Author response:

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

Responses to Reviewer’s Comments:  

To Reviewer #2:

(1) The use of two m⁵C reader proteins is likely a reason for the high number of edits introduced by the DRAM-Seq method. Both ALYREF and YBX1 are ubiquitous proteins with multiple roles in RNA metabolism including splicing and mRNA export. It is reasonable to assume that both ALYREF and YBX1 bind to many mRNAs that do not contain m⁵C. 

To substantiate the author's claim that ALYREF or YBX1 binds m⁵C-modified RNAs to an extent that would allow distinguishing its binding to non-modified RNAs from binding to m⁵Cmodified RNAs, it would be recommended to provide data on the affinity of these, supposedly proven, m⁵C readers to non-modified versus m⁵C-modified RNAs. To do so, this reviewer suggests performing experiments as described in Slama et al., 2020 (doi: 10.1016/j.ymeth.2018.10.020). However, using dot blots like in so many published studies to show modification of a specific antibody or protein binding, is insufficient as an argument because no antibody, nor protein, encounters nanograms to micrograms of a specific RNA identity in a cell. This issue remains a major caveat in all studies using so-called RNA modification reader proteins as bait for detecting RNA modifications in epitranscriptomics research. It becomes a pertinent problem if used as a platform for base editing similar to the work presented in this manuscript.

The authors have tried to address the point made by this reviewer. However, rather than performing an experiment with recombinant ALYREF-fusions and m⁵C-modified to unmodified RNA oligos for testing the enrichment factor of ALYREF in vitro, the authors resorted to citing two manuscripts. One manuscript is cited by everybody when it comes to ALYREF as m⁵C reader, however none of the experiments have been repeated by another laboratory. The other manuscript is reporting on YBX1 binding to m⁵C-containing RNA and mentions PARCLiP experiments with ALYREF, the details of which are nowhere to be found in doi: 10.1038/s41556-019-0361-y.

Furthermore, the authors have added RNA pull-down assays that should substitute for the requested experiments. Interestingly, Figure S1E shows that ALYREF binds equally well to unmodified and m⁵C-modified RNA oligos, which contradicts doi:10.1038/cr.2017.55, and supports the conclusion that wild-type ALYREF is not specific m⁵C binder. The necessity of including always an overexpression of ALYREF-mut in parallel DRAM experiments, makes the developed method better controlled but not easy to handle (expression differences of the plasmid-driven proteins etc.) 

Thank you for pointing this out. First, we would like to correct our previous response: the binding ability of ALYREF to m⁵C-modified RNA was initially reported in doi: 10.1038/cr.2017.55, (and not in doi: 10.1038/s41556-019-0361-y), where it was observed through PAR-CLIP analysis that the K171 mutation weakens its binding affinity to m⁵C -modified RNA.

Our previous experimental approach was not optimal: the protein concentration in the INPUT group was too high, leading to overexposure in the experimental group. Additionally, we did not conduct a quantitative analysis of the results at that time. In response to your suggestion, we performed RNA pull-down experiments with YBX1 and ALYREF, rather than with the pan-DRAM protein, to better validate and reproduce the previously reported findings. Our quantitative analysis revealed that both ALYREF and YBX1 exhibit a stronger affinity for m⁵C -modified RNAs. Furthermore, mutating the key amino acids involved in m⁵C recognition significantly reduced the binding affinity of both readers. These results align with previous studies (doi: 10.1038/cr.2017.55 and doi: 10.1038/s41556-019-0361-y), confirming that ALYREF and YBX1 are specific readers of m⁵C -modified RNAs. However, our detection system has certain limitations. Despite mutating the critical amino acids, both readers retained a weak binding affinity for m⁵C, suggesting that while the mutation helps reduce false positives, it is still challenging to precisely map the distribution of m⁵C modifications. To address this, we plan to further investigate the protein structure and function to obtain a more accurate m⁵C sequencing of the transcriptome in future studies. Accordingly, we have updated our results and conclusions in lines 294-299 and discuss these limitations in lines 109114.

In addition, while the m⁵C assay can be performed using only the DRAM system alone, comparing it with the DRAM^mut control enhances the accuracy of m⁵C region detection. To minimize the variations in transfection efficiency across experimental groups, it is recommended to use the same batch of transfections. This approach not only ensures more consistent results but also improve the standardization of the DRAM assay, as discussed in the section added on line 308-312.

(2) Using sodium arsenite treatment of cells as a means to change the m⁵C status of transcripts through the downregulation of the two major m⁵C writer proteins NSUN2 and NSUN6 is problematic and the conclusions from these experiments are not warranted. Sodium arsenite is a chemical that poisons every protein containing thiol groups. Not only do NSUN proteins contain cysteines but also the base editor fusion proteins. Arsenite will inactivate these proteins, hence the editing frequency will drop, as observed in the experiments shown in Figure 5, which the authors explain with fewer m⁵C sites to be detected by the fusion proteins.

