two biological replicates for the E. coli dataset.

1. There needs to be more information on the "pattern-based method" that was used to correct the GWAS for multiple tests. How does this method work? What genome-wide threshold did it end up producing? Was there adjustment for the number of genes tested in addition to the number of variants? Was the correction done per variant class or across all variant classes?

In line with an earlier comment from this reviewer, we have expanded the section in the Methods (e.g. L689) that explains how this correction worked to include as many details as possible, in order to provide the readers with the full context under which our analyses were carried out.

1. For a paper that, at its core, performs a cis-eQTL mapping, it is an oversight that there seems not to be a single reference to the rich literature in this space, comprising hundreds of papers, in other species ranging from humans, many other animals, to yeast and plants.

We thank both reviewer #1 and #3 for pointing out this lack of references to the extensive literature on the subject. We have added a number of references about the applications of eQTL studies, and specifically its application in microbial pangenomes, which we believe is more relevant to our study, in the introduction.

Minor comments:

1. I wasn't able to understand the top panels in Figure 4. For ulaE, most strains have the solid colors, and the corresponding bottom panel shows mostly red points. But for waaQ, most strains have solid color in the top panel, but only a few strains in the bottom panel are red. So solid color in the top does not indicate a variant allele? And why are there so many solid alleles; are these all indels? Even if so, for kgtP, the same colors (i.e., nucleotides) seem to seamlessly continue into the bottom, pale part of the top panel. How are these strains different genotypically? Are these blocks of solid color counted as one indel or several SNPs, or somehow as k-mer differences? As the authors can see, these figures are really hard to understand and should be reworked. The same comment applies to Figure 5, where it seems that all (!) strains have the "variant"?

We thank the reviewer for pointing out some limitations with our visualizations, most importantly with the way we explained how to read those two figures. We have amended the captions to more explicitly explain what is shown. The solid colors in the “sequence pseudo-alignment” panels indicate the focal cis variant, which is indicated in red in the corresponding “predicted transcription rate” panels below. In the case of Figure 5, the solid color indicates instead the position of the TFBS in the reference.

1. Figure 1A & B: It would be helpful to add the total number of analyzed genes somewhere so that the numbers denoted in the colored outer rings can be interpreted in comparison to the total.

We have added the total number of genes being considered for either species in the legend.

1. Figure 1C & D: It would be better to spell out the COG names in the figure, as it is cumbersome for the reader to have to look up what the letters stand for in a supplementary table in a separate file.

While we do not disagree with the awkwardness of having to move to a supplementary table to identify the full name of a COG category, we also would like to point out that the very long names of each category would clutter the figure to a degree that would make it difficult to read. We had indeed attempted something similar to what the reviewer suggests in early drafts of this manuscript, leading to small and hard to read labels. We have therefore left the full names of each COG category in Supplementary Table 3.

1. Line 107: "Similarly," does not fit here as the following example (with one differentially expressed gene in an operon) is conceptually different from the one before, where all genes in the operon were differentially expressed.

We agree and have amended the sentence accordingly.

1. Figure 5 bottom panel: it is odd that on the left the swarm plots (i.e., the dots) are on the inside of the boxplots while on the right they are on the outside.

We have fixed the position of the dots so that they are centered with respect to the underlying boxplots.

1. It is not clear to me how only one or a few genes in an operon can show differential mRNA abundance. Aren't all genes in an operon encoded by the same mRNA? If so, shouldn't this mRNA be up- or downregulated in the same manner for all genes it encodes? As I am not closely familiar with bacterial systems, it is well possible that I am missing some critical fact about bacterial gene expression here. If this is not an analysis artifact, the authors could briefly explain how this observation is possible.

We thanks the reviewer for their comment, which again echoes one of the main concerns from reviewer #2. As noted in our reply above, it has been established in multiple studies (see the three we have indicated above in our reply to reviewer #2) how bacteria encode for multiple “non-canonical” transcriptional units (i.e. operons), due to the presence of accessory terminators and promoters. This, together with other biological effects such as the presence of mRNA molecules of different lengths due to active transcription and degradation and technical noise induced by RNA isolation and sequencing can result in variability in the estimation of abundance for each gene.

Author response:

The following is the authors’ response to the original reviews.

eLife Assessment

This work provides an important resource identifying 72 proteins as novel candidates for plasma membrane and/or cell wall damage repair in budding yeast, and describes the temporal coordination of exocytosis and endocytosis during the repair process. The data are convincing; however, additional experimental validation will better support the claim that repair proteins shuttle between the bud tip and the damage site.

We thank the editors and reviewers for their positive assessment of our work and the constructive feedback to improve our manuscript. We agree with the assessment that additional validation of repair protein shuttling between the bud tip and the damage site is required to further support the model.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Yamazaki et al. conducted multiple microscopy-based GFP localization screens, from which they identified proteins that are associated with PM/cell wall damage stress response. Specifically, the authors identified that budlocalized TMD-containing proteins and endocytotic proteins are associated with PM damage stress. The authors further demonstrated that polarized exocytosis and CME are temporally coupled in response to PM damage, and CME is required for polarized exocytosis and the targeting of TMD-containing proteins to the damage site. From these results, the authors proposed a model that CME delivers TMD-containing repair proteins between the bud tip and the damage site.