The authors have not addressed the point made by this reviewer. Instead the authors state that they have not addressed that possibility. They claim that they have revised the results section, but this reviewer can only see the point raised in the conclusions. An experiment would have been to purify base editors via the HA tag and then perform some kind of binding/editing assay in vitro before and after arsenite treatment of cells.

We appreciate the reviewer’s insightful comment. We fully agree with the concern raised. In the original manuscript, our intention was to use sodium arsenite treatment to downregulate NSUN mediated m⁵C levels and subsequently decrease DRAM editing efficiency, with the aim of monitoring m⁵C dynamics through the DRAM system. However, as the reviewer pointed out, sodium arsenite may inactivate both NSUN proteins and the base editor fusion proteins, and any such inactivation would likely result in a reduced DRAM editing.

This confounds the interpretation of our experimental data.

As demonstrated in Author response image 1A, western blot analysis confirmed that sodium arsenite indeed decreased the expression of fusion proteins. In addition, we attempted in vitro fusion protein purificationusing multiple fusion tags (HIS, GST, HA, MBP) for DRAM fusion protein expression, but unfortunately, we were unable to obtain purified proteins. However, using the Promega TNT T7 Rapid Coupled In Vitro Transcription/Translation Kit, we successfully purified the DRAM protein (Author response image 1B). Despite this success, subsequent in vitro deamination experiments did not yield the expected mutation results (Author response image 1C), indicating that further optimization is required. This issue is further discussed in line 314-315.

Taken together, the above evidence supports that the experiment of sodium arsenite treatment was confusing and we determined to remove the corresponding results from the main text of the revised manuscript.

Author response image 1.

(3) The authors should move high-confidence editing site data contained in Supplementary Tables 2 and 3 into one of the main Figures to substantiate what is discussed in Figure 4A. However, the data needs to be visualized in another way then excel format. Furthermore, Supplementary Table 2 does not contain a description of the columns, while Supplementary Table 3 contains a single row with letters and numbers.

The authors have not addressed the point made by this reviewer. Figure 3F shows the screening process for DRAM-seq assays and principles for screening highconfidence genes rather than the data contained in Supplementary Tables 2 and 3 of the former version of this manuscript.

Thank you for your valuable suggestion. We have visualized the data from Supplementary Tables 2 and 3 in Figure 4A as a circlize diagram (described in lines 213-216), illustrating the distribution of mutation sites detected by the DRAM system across each chromosome. Additionally, to improve the presentation and clarity of the data, we have revised Supplementary Tables 2 and 3 by adding column descriptions, merging the DRAM-ABE and DRAM-CBE sites, and including overlapping m⁵C genes from previous datasets.

Responses to Reviewer’s Comments:  

To Reviewer #3:

The authors have again tried to address the former concern by this reviewer who questioned the specificity of both m⁵C reader proteins towards modified RNA rather than unmodified RNA. The authors chose to do RNA pull down experiments which serve as a proxy for proving the specificity of ALYREF and YBX1 for m⁵C modified RNAs. Even though this reviewer asked for determining the enrichment factor of the reader-base editor fusion proteins (as wildtype or mutant for the identified m⁵C specificity motif) when presented with m⁵C-modified RNAs, the authors chose to use both reader proteins alone (without the fusion to an editor) as wildtype and as respective m⁵C-binding mutant in RNA in vitro pull-down experiments along with unmodified and m⁵C-modified RNA oligomers as binding substrates. The quantification of these pull-down experiments (n=2) have now been added, and are revealing that (according to SFigure 1 E and G) YBX1 enriches an RNA containing a single m⁵C by a factor of 1.3 over its unmodified counterpart, while ALYREF enriches by a factor of 4x. This is an acceptable approach for educated readers to question the specificity of the reader proteins, even though the quantification should be performed differently (see below).

Given that there is no specific sequence motif embedding those cytosines identified in the vicinity of the DRAM-edits (Figure 3J and K), even though it has been accepted by now that most of the m⁵C sites in mRNA are mediated by NSUN2 and NSUN6 proteins, which target tRNA like substrate structures with a particular sequence enrichment, one can conclude that DRAM-Seq is uncovering a huge number of false positives. This must be so not only because of the RNA bisulfite seq data that have been extensively studied by others, but also by the following calculations: Given that the m⁵C/C ratio in human mRNA is 0.02-0.09% (measured by mass spec) and assuming that 1/4 of the nucleotides in an average mRNA are cytosines, an mRNA of 1.000 nucleotides would contain 250 Cs. 0.02- 0.09% m⁵C/C would then translate into 0.05-0.225 methylated cytosines per 250 Cs in a 1000 nt mRNA. YBX1 would bind every C in such an mRNA since there is no m⁵C to be expected, which it could bind with 1.3 higher affinity. Even if the mRNAs would be 10.000 nt long, YBX1 would bind to half a methylated cytosine or 2.25 methylated cytosines with 1.3x higher affinity than to all the remaining cytosines (2499.5 to 2497.75 of 2.500 cytosines in 10.000 nt, respectively). These numbers indicate a 4999x to 1110x excess of cytosine over m⁵C in any substrate RNA, which the "reader" can bind as shown in the RNA pull-downs on unmodified RNAs. This reviewer spares the reader of this review the calculations for ALYREF specificity, which is slightly higher than YBX1. Hence, it is up to the capable reader of these calculations to follow the claim that this minor affinity difference allows the unambiguous detection of the few m⁵C sites in mRNA be it in the endogenous scenario of a cell or as fusion-protein with a base editor attached? 