Strengths:

Overall, this is a well-written manuscript, and the experiments are well-conducted. The authors identified many repair proteins and revealed the temporal coordination of different categories of repair proteins. Furthermore, the authors demonstrated that CME is required for targeting of repair proteins to the damage site, as well as cellular survival in response to stress related to PM/cell wall damage. Although the roles of CME and bud-localized proteins in damage repair are not completely new to the field, this work does have conceptual advances by identifying novel repair proteins and proposing the intriguing model that the repairing cargoes are shuttled between the bud tip and the damaged site through coupled exocytosis and endocytosis.

Weaknesses:

While the results presented in this manuscript are convincing, they might not be sufficient to support some of the authors' claims. Especially in the last two result sessions, the authors claimed CME delivers TMD-containing repair proteins from the bud tip to the damage site. The model is no doubt highly possible based on the data, but caveats still exist. For example, the repair proteins might not be transported from one localization to another localization, but are degraded and resynthesized. Although the Gal-induced expression system can further support the model to some extent, I think more direct verification (such as FLIP or photo-convertible fluorescence tags to distinguish between pre-existing and newly synthesized proteins) would significantly improve the strength of evidence.

Major experiment suggestions:

(1) The authors may want to provide more direct evidence for "protein shuttling" and for excluding the possibility that proteins at the bud are degraded and synthesized de novo near the damage site. For example, if the authors could use FLIP to bleach budlocalized fluorescent proteins, and the damaged site does not show fluorescent proteins upon laser damage, this will strongly support the authors' model. Alternatively, the authors could use photo-convertible tags (e.g., Dendra) to differentiate between preexisting repair proteins and newly synthesized proteins.

We thank the reviewer for evaluating our work and giving us important feedback. We agree that the FLIP and photo-convertible experiments will further confirm our model. Here, due to time and resource constraints, we decided not to perform this experiment. Instead, we have discussed this limitation in 363-366. Our proposed model of repair protein shuttling should be further tested in our future work.

(2) In line with point 1, the authors used Gal-inducible expression, which supported their model. However, the author may need to show protein abundance in galactose, glucose, and upon PM damage. Western blot would be ideal to show the level of fulllength proteins, or whole-cell fluorescence quantification can also roughly indicate the protein abundance. Otherwise, we cannot assume that the tagged proteins are only expressed when they are growing in galactose-containing media.

Thank you very much for raising the concern and suggesting the important experiments.We agree that the Western blot experiment to confirm the mNG-Snc1 expression in each medium will further strengthen our conclusion. Along with point (1), further investigation of repair protein shuttling between the bud tip and the damage site and the mechanisms underlying it will be an important future direction. As described above, we have discussed this limitation in 363-366.

(3) Similarly, for Myo2 and Exo70 localization in CME mutants (Figure 4), it might be worth doing a western or whole-cell fluorescence quantification to exclude the caveat that CME deficiency might affect protein abundance or synthesis.

We thank the reviewer for suggesting the point. Following the reviewer’s suggestion, we quantified the whole-cell fluorescence of WT and CME mutants and verified that the effect of the CME deletion on the expression levels of Myo2-sfGFP and Exo70-mNG is minimal ( Figure S6). We added the description in lines 211-212.

(4) From the authors' model in Figure 7, it looks like the repair proteins contribute to bud growth. Does laser damage to the mother cell prevent bud growth due to the reduction of TMD-containing repair proteins at the bud? If the authors could provide evidence for that, it would further support the model.

Thank you very much for raising the important point. We speculate that the reduction of TMD-containing proteins at the bud by CME is one of the causes of cell growth arrest after PM damage (1). This is because TMD-containing repair proteins at the bud tip, including phospholipid flippases (Dnf1/Dnf2), Snc1, and Dfg5, are involved in polarized cell growth (2-4). This will be an important future direction as well.

(5) Is the PM repair cell-cycle-dependent? For example, would the recruitment of repair proteins to the damage site be impaired when the cells are under alpha-factor arrest?

Thank you for raising this interesting point. Indeed, the senior author Kono previously performed this experiment when she was in David Pellman’s lab. The preliminary results suggest that Pkc1 can be targeted to the damage site, without any impairment, under alpha-factor arrest. A more comprehensive analysis in the future will contribute to concluding the relation between PM repair and the cell cycle.

Reviewer #2 (Public review):

This paper remarkably reveals the identification of plasma membrane repair proteins, revealing spatiotemporal cellular responses to plasma membrane damage. The study highlights a combination of sodium dodecyl sulfate (SDS) and lase for identifying and characterizing proteins involved in plasma membrane (PM) repair in Saccharomyces cerevisiae. From 80 PM, repair proteins that were identified, 72 of them were novel proteins. The use of both proteomic and microscopy approaches provided a spatiotemporal coordination of exocytosis and clathrin-mediated endocytosis (CME) during repair. Interestingly, the authors were able to demonstrate that exocytosis dominates early and CME later, with CME also playing an essential role in trafficking transmembrane-domain (TMD)containing repair proteins between the bud tip and the damage site.

Weaknesses/limitations:

(1) Why are the authors saying that Pkc1 is the best characterized repair protein? What is the evidence?

We would like to thank the reviewer for taking his/her time to evaluate our work and for valuable suggestions. We described Pkc1 as “best characterized” because it was the first protein reported to accumulate at the laser damage site in budding yeast (5). However, as the reviewer suggested, we do not have enough evidence to describe Pkc1 as “best characterized”. We therefore used “one of the known repair proteins” to mention Pkc1 in the manuscript (lines 90-91).

(2) It is unclear why the authors decided on the C-terminal GFP-tagged library to continue with the laser damage assay, exclusively the C-terminal GFP-tagged library. Potentially, this could have missed N-terminal tag-dependent localizations and functions and may have excluded functionally important repair proteins

Thank you very much for the comments. We decided to use the C-terminal GFP-tagged library for the laser damage assay because we intended to evaluate the proteins of endogenous expression levels. The N-terminal sfGFP-tagged library is expressed by the NOP1 promoter, while the C-terminal GFP-tagged library is expressed by the endogenous promoters. We clarified these points in lines 114-118. We agree with the reviewer on that we may have missed some portion of repair proteins in the N-terminaldependent localization and functions by this approach. Therefore, in our manuscript, we discussed these limitations in lines 281-289.

(3) The use of SDS and laser damage may bias toward proteins responsive to these specific stresses, potentially missing proteins involved in other forms of plasma membrane injuries, such as mechanical, osmotic, etc.). SDS stress is known to indirectly induce oxidative stress and heat-shock responses.

Thank you very much for raising this point. We agree that the combination of SDS and laser may be biased to identify PM repair proteins. Therefore, in the manuscript, we discussed this point as a limitation of this work in lines 292-298.

(4) It is unclear what the scale bars of Figures 3, 5, and 6 are. These should be included in the figure legend.

We apologize for the missing scale bars. We added them to the legends of the figures in the manuscript.

(5) Figure 4 should be organized to compare WT vs. mutant, which would emphasize the magnitude of impairment.

Thank you for raising this point. Following the suggestion, we updated Figure 4. In the Figure 4, we compared WT vs mutant in the manuscript. We clarified it in the legends in the manuscript. 

(6) It would be interesting to expand on possible mechanisms for CME-mediated sorting and retargeting of TMD proteins, including a speculative model.

Thank you very much for this important suggestion. We think it will be very important to characterize the mechanism of CME-mediated TMD protein trafficking between the bud tip and the damage site. In the manuscript, we discussed the possible mechanism for CME activation at the damage site in lines 328-333. We speculate that the activation of the CME may facilitate the retargeting of the TMD proteins from the damage site to the bud tip.

We do not have a model of how CMEs activate at the bud tip to sort and target the TMD proteins to the damage site. One possibility is that the cell cycle arrest after PM damage (1) may affect the localization of CME proteins because the cell cycle affects the localization of some of the CME proteins (6). We will work on the mechanism of repair protein sorting from the bud tip to the damage site in our future work.

Reviewer #3 (Public review):

Summary:

This work aims to understand how cells repair damage to the plasma membrane (PM). This is important, as failure to do so will result in cell lysis and death. Therefore, this is an important fundamental question with broad implications for all eukaryotic cells. Despite this importance, there are relatively few proteins known to contribute to this repair process. This study expands the number of experimentally validated PM from 8 to 80. Further, they use precise laser-induced damage of the PM/cell wall and use livecell imaging to track the recruitment of repair proteins to these damage sites. They focus on repair proteins that are involved in either exocytosis or clathrin-mediated endocytosis (CME) to understand how these membrane remodeling processes contribute to PM repair. Through these experiments, they find that while exocytosis and CME both occur at the sites of PM damage, exocytosis predominates in the early stages of repairs, while CME predominates in the later stages of repairs. Lastly, they propose that CME is responsible for diverting repair proteins localized to the growing bud cell to the site of PM damage.

Strengths:

The manuscript is very well written, and the experiments presented flow logically. The use of laser-induced damage and live-cell imaging to validate the proteome-wide screen using SDS-induced damage strengthens the role of the identified candidates in PM/cell wall repair.

Weaknesses:

(1) Could the authors estimate the fraction of their candidates that are associated with cell wall repair versus plasma membrane repair? Understanding how many of these proteins may be associated with the repair of the cell wall or PM may be useful for thinking about how these results are relevant to systems that do or do not have a cell wall. Perhaps this is already in their GO analysis, but I don't see it mentioned in the manuscript.

We would like to thank the reviewer for taking his/her time to evaluate our work and valuable suggestions. We agree that this is important information to include. Although it may be difficult to completely distinguish the PM repair and cell wall repair proteins, we have identified at least six proteins involved in cell wall synthesis (Flc1, Dfg5, Smi1, Skg1, Tos7, and Chs3). We included this information in lines 142-146 in the manuscript.

(2) Do the authors identify actin cable-associated proteins or formin regulators associated with sites of PM damage? Prior work from the senior author (reference 26) shows that the formin Bnr1 relocalizes to sites of PM damage, so it would be interesting if Bnr1 and its regulators (e.g., Bud14, Smy1, etc) are recruited to these sites as well. These may play a role in directing PM repair proteins (see more below).

Thank you for the suggestion. We identified several Bnr1-interacting proteins, including Bud6, Bil1, and Smy1 (Table S2), although Bnr1 itself was not identified in our screening. This could be attributed to the fact that (1) C-terminal GFP fusion impaired the function of Bnr1, and (2) a single GFP fusion is not sufficient to visualize the weak signal at the damage site. Indeed, in reference 26, 3GFP-Bnr1 (N-terminal 3xGFP fusion) was used.

(3) Do the authors suspect that actin cables play a role in the relocalization of material from the bud tip to PM damage sites? They mention that TMD proteins are secretory vesicle cargo (lines 134-143) and that Myo2 localizes to damage sites. Together, this suggests a possible role for cable-based transport of repair proteins. While this may be the focus of future work, some additional discussion of the role of cables would strengthen their proposed mechanism (steps 3 and 4 in Figure 7).