We sincerely appreciate the reviewer’s rigorous analysis. We would like to clarify that in our RNA pulldown assays, we indeed utilized the full DRAM system (reader protein fused to the base editor) to reflect the specificity of m⁵C recognition. As previously suggested by the reviewer, to independently validate the m⁵C-binding specificity of ALYREF and YBX1, we performed separate pulldown experiments with wild-type and mutant reader proteins (without the base editor fusion) using both unmodified and m⁵C-modified RNA substrates. This approach aligns with established methodologies in the field (doi:10.1038/cr.2017.55 and doi: 10.1038/s41556-019-0361-y). We have revised the Methods section (line 230) to explicitly describe this experimental design.

Although the m⁵C/C ratios in LC/MS-assayed mRNA are relatively low (ranging from 0.02% to 0.09%), as noted by the reviewer, both our data and previous studies have demonstrated that ALYREF and YBX1 preferentially bind to m⁵C-modified RNAs over unmodified RNAs, exhibiting 4-fold and 1.3-fold enrichment, respectively (Supplementary Figure 1E–1G). Importantly, this specificity is further enhanced in the DRAM system through two key mechanisms: first, the fusion of reader proteins to the deaminase restricts editing to regions near m⁵C sites, thereby minimizing off-target effects; second, background editing observed in reader-mutant or deaminase controls (e.g., DRAM^mut-CBE in Figure 2D) is systematically corrected for during data analysis.

We agree that the theoretical challenge posed by the vast excess of unmodified cytosines. However, our approach includes stringent controls to alleviate this issue. Specifically, sites identified in NSUN2/NSUN6 knockout cells or reader-mutant controls are excluded (Figure 3F), which significantly reduces the number of false-positive detections. Additionally, we have observed deamination changes near high-confidence m⁵C methylation sites detected by RNA bisulfite sequencing, both in first-generation and high-throughput sequencing data. This observation further substantiates the validity of DRAM-Seq in accurately identifying m⁵C sites.

We fully acknowledge that residual false positives may persist due to the inherent limitations of reader protein specificity, as discussed in line 299-301 of our manuscript. To address this, we plan to optimize reader domains with enhanced m⁵C binding (e.g., through structure-guided engineering), which is also previously implemented in the discussion of the manuscript.

The reviewer supports the attempt to visualize the data. However, the usefulness of this Figure addition as a readable presentation of the data included in the supplement is up to debate.

Thank you for your kind suggestion. We understand the reviewer's concern regarding data visualization. However, due to the large volume of DRAM-seq data, it is challenging to present each mutation site and its characteristics clearly in a single figure. Therefore, we chose to categorize the data by chromosome, which not only allows for a more organized presentation of the DRAM-seq data but also facilitates comparison with other database entries. Additionally, we have updated Supplementary Tables 2 and 3 to provide comprehensive information on the mutation sites. We hope that both the reviewer and editors will understand this approach. We will, of course, continue to carefully consider the reviewer's suggestions and explore better ways to present these results in the future.

(3) A set of private Recommendations for the Authors that outline how you think the science and its presentation could be strengthened

NEW COMMENTS to TEXT:

Abstract:

"5-Methylcytosine (m⁵C) is one of the major post-transcriptional modifications in mRNA and is highly involved in the pathogenesis of various diseases."

In light of the increasing use of AI-based writing, and the proof that neither DeepSeek nor ChatGPT write truthfully statements if they collect metadata from scientific abstracts, this sentence is utterly misleading.

m⁵C is not one of the major post-transcriptional modifications in mRNA as it is only present with a m⁵C/C ratio of 0.02- 0.09% as measured by mass-spec. Also, if m⁵C is involved in the pathogenesis of various diseases, it is not through mRNA but tRNA. No single published work has shown that a single m⁵C on an mRNA has anything to do with disease. Every conclusion that is perpetuated by copying the false statements given in the many reviews on the subject is based on knock-out phenotypes of the involved writer proteins. This reviewer wishes that the authors would abstain from the common practice that is currently flooding any scientific field through relentless repetitions in the increasing volume of literature which perpetuate alternative facts.

We sincerely appreciate the reviewer’s insightful comments. While we acknowledge that m⁵C is not the most abundant post-transcriptional modification in mRNA, we believe that research into m⁵C modification holds considerable value. Numerous studies have highlighted its role in regulating gene expression and its potential contribution to disease progression. For example, recent publications have demonstrated that m⁵C modifications in mRNA can influence cancer progression, lipid metabolism, and other pathological processes (e.g., PMID: 37845385; 39013911; 39924557; 38042059; 37870216).

We fully agree with the reviewer on the importance of maintaining scientific rigor in academic writing. While m⁵C is not the most abundant RNA modification, we cannot simply draw a conclusion that the level of modification should be the sole criterion for assessing its biological significance. However, to avoid potential confusion, we have removed the word “major”.

COMMENTS ON FIGURE PRESENTATION:

Figure 2D:

The main text states: "DRAM-CBE induced C to U editing in the vicinity of the m⁵C site in AP5Z1 mRNA, with 13.6% C-to-U editing, while this effect was significantly reduced with APOBEC1 or DRAM^mut-CBE (Fig.2D)." The Figure does not fit this statement. The seq trace shows a U signal of about 1/3 of that of C (about 30%), while the quantification shows 20+ percent

Thank you for your kind suggestion. Upon visual evaluation, the sequencing trace in the figure appears to suggest a mutation rate closer to 30% rather than 22%. However, relying solely on the visual interpretation of sequencing peaks is not a rigorous approach. The trace on the left represents the visualization of Sanger sequencing results using SnapGene, while the quantification on the right is derived from EditR 1.0.10 software analysis of three independent biological replicates. The C-to-U mutation rates calculated were 22.91667%, 23.23232%, and 21.05263%, respectively. To further validate this, we have included the original EditR analysis of the Sanger sequencing results for the DRAM-CBE group used in the left panel of Figure 2D (see Author response image 2). This analysis confirms an m⁵C fraction (%) of 22/(22+74) = 22.91667, and the sequencing trace aligns well with the mutation rate we reported in Figure 2D. In conclusion, the data and conclusions presented in Figure 2D are consistent and supported by the quantitative analysis.

Author response image 2.

Figure 4B: shows now different numbers in Venn-diagrams than in the same depiction, formerly Figure 4A

We sincerely thank the reviewer for pointing out this issue, and we apologize for not clearly indicating the changes in the previous version of the manuscript. In response to the initial round of reviewer comments, we implemented a more stringent data filtering process (as described in Figure 3F and method section) : "For high-confidence filtering, we further adjusted the parameters of Find_edit_site.pl to include an edit ratio of 10%–60%, a requirement that the edit ratio in control samples be at least 2-fold higher than in NSUN2 or NSUN6knockout samples, and at least 4 editing events at a given site." As a result, we made minor adjustments to the Venn diagram data in Figure 4A, reducing the total number of DRAM-edited mRNAs from 11,977 to 10,835. These changes were consistently applied throughout the manuscript, and the modifications have been highlighted for clarity. Importantly, these adjustments do not affect any of the conclusions presented in the manuscript.

Figure 4B and D: while the overlap of the DRAM-Seq data with RNA bisulfite data might be 80% or 92%, it is obvious that the remaining data DRAM seq suggests a detection of additional sites of around 97% or 81.83%. It would be advised to mention this large number of additional sites as potential false positives, unless these data were normalized to the sites that can be allocated to NSUN2 and NSUN6 activity (NSUN mutant data sets could be substracted).

Thank you for pointing this out. The Venn diagrams presented in Figure 4B and D already reflect the exclusion of potential false-positive sites identified in methyltransferasedeficient datasets, as described in our experimental filtering process, and they represent the remaining sites after this stringent filtering. However, we acknowledge that YBX1 and ALYREF, while preferentially binding to m⁵C-modified RNA, also exhibit some affinity for unmodified RNA. Although we employed rigorous controls, including DRAM^mut and deaminase groups, to minimize false positives, the possibility of residual false positives cannot be entirely ruled out. Addressing this limitation would require even more stringent filtering methods, as discussed in lines 299–301 of the manuscript. We are committed to further optimizing the DRAM system to enhance the accuracy of transcriptome-wide m⁵C analysis in future studies.

SFigure 1: It is clear that the wild type version of both reader proteins are robustly binding to RNA that does not contain m⁵C. As for the calculations of x-fold affinity loss of RNA binding using both ALYREF -mut or YBX1 -mut, this reviewer asks the authors to determine how much less the mutated versions of the proteins bind to a m⁵C-modified RNAs. Hence, a comparison of YBX1 versus YBX1 -mut (ALYREF versus ALYREF -mut) on the same substrate RNA with the same m⁵C-modified position would allow determining the contribution of the so-called modification binding pocket in the respective proteins to their RNA binding. The way the authors chose to show the data presently is misleading because what is compared is the binding of either the wild type or the mutant protein to different RNAs.