Thank you very much for the suggestion. We agree that actin cables may play a role in the targeting of vesicles and repair proteins to the damage site. Following the reviewer’s suggestion, we discussed the roles of Bnr1 and actin cables for repair protein trafficking in lines 309-313 in the manuscript.

(4) Lines 248-249: I find the rationale for using an inducible Gal promoter here unclear. Some clarification is needed.

Thank you for raising this point. We clarified this as possible as we could in lines 249255 in the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The N-terminal GFP collection screen is interesting but seems irrelevant to the rest of the results. The authors discussed that in the discussion part, but it might be worth showing how many hits from the laser damage screen (in Figure 2) overlap with the Nterminal GFP screen hits.

Thank you for the suggestion. We found that 48 out of 80 repair proteins are hits in the N-terminal GFP library (Table S1 and S2). This result suggested that the N-terminal library is also a useful resource for identifying repair proteins. In the manuscript, we discussed it in lines 288-289.

(2) SDS treatment seems a harsh stressor. As the authors mentioned, the overlapped hits from the N- and C-terminal GFP screen might be more general stress factors. Thus, I think Line 84 (the subtitle) might be overclaiming, and the authors might need to tone down the sentence.

Thank you for the suggestion. Following the reviewer’s suggestion, we changed the sentence to “Proteome-scale identification of SDS-responsive proteins” in the manuscript. We believe that the new sentence describes our findings more precisely.

(3) Line 103-106, it does not seem obvious to me that the protein puncta in the cytoplasm are due to endocytosis. The authors might need to provide more experimental evidence for the conclusion, or at least provide more reasoning/references on that aspect (e.g.,several specific protein hits belonging to that group have been shown to be endocytosed).

Thank you very much for raising this point. We agree with the reviewer and deleted the description that these puncta are due to endocytosis in the manuscript.

(4) For Figure 1D and S1C, the authors annotated some of the localization changes clearly, but some are confusing to me. For example," from bud tip/neck" to where? And from where to "Puncta/foci"? A clearer annotation might help the readers to understand the categorization.

Thank you very much for the suggestion. These annotations were defined because it is difficult to conclusively describe the protein localization after SDS treatment. To convincingly identify the destination of the GFP fusion proteins, the dual color imaging of proteins with organelle markers or deep learning-based localization estimation is required. We feel that this might be out of the scope of this work. Therefore, as criteria, we used the localization of protein localization in normal/non-stressed conditions reported in (7) and the Saccharomyces Genome Database (SGD). We clarified this annotation definition in the manuscript (lines 413-436).

(5) For localization in Figure 2C, as I understand, does it refer to6 the "before damage/normal" localization? If so, I think it would be helpful to state that these localizations are based on the untreated/normal conditions in the text.

Yes, it refers to the “before damage/normal localization”. Following the reviewer’s suggestion, we stated that these localizations are based on these conditions in the manuscript (line 130).

(6) The authors mentioned "four classes" in Line 120, but did not mention the "PM to cytoplasm" class in the text. It would be helpful to discuss/speculate why these transporters might contribute to PM damage repair.

Thank you very much for this suggestion. We speculated that these transporters are endocytosed after PM damage because endocytosis of PM proteins contributes to cell adaptation to environmental stress (8). We mentioned it in the manuscript (lines 120-122).

(7) Line 175-180 My understanding of the text is that the signals of Exo70-mNG/Dnf1mNG peak before the Ede1-mSc-I peaks. They occur simultaneously, but their dominating phase are different. It is clearer when looking at the data, but I think the conclusion sentences themselves are confusing to me. The authors might consider rewriting the sentences to make them more straightforward.

Thank you very much for pointing this out. Following the reviewer’s suggestion, we revised the sentence (lines 177-182 in the manuscript).

Reviewer #2 (Recommendations for the authors):

It would be interesting to expand on the functional characterization of the 72 novel candidates and explore possible mechanisms for CME-mediated sorting and retargeting of TMD proteins by including a speculative model.

Thank you very much for the comment. We agree that the further characterization of novel repair proteins and exploration of the possible mechanisms for CME-mediated TMD protein sorting and retargeting are truly important. This should be our important future direction.

Reviewer #3 (Recommendations for the authors):

The x-axis in Figure 1C is labeled 'Ratio' - what is this a ratio of?

Thank you for raising this point. It is the ratio of the number of proteins associated with a GO term to the total number of proteins in the background. We clarified it in the legend of Figure 1C in the manuscript.

References

(1) K. Kono, A. Al-Zain, L. Schroeder, M. Nakanishi, A. E. Ikui, Plasma membrane/cell wall perturbation activates a novel cell cycle checkpoint during G1 in Saccharomyces cerevisiae. Proc Natl Acad Sci U S A 113, 6910-6915 (2016).

(2) A. Das et al., Flippase-mediated phospholipid asymmetry promotes fast Cdc42 recycling in dynamic maintenance of cell polarity. Nat Cell Biol 14, 304-310 (2012).

(3) M. Adnan et al., SNARE Protein Snc1 Is Essential for Vesicle Trafficking, Membrane Fusion and Protein Secretion in Fungi. Cells 12 (2023).

(4) H.-U. Mösch, G. R. Fink, Dissection of Filamentous Growth by Transposon Mutagenesis in Saccharomyces cerevisiae. Genetics 145, 671-684 (1997).

(5) K. Kono, Y. Saeki, S. Yoshida, K. Tanaka, D. Pellman, Proteasomal degradation resolves competition between cell polarization and cellular wound healing. Cell 150, 151-164 (2012).

(6) A. Litsios et al., Proteome-scale movements and compartment connectivity during the eukaryotic cell cycle. Cell 187, 1490-1507.e1421 (2024).

(7) W.-K. Huh et al., Global analysis of protein localization in budding yeast.Nature 425, 686-691 (2003).

(8) T. López-Hernández, V. Haucke, T. Maritzen, Endocytosis in the adaptation to cellular stress. Cell Stress 4, 230-247 (2020).

Reference:

Preprints. (2024). Traditional ecological knowledge and environmental stewardship. https://doi.org/10.20944/preprints202406.1838.v1

“Environmental stewardship in Indigenous and local communities should not be understood only as a response to poverty or lack of alternatives.”(Preprints,2024)

The key idea of this article is that Environmental stewardship is an intention choice instead of that something people do because of no option. The author challenges the assumption that local people and communities protect the environment because of poverty. In this article Stewardship is presented as a value based practice that is shaped by culture, ethics and responsibility to future generations. By definition and reframing stewardship as purposeful, the author argues that local communities are active decision makers in environmental protection, not a passive participants.

Reference:

Preprints. (2024). Traditional ecological knowledge and environmental stewardship. https://doi.org/10.20944/preprints202406.1838.v1

“Practices rooted in Traditional Ecological Knowledge have contributed to long-term ecosystem resilience in various local contexts.”(Preprints,2024)

This idea can be connected to real world example like indigenous fire management practices . IFMP controlled burns that reduces wildlife risk and maintain ecosystem balance. These practices are based on long term observation of land and seasonal patterns instead of modern emergency responses. In many cases, when these practices ignored, then ecosystems became more vulnerable to environmental damage on large scale. This example shows that how TEK is applied in real world and it produces measurable environmental benefits. This example also supports the article that TEK is not just about theoretical knowledge but also effective practically in managing ecosystems and sustainability.

Reference:

Preprints. (2024). Traditional ecological knowledge and environmental stewardship. https://doi.org/10.20944/preprints202406.1838.v1

“Traditional Ecological Knowledge (TEK) represents a knowledge system grounded in lived experience and intergenerational learning.”(Preprints,2024)

This article connects strongly to our course because in class we will study sustainability and social-ecological systems, In class we already discussed about social ecological system where we learned that Environmental management is not just technical but it's also related to social and historical things. In class. we discussed about how ecosystems and humans influence each other, which is exactly what Traditional ecological knowledge is based on. TEK is defined as generations of observation, trial and error instead of short term scientific studies and policies. This article also connects to discussion about whose knowledge is considered valid in environmental decision making. The course gives the idea that ignoring indigenous people's knowledge leads to ineffective policies and wrong results. This article support the course argument that for effective environmental management multiple ways of knowing the TEK is necessary. This article also reinforces that sustainability is not just about protecting nature but also about respecting culture, people and historical experience.

Reference

Preprints. (2024). Traditional ecological knowledge and environmental stewardship. https://doi.org/10.20944/preprints202406.1838.v1

"Traditional Ecological Knowledge (TEK) refers to the cumulated wisdom, practices, and beliefs concerning their natural environment developed over centuries by indigenous and local communities"(Preprints,2024)

This definition explains that Traditional Ecological Knowledge (TEK) is not just a information about nature but it is a system that includes historical knowledge developed over past generations. The phrase "long term interaction" is important because it shows that TEK knowledge comes from repeated experience with same land over time. TEK focus on continuous observation and adaptation as compared to scientific research which focus on limited timeframes. This definition gave clarification that TEK is structured and intentional, not outdated or random knowledge. TEK challenges modern science that Environmental knowledge only comes from modern science.

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

Learn more at Review Commons

Reply to the reviewers

We sincerely appreciate the feedback, attention to detail and timeliness of the referees for our manuscript. Below, we provide a point-by-point response to all comments from the referees, detailing the changes we have already made, and those that are in progress. Referee's comments will appear in bolded text, while our responses will be unbolded. Any text quoted directly from the manuscript will be italicised and contained within "quotation marks". Additionally, we have grouped all comments into four categories (structural changes, minor text changes, experimental changes, figure changes), comments are numbered 1-n in each of these categories. Please note: this response to reviewer's comments included some images that cannot be embedded in this text-only section.

1. General Statements

We appreciate the overall highly positive and enthusiastic comments from all reviewers, who clearly appreciated the technical difficulty of this study, and noted amongst other things that this study represents" a major contribution to the future advancement of oocyst-sporozoite biology" and the development of the segmentation score for oocysts as a "major advance[ment]". We apologise for the omission of line numbers on the document sent to reviewers, we removed these for the bioRxiv submission without considering that this PDF would be transferred across to Review Commons.