We appreciate the reviewer’s valuable feedback and apologize for any confusion caused by the presentation of our data. We would like to clarify the rationale behind our approach. The decision to present the wild-type and mutant reader proteins in separate panels, rather than together, was made in response to comments from Reviewer 2. Below, we provide a detailed explanation of our experimental design and its justification.

First, we confirmed that YBX1 and ALYREF exhibit stronger binding affinity to m⁵Cmodified RNA compared to unmodified RNA, establishing their role as m⁵C reader proteins. Next, to validate the functional significance of the DRAM^mut group, we demonstrated that mutating key amino acids in the m⁵C-binding pocket significantly reduces the binding affinity of YBX1^mut and ALYREF^mut to m⁵C-modified RNA. This confirms that the DRAM^mut group effectively minimizes false-positive results by disrupting specific m⁵C interactions.

Crucially, in our pull-down experiments, both the wild-type and mutant proteins (YBX1/YBX1^mut and ALYREF/ALYREF^mut) were incubated with the same RNA sequences. To avoid any ambiguity, we have included the specific RNA sequence information in the Methods section (lines 463–468). This ensures a assessment of the reduced binding affinity of the mutant versions relative to the wild-type proteins, even though they are presented in separate panels.

We hope this explanation clarifies our approach and demonstrates the robustness of our findings. We sincerely appreciate the reviewer’s understanding and hope this addresses their concerns.

SFigure 2C: first two panels are duplicates of the same image.

Thank you for pointing this out. We sincerely apologize for incorrectly duplicating the images. We have now updated Supplementary Figure 2C with the correct panels and have provided the original flow cytometry data for the first two images. It is important to note that, as demonstrated by the original data analysis, the EGFP-positive quantification values (59.78% and 59.74%) remain accurate. Therefore, this correction does not affect the conclusions of our study. Thank you again for bringing this to our attention.

Author response image 3.

SFigure 4B: how would the PCR product for NSUN6 be indicative of a mutation? The used primers seem to amplify the wildtype sequence.

Thank you for your kind suggestion. In our NSUN6^-/- cell line, the NSUN6 gene is only missing a single base pair (1bp) compared to the wildtype, which results in frame shift mutation and reduction in NSUN6 protein expression. We fully agree with the reviewer that the current PCR gel electrophoresis does not provide a clear distinction of this 1bp mutation. To better illustrate our experimental design, we have included a schematic representation of the knockout sequence in SFigure 4B. Additionally, we have provided the original sequencing data, and the corresponding details have been added to lines 151-153 of the manuscript for further clarification.

Author response image 4.

SFigure 4C: the Figure legend is insufficient to understand the subfigure.

Thank you for your valuable suggestion. To improve clarity, we have revised the figure legend for SFigure 4C, as well as the corresponding text in lines 178-179. We have additionally updated the title of SFigure 4 for better clarity. The updated SFigure 4C now demonstrates that the DRAM-edited mRNAs exhibit a high degree of overlap across the three biological replicates.

SFigure 4D: the Figure legend is insufficient to understand the subfigure.

Thank you for your kind suggestion. We have revised the figure legend to provide a clearer explanation of the subfigure. Specifically, this figure illustrates the motif analysis derived from sequences spanning 10 nucleotides upstream and downstream of DRAMedited sites mediated by loci associated with NSUN2 or NSUN6. To enhance clarity, we have also rephrased the relevant results section (lines 169-175) and the corresponding discussion (lines 304-307).

SFigure 7: There is something off with all 6 panels. This reviewer can find data points in each panel that do not show up on the other two panels even though this is a pairwise comparison of three data sets (file was sent to the Editor) Available at https://elife-rp.msubmit.net/elife-rp_files/2025/01/22/00130809/02/130809_2_attach_27_15153.pdf

Response: We thank the reviewer for pointing this out. We would like to clarify the methodology behind this analysis. In this study, we conducted pairwise comparisons of the number of DRAM-edited sites per gene across three biological replicates of DRAM-ABE or DRAM-CBE, visualized as scatterplots. Each data point in the plots corresponds to a gene, and while the same gene is represented in all three panels, its position may vary vertically or horizontally across the panels. This variation arises because the number of mutation sites typically differs between replicates, making it unlikely for a data point to occupy the exact same position in all panels. A similar analytical approach has been used in previous studies on m6A (PMID: 31548708). To address the reviewer’s concern, we have annotated the corresponding positions of the questioned data points with arrows in Author response image 5.

Author response image 5.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In their manuscript entitled 'The domesticated transposon protein L1TD1 associates with its ancestor L1 ORF1p to promote LINE-1 retrotransposition', Kavaklıoğlu and colleagues delve into the role of L1TD1, an RNA binding protein (RBP) derived from a LINE1 transposon. L1TD1 proves crucial for maintaining pluripotency in embryonic stem cells and is linked to cancer progression in germ cell tumors, yet its precise molecular function remains elusive. Here, the authors uncover an intriguing interaction between L1TD1 and its ancestral LINE-1 retrotransposon.