We have responded to all reviewers comments through a variety of text changes, experimental inclusions, or direct query response. Significant changes to the manuscript since initial submission are as follows:

1. Refinement of rhoptry biogenesis model: Reviewers requested more detail around the content of the AORs, which we had previously suggested were a vehicle for rhoptry biogenesis as we saw they carried the rhoptry neck protein RON4. To address this, we first attempted to address this using antibodies against rhoptry bulb proteins but were unsuccessful. We then developed a * berghei* line where there rhoptry bulb protein RhopH3 was GFP-tagged. Using this parasite line, we observed that the earliest rhoptry-like structure, which we had previously interpreted as an AOR contained RhopH3. By contrast, RhopH3 was absent from AORs. Reflecting these observations we have renamed this initial structure the 'pre-rhoptry' and suggested a model for rhoptry biogenesis where rhoptry neck cargo are trafficked via the AOR but rhoptry bulb cargo are trafficked by small vesicles that move along the rootlet fibre (previously observed by EM).
2. Measurement of rhoptry neck vs bulb: While not directly suggested by the reviewers, we have also included an analysis that estimates the proportion of the sporozoite rhoptry that represents the rhoptry neck. By contrast to merozoites, which we show are overwhelmingly represented by the rhoptry bulb, the vast majority of the sporozoite rhoptry represents the rhoptry neck.
3. Measurement of subpellicular microtubules: One reviewer asked if we could measure the length of subpellicular microtubules where we had previously observed that they were longer on one side of the sporozoite than the other. We have now provided absolute and relative (% sporozoite length) length measurements for these subpellicular microtubules and also calculated the proportion of the microtubule that is polyglutamylated.
4. More detailed analysis of RON11cKD rhoptries: Multiple comments suggested a more detailed analysis of the rhoptries that were formed/not formed in RON11cKD We have included an updated analysis that shows the relative position of these rhoptries in sporozoites.

2. Point-by-point description of the revisions

Reviewer #1

Minor text changes (Reviewer #1)

1. __Text on page 12 could be condensed to highlight the new data of ron4 staining of the AOR. __

We agree with the reviewer that it is a reasonable suggestion. After obtaining additional data on the contents of the AOR (as described in General Statements #1), this section has been significantly rewritten to highlight these findings. 2.

__Add reference on page 3 after 'disrupted parasites' __

This sentence has been rewritten slightly with some references included and now reads: "Most data on these processes comes from electron microscopy studies 6-8, with relatively few functional reports on gene deleted or disrupted parasites9-11. 3.

__Change 'the basal complex at the leading edge' - this seems counterintuitive __

This change has been made. 4.

__Change 'mechanisms underlying SG are poorly' - what mechanisms? of invasion or infection? __

This was supposed to read "SG invasion" and has now been fixed. 5.

__On page 4: 'handful of proteins' __

This error has been corrected. 6.

__What are the 'three microtubule spindle structures'? __

The three microtubule spindle structures: hemispindle, mitotic spindle, and interpolar spindle are now listed explicitly in the text. 7.

__On page 5: 'little is known' - please describe what is known, also in other stages. At the end of the paper I would like to know what is the key difference to rhoptry function in other stages? __

The following sentence already detailed that we had recently used U-ExM to visualise rhoptry biogenesis in blood-stage parasites, but the following two sentences have been added to provide extra detail on these findings: "In that study, we defined the timing of rhoptry biogenesis showing that it begun prior to cytokinesis and completed approximate coincident with the final round of mitosis. Additionally, we observed that rhoptry duplication and inheritance was coupled with centriolar plaque duplication and nuclear fission." 8.

__change 'rhoptries golgi-derived, made de novo' __

This has been fixed. 9.

__change 'new understand to' __

This change has been made 10.

__'rhoptry malformations' seem to be similar in sporozoites and merozoites. Is that surprising/new? __

We assume this is in reference to mention of "rhoptry malformations" in the abstract. In the RON11 merozoite study (PMID:39292724) the authors noted no gross rhoptry malformations, only that one was not formed/missing. The abstract sentence has been changed to the following to better reflect this nuance: "*We show that stage-specific disruption of RON11 leads to a formation of sporozoites that only contain half the number of rhoptries of controls like in merozoites, however unlike in merozoites the majority of rhoptries appear grossly malformed."

* 11.

__What is known about crossing the basal lamina. Where rhoptries thought to be involved in this process? Or is it proteins on the surface or in other secretory organelles? __

We are unaware of any studies that specifically look at sporozoites crossing the SG basal lamina. A review, although now ~15 years old stated that "No information is available as to how the sporozoites traverse the basal lamina" (PMID:19608457) and we don't know any more information since then. To try and better define our understanding of rhoptry secretion during SG invasion, we have added the following sentence:

"It is currently unclear precisely when during these steps of SG invasion rhoptry proteins are required, but rhoptry secretion is thought to begin before in the haemolymph before SG invasion16." 12.

__On page change/specify: 'wide range of parasite structures' __

The structures observed have been listed: centriolar plaque, rhoptry, apical polar rings, rootlet fibre, basal complex, apicoplast. 13.

__On page 7: is Airyscan2 a particular method or a specific microscope? __

Airyscan2 is a detector setup on Zeiss LSM microscopes, this was already detailed in the materials and methods sections, but figure legends have been clarified to read: "...imaged by an LSM900 microscopy with an Airyscan2 detector". 14.

__how large is RON11? __

RON11 is 112 kDa in * berghei*, as noted in the text. 15.

__There is no causal link between ookinete invasion and oocyst developmental asynchrony __

We have deleted the sentence that implied that ookinete invasion was responsible for oocyst asynchrony. This section now simply states that "Development of each oocyst within a midgut is asynchronous..." 16.

__First sentence of page 24 appears to contradict what is written in results____ I don't understand the first two sentences in the paragraph titled Comparison between Plasmodium spp __

This sentence was worded confusingly, making it appear contradictory when that was not the intention. The sentence has been changed to more clearly support what is written in the discussion and now reads: "Our extensive analysis only found one additional ultrastructural difference between Plasmodium spp."

__On page 25 or before the vast number of electron microscopy studies should be discussed and compared with the authors new data. __

It is not entirely clear which new data should be specifically discussed based on this comment. However, we have added a new paragraph that broadly compares MoTissU-ExM and our findings with other imaging methods previously used on mosquito-stage malaria parasites:

"*Comparison of MoTissU-ExM and other imaging modalities

Prior to the development of MoTissU-ExM, imaging of mosquito-stage malaria parasites in situ had been performed using electron microscopy7,8,11,28, conventional immunofluorescence assays (IFA)10, and live-cell microscopy25. MoTissU-ExM offers significant advantages over electron microscopy techniques, especially volume electron microscopy, in terms of accessibility, throughput, and detection of multiple targets. While we have benchmarked many of our observations against previous electron microscopy studies, the intracellular detail that can be observed by MoTissU-ExM is not as clear as electron microscopy. For example, previous electron microscopy studies have observed Golgi-derived vesicles trafficking along the rootlet fibre8 and distinguished the apical polar rings44; both of which we could not observe using MoTissU-ExM. Compared to conventional IFA, MoTissU-ExM dramatically improves the number and detail of parasite structures/organelles that can be visualised while maintaining the flexibility of target detection. By contrast, it can be difficult or impossible to reliably quantify fluorescence intensity in samples prepared by expansion microscopy, something that is routine for conventional IFA. For studying temporally complex processes, live-cell microscopy is the 'gold-standard' and there are some processes that fundamentally cannot be studied or observed in fixed cells. We attempt to increase the utility of MoTissU-ExM in discerning temporal relationships through the development of the segmentation score but note that this cannot be applied to the majority of oocyst development. Collectively, MoTissU-ExM offers some benefits over these previously applied techniques but does not replace them and instead serves as a novel and complementary tool in studying the cell biology of mosquito-stage malaria parasites.**"

*

__First sentence on page 27: there are many studies on parasite proteins involved in salivary gland invasion that could be mentioned/discussed. __

The sentence in question is "To the best of our knowledge, the ability of sporozoites to cross the basal lamina and accumulate in the SG intercellular space has never previously been reported."

This sentence has now been changed to read as follows: "While numerous studies have characterized proteins whose disruption inhibited SG invasion9,10,15,59-63, to the best of our knowledge the ability of sporozoites to cross the basal lamina and accumulate in the SG intercellular space has never previously been reported ."

__On page 10 I suggest to qualify the statement 'oocyst development has typcially been inferred by'. There seem a few studies that show that size doesn't reflect maturation. __

In our opinion, this statement is already qualified in the following sentence which reads: "Recent studies have shown that while oocysts increase in size initially, their size eventually plateaus (11 days pot infection (dpi) in P. falciparum4)."

__On page 16 the authors state that different rhoptries might have different function. This is an interesting hypothesis/result that could be mentioned in the abstract. __

The abstract already contains the following statement: "...and provide the first evidence that rhoptry pairs are specialised for different invasion events." We see this as an equivalent statement.

Experimental changes (Reviewer #1)

1. On page 19: do the parasites with the RON11 knockout only have the cytoplasmic or only the apical rhoptries?

The answer to this is not completely clear. We have added the following data to Figures 6 and 8 where we quantify the proportion of rhoptries that are either apical or cytoplasmic: In both wildtype parasites and RON11ctrl parasites, oocyst spz rhoptries are roughly 50:50 apical:cytoplasmic (with a small but consistent majority apical), while almost all rhoptries are found at the apical end (>90%) in SG spz. Presumably, after the initial apical rhoptries are 'used up' during SG invasion, the rhoptries that were previously cytoplasmic take their place. In RON11cKD the ratio of apical:cytoplasmic rhoptries is fairly similar to control oocyst spz. In RON11cKD SG spz, the proportion of cytoplasmic rhoptries decreases but not to the same extent as in wildtype or RON11Ctrl. From this, we infer that the two rhoptries that are lost/not made in RON11cKD sporozoites are likely a combination of both the apical and cytoplasmic rhoptries we find in control sporozoites.

__in panel G: Are the dense granules not micronemes? What are the dark lines? Rhoptries?? __

We have labelled all of Figure 1 more clearly to point out that the 'dark lines' are indeed rhoptries. Additionally, we have renamed the 'protein-dense granules' to 'protein-rich granules', as it seems we are suggesting that these structures are dense granules the secretory organelle. At this stage we simply do not know what all of these granules are. The observation that some but not all of these granules contain CSP (Supplementary Figure 2) suggests that they may represent heterogenous structures. It is indeed possible that some are micronemes, however, we think it is unlikely that they are all micronemes for a number of reasons: (1) micronemes are not nearly this protein dense in other Plasmodium lifecycle stages, (2) some of them carry CSP which has not been demonstrated to be micronemal, (3) very few of these granules are present in SG sporozoites, which would be unexpected because microneme secretion is required for hepatocyte invasion.

__Figure 2 seems to add little extra compared to the following figures and could in my view go to the supplement. __

We agree that Figure 2b adds little and so have moved that to Supplementary Figure 2, but think that the relative ease at which it can be distinguished if sporozoites are in the secretory cavity or SG epithelial cell is a key observation because of the difficulty in doing this by conventional IFA.