The authors delete the DNA methyltransferase DNMT1 in a haploid human cell line (HAP1), inducing widespread DNA hypo-methylation. This hypomethylation prompts abnormal expression of L1TD1. To scrutinize L1TD1's function in a DNMT1 knock-out setting, the authors create DNMT1/L1TD1 double knock-out cell lines (DKO). Curiously, while the loss of global DNA methylation doesn't impede proliferation, additional depletion of L1TD1 leads to DNA damage and apoptosis.

To unravel the molecular mechanism underpinning L1TD1's protective role in the absence of DNA methylation, the authors dissect L1TD1 complexes in terms of protein and RNA composition. They unveil an association with the LINE-1 transposon protein L1-ORF1 and LINE-1 transcripts, among others.

Surprisingly, the authors note fewer LINE-1 retro-transposition events in DKO cells compared to DNMT1 KO alone.

Strengths:

The authors present compelling data suggesting the interplay of a transposon-derived human RNA binding protein with its ancestral transposable element. Their findings spur interesting questions for cancer types, where LINE1 and L1TD1 are aberrantly expressed.

Weaknesses:

Suggestions for refinement:

The initial experiment, inducing global hypo-methylation by eliminating DNMT1 in HAP1 cells, is intriguing and warrants more detailed description. How many genes experience misregulation or aberrant expression? What phenotypic changes occur in these cells? Why did the authors focus on L1TD1? Providing some of this data would be helpful to understand the rationale behind the thorough analysis of L1TD1.

The finding that L1TD1/DNMT1 DKO cells exhibit increased apoptosis and DNA damage but decreased L1 retro-transposition is unexpected. Considering the DNA damage associated with retro-transposition and the DNA damage and apoptosis observed in L1TD1/DNMT1 DKO cells, one would anticipate the opposite outcome. Could it be that the observation of fewer transposition-positive colonies stems from the demise of the most transpositionpositive colonies? Further exploration of this phenomenon would be intriguing.

Reviewer #2 (Public review):

In this study, Kavaklıoğlu et al. investigated and presented evidence for a role for domesticated transposon protein L1TD1 in enabling its ancestral relative, L1 ORF1p, to retrotranspose in HAP1 human tumor cells. The authors provided insight into the molecular function of L1TD1 and shed some clarifying light on previous studies that showed somewhat contradictory outcomes surrounding L1TD1 expression. Here, L1TD1 expression was correlated with L1 activation in a hypomethylation dependent manner, due to DNMT1 deletion in HAP1 cell line. The authors then identified L1TD1 associated RNAs using RIPSeq, which display a disconnect between transcript and protein abundance (via Tandem Mass Tag multiplex mass spectrometry analysis). The one exception was for L1TD1 itself, is consistent with a model in which the RNA transcripts associated with L1TD1 are not directly regulated at the translation level. Instead, the authors found L1TD1 protein associated with L1-RNPs and this interaction is associated with increased L1 retrotransposition, at least in the contexts of HAP1 cells. Overall, these results support a model in which L1TD1 is restrained by DNA methylation, but in the absence of this repressive mark, L1TD1 is expression, and collaborates with L1 ORF1p (either directly or through interaction with L1 RNA, which remains unclear based on current results), leads to enhances L1 retrotransposition. These results establish feasibility of this relationship existing in vivo in either development or disease, or both.

Comments on revised version:

In general, the authors did an acceptable job addressing the major concerns throughout the manuscript. This revision is much clearer and has improved in terms of logical progression.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have addressed all my questions in the revised version of the manuscript.

Reviewer #2 (Recommendations for the authors):

Revised comments:

A few points we'd like to see addressed are our comments about the model (Figure S7C), as this is important for the readership to understand this complex finding. Please try to apply some quantification, if possible (question 8). Please do your best to tone down the direct relationship of these findings to embryology (question 11). Based on both reviewer comments, we believe addressing reviewer #1s "Suggestions for refinement" (2 points), would help us change our view of solid to convincing.

Responses to changes:

Major

(1) The study only used one knockout (KO) cell line generated by CRISPR/Cas9.

Considering the possibility of an off-target effect, I suggest the authors attempt one or both of these suggestions.

A)  Generate or acquire a similar DMNT1 deletion that uses distinct sgRNAs, so that the likelihood of off-targets is negligible. A few simple experiments such as qRT-PCR would be sufficient to suggest the same phenotype.

B)  Confirm the DNMT1 depletion also by siRNA/ASO KD to phenocopy the KO effect.