__On page 8 the authors mention a second layer of CSP but do not further investigate it. It is likely hard to investigate this further but to just let it stand as it is seems unsatisfactory, considering that CSP is the malaria vaccine. What happens if you add anti-CSP antibodies? I would suggest to shorten the opening paragraphs of this paper and to focus on the rhoptries. This could be done be toning down the text on all aspects that are not rhoptries and point to the open question some of the observations such as the CSP layers raise for future studies. __

When writing the manuscript, we were unsure whether to include this data at all as it is a purely incidental finding. We had no intention of investigating CSP specifically, but anti-CSP antibodies were included in most of the salivary gland imaging experiments so we could more easily find sporozoites. Given the tremendous importance of CSP to the field, we figured that these observations were potentially important enough that they should be reported in the literature even though they are not something we have the intention or resources to investigate subsequently. Additionally, after consultation with other microscopists we think there is a reasonable chance that this double-layer effect could be a product of chemical fixation. To account for this, we have qualified the paragraph on CSP with this sentence:

"We cannot determine if there is any functional significance of this second CSP layer and considering that it has not been observed previously it may well represent an artefact of chemical (paraformaldehyde) fixation."

__Maybe include more detail of the differences between species on rhoptry structure into Figure 4. I would encourage to move the Data on rhoptries in Figure S6 to the main text ie to Figure 4. __

We have moved the images of developing rhoptries in * falciparum *(previously Figure S6a and b) into figure 4, which now looks as follows:

Figure S8 (previously S6c) now consists only of the MG spz rhoptry quantification

Manuscript structural changes (Reviewer #1)

1. Abstract: don't focus on technique but on the questions you tried to answer (ie rewrite or delete the 3rd and 4th sentence)

2. 'range of cell biology processes' - I understand the paper that the key discovery concerns rhoptry biogenesis and function, so focus on that, all other aspects appear rather peripheral.

3. 'Much of this study focuses on the secretory organelles': I would suggest to rewrite the intro to focus solely on those, which yield interesting findings.

4. Page 11: I am tempted to suggest the authors start their study with Figure 3 and add panel A from Figure 2 to it. This leads directly to their nice work on rhoptries. Other features reported in Figures 1 and 2 are comparatively less exciting and could be moved to the supplement or reported in a separate study.____ Page 23: I suggest to delete the first sentence and focus on the functional aspects and the discoveries.

5. __Maybe add a conclusion section rather than a future application section, which reads as if you want to promoted the use of ultrastructure expansion microscopy. To my taste the technological advance is a bit overplayed considering the many applications of this techniques over the last years, especially in parasitology, where it seems widely used. In any case, please delete 'extraordinarily' __

Response to Reviewer#1 manuscript structural changes 1-5: This reviewer considers the findings related to rhoptry biology as the most significant aspect of the study and suggests rewriting the manuscript to emphasize these findings specifically. Doing so might make the key findings easier to interpret. However, in our view, this approach could misrepresent how the study originated and what we see as the most important outcomes. We did not develop MoTissU-ExM specifically to investigate rhoptry biology. Instead, this technique was created independently of any particular biological question, and once established, we asked what questions it could answer, using rhoptry biology as a proof of concept. Given the authors' previous work and available resources, we chose to focus on rhoptry biology. Since this was driven by basic research rather than a specific hypothesis, it's important to acknowledge this in the manuscript. While we agree that the findings related to rhoptry biology are valuable, we believe that highlighting the technique's ability to observe organelles, structures, and phenotypes with unprecedented ease and detail is more important than emphasizing the rhoptry findings alone. For these reasons, we have decided not to restructure the manuscript as suggested.

Reviewer #2

Minor text changes (Reviewer #2)

1. __The 'image Z-depth' value indicated in the figures is ambiguous. It is not clear whether this refers to the distance from the coverslip surface or the starting point of the z-stack image acquisition. A precise definition of this parameter would be beneficial. __

In the legend of Figure 1, the image Z-depth has been clarified as "sum distance of Z-slices in max intensity projection". 2.

__Paragraph 3 of the introduction - line 7, "handful or proteins" should be handful of proteins __

This has been corrected. 3.

__Paragraph 5 of the introduction - line 7, "also able to observed" should be observe __

This has been changed. 4.

__In the final paragraph of the introduction - line 1, "leverage this new understand" should be understanding __

This has been fixed. 5.

__The first paragraph of the discussion summary contains an incomplete sentence on line 7, "PbRON11ctrl-infected SGs." __

This has been removed. 6.

__The second paragraph of the discussion - line 10, "until cytokinesis beings" should be begins __

This mistake has been corrected. 7.

__One minor point that author suggest that oocyst diameter is not appropriate for the development of sporozoite develop. This is not so true as oocyst diameter tells between cell division and cell growth so it is important parameter especially where the proliferation with oocyst does not take place but the growth of oocyst takes place. __

We agree that this was not highlighted enough in the text. The final sentence of the results section about this now reads:

"While diameter is a useful readout for oocyst development in the early stages of its growth, this suggests that diameter is a poor readout for oocyst development once sporozoite formation has begun and highlights the usefulness of the segmentation score as an alternative.", and the final sentence of the discussion section about this now reads "Considering that oocyst size does not plateau until cytokinesis begins4, measuring oocyst diameter may represent a useful biological clock specifically when investigating the early stages of oocyst development." 8.