(2) In addition to the strategies to demonstrate reproducibility, a rescue experiment restoring DNMT1 to the KO or KD cells would be more convincing. (Partial rescue would suffice in this case, as exact endogenous expression levels may be hard to replicate).

We have undertook several approaches to study the effect of DNMT1 loss or inactivation: As described above, we have generated a conditional KO mouse with ablation of DNMT1 in the epidermis. DNMT1-deficient keratinocytes isolated from these mice show a significant increase in L1TD1 expression. In addition, treatment of primary human keratinocytes and two squamous cell carcinoma cell lines with the DNMT inhibitor aza-deoxycytidine led to upregulation of L1TD1 expression. Thus, the derepression of L1TD1 upon loss of DNMT1 expression or activity is not a clonal effect.

Also, the spectrum of RNAs identified in RIP experiments as L1TD1-associated transcripts in HAP1 DNMT1 KO cells showed a strong overlap with the RNAs isolated by a related yet different method in human embryonic stem cells. When it comes to the effect of L1TD1 on L1-1 retrotranspostion, a recent study has reported a similar effect of L1TD1 upon overexpression in HeLa cells [4].

All of these points together help to convince us that our findings with HAP1 DNMT KO are in agreement with results obtained in various other cell systems and are therefore not due to off-target effects. With that in mind, we would pursue the suggestion of Reviewer 1 to analyze the effects of DNA hypomethylation upon DNMT1 ablation.

Thank you for addressing this concern. The reference to Beck 2021 and the additional cells lines (R2: keratinocytes and R3: squamous cell carcinoma) provides sufficient evidence that this result is unlikely to be a result of clonal expansion or off targets.

Question: Was the human ES Cell RIP Experiment shown here? What is the overlap?

We refer to the recently published study by Jin et al. (PMID: 38165001). As stated in the Discussion, the majority of L1TD1-associated transcripts in HAP1 cells (69%) identified in our study were also reported as L1TD1 targets in hESCs suggesting a conserved binding affinity of this domesticated transposon protein across different cell types.  

(3) As stated in the introduction, L1TD1 and ORF1p share "sequence resemblance" (Martin 2006). Is the L1TD1 antibody specific or do we see L1 ORF1p if Fig 1C were uncropped?

(6) Is it possible the L1TD1 antibody binds L1 ORF1p? This could make Figure 2D somewhat difficult to interpret. Some validation of the specificity of the L1TD1 antibody would remove this concern (see minor concern below).

This is a relevant question. We are convinced that the L1TD1 antibody does not crossreact with L1 ORF1p for the following reasons: Firstly, the antibody does not recognize L1 ORF1p (40 kDa) in the uncropped Western blot for Figure 1C (Figure R4A). Secondly, the L1TD1 antibody gives only background signals in DKO cells in the indirect immunofluorescence experiment shown in Figure 1E of the manuscript.

Thirdly, the immunogene sequence of L1TD1 that determines the specificity of the antibody was checked in the antibody data sheet from Sigma Aldrich. The corresponding epitope is not present in the L1 ORF1p sequence.

Finally, we have shown that the ORF1p antibody does not cross-react with L1TD1 (Figure R4B).

Response: Thank you for sharing these images. These full images relieve concerns about specificity. The increase of ORF1P in R4B and Main figure 3C is interesting and pointed out in the manuscript. Not for the purposes of this review, but the observation of reduced transposition despite increased ORF1P could be an interesting follow up to this study (combined with the similar UPF1 result could indicate a complex of some kind).

(4) In abstract (P2), the authors mentioned that L1TD1 works as an RNA chaperone, but in the result section (P13), they showed that L1TD1 associates with L1 ORF1p in an RNA independent manner. Those conclusions appear contradictory. Clarification or revision is required.

Our findings that both proteins bind L1 RNA, and that L1TD1 interacts with ORF1p are compatible with a scenario where L1TD1/ORF1p heteromultimers bind to L1 RNA. The additional presence of L1TD1 might thereby enhance the RNA chaperone function of ORF1p. This model is visualized now in Suppl. Figure S7C.

Response: Thank you for the model. To further clarify, do you mean that L1TD1 can bind L1 RNA, but this is not needed for the effect, however this "bonus" binding (that is enabled by heteromultimerization) appears to enhance the retrotransposition frequency? Do you think L1TD1 is binding L1 RNA in this context or simply "stabilizing" ORF1P (Trimer) RNP?

Based on our data, L1TD1 associates with L1 RNA and interacts with L1 ORF1p. Both features might contribute to the enhanced retrotransposition frequency. Interestingly, the L1TD1 protein shares with its ancestor L1 ORF1p the non-canonical RNA recognition motif and the coiled-coil motif required for the trimerization but has two copies instead of one of the C-terminal domain (CTD), a structure with RNA binding and chaperone function. We speculate that the presence of an additional CTD within the L1TD1 protein might thereby enhance the RNA binding and chaperone function of L1TD1/ORF1p heteromultimers.

(5) Figure 2C fold enrichment for L1TD1 and ARMC1 is a bit difficult to fully appreciate. A 100 to 200-fold enrichment does not seem physiological. This appears to be a "divide by zero" type of result, as the CT for these genes was likely near 40 or undetectable. Another qRT-PCR based approach (absolute quantification) would be a more revealing experiment. This is the validation of the RIP experiments and the presentation mode is specifically developed for quantification of RIP assays (Sigma Aldrich RIP-qRT-PCR: Data Analysis Calculation Shell). The unspecific binding of the transcript in the absence of L1TD1 in DNMT1/L1TD1 DKO cells is set to 1 and the value in KO cells represents the specific binding relative the unspecific binding. The calculation also corrects for potential differences in the abundance of the respective transcript in the two cell lines. This is not a physiological value but the quantification of specific binding of transcripts to L1TD1. GAPDH as negative control shows no enrichment, whereas specifically associated transcripts show strong enrichement. We have explained the details of RIPqRT-PCR evaluation in Materials and Methods (page 14) and the legend of Figure 2C in the revised manuscript.

Response: Thank you for the clarification and additional information in the manuscript.

(6) Is it possible the L1TD1 antibody binds L1 ORF1p? This could make Figure 2D somewhat difficult to interpret. Some validation of the specificity of the L1TD1 antibody would remove this concern (see minor concern below).

See response to (3).

Response: Thanks.

(7) Figure S4A and S4B: There appear to be a few unusual aspects of these figures that should be pointed out and addressed. First, there doesn't seem to be any ORF1p in the Input (if there is, the exposure is too low). Second, there might be some L1TD1 in the DKO (lane 2) and lane 3. This could be non-specific, but the size is concerning. Overexposure would help see this.

The ORF1p IP gives rise to strong ORF1p signals in the immunoprecipitated complexes even after short exposure. Under these conditions ORF1p is hardly detectable in the input. Regarding the faint band in DKO HAP1 cells, this might be due to a technical problem during Western blot loading. Therefore, the input samples were loaded again on a Western blot and analyzed for the presence of ORF1p, L1TD1 and beta-actin (as loading control) and shown as separate panel in Suppl. Figure S4A.

The enhanced image is clearer. Thanks.

S4A and S4B now appear to the S6A and S6B, is that correct? (This is due to the addition of new S1 and S2, but please verify image orders were not disturbed).

Yes, the input is shown now as a separate panel in Suppl. Figure S6A.

(8) Figure S4C: This is related to our previous concerns involving antibody cross-reactivity. Figure 3E partially addresses this, where it looks like the L1TD1 "speckles" outnumber the ORF1p puncta, but overlap with all of them. This might be consistent with the antibody crossreacting. The western blot (Figure 3C) suggests an upregulation of ORF1p by at least 23x in the DKO, but the IF image in 3E is hard to tell if this is the case (slightly more signal, but fewer foci). Can you return to the images and confirm the contrast are comparable? Can you massively overexpose the red channel in 3E to see if there is residual overlap? In Figure 3E the L1TD1 antibody gives no signal in DNMT1/L1TD1 DKO cells confirming that it does not recognize ORF1p. In agreement with the Western blot in Figure 3C the L1 ORF1p signal in Figure 3E is stronger in DKO cells. In DNMT1 KO cells the L1 ORF1p antibody does not recognize all L1TD1 speckles. This result is in agreement with the Western blot shown above in Figure R4B and indicates that the L1 ORF1p antibody does not recognize the L1TD1 protein. The contrast is comparable and after overexposure there are still L1TD1 specific speckles. This might be due to differences in abundance of the two proteins.

Response: Suggestion: Would it be possible to use a program like ImageJ to supplement the western blot observation? Qualitatively, In figure 3E, it appears that there is more signal in the DKO, but this could also be due to there being multiple cells clustered together or a particularly nicely stained region. Could you randomly sample 20-30 cells across a few experiments to see if this holds up. I am interested in whether the puncta in the KO image(s) is a very highly concentrated region and in the DKO this is more disperse. Also, the representative DKO seems to be cropped slightly wrong. (Please use puncta as a guide to make the cropping more precise)

As suggested by the reviewer we have quantified the signals of 60 KO cells and 56 DKO cells in three different IF experiments by ImageJ. We measured a 1.4-fold higher expression level of L1 ORF1p in DKO cells. However, the difference is not statistically significant. This is most probably due to the change in cell size and protein content during the cell cycle with increasing protein contents from G1 to G2. Western blot analysis provides signals of comparable protein amounts representing an average expression levels over ten thousands of cells. Nevertheless, the quantification results reflect in principle the IF pictures shown in Figure 3E but IF is probably not the best method to quantify protein amounts. We have also corrected Figure 3E.

Author response image 1.

(9) The choice of ARMC1 and YY2 is unclear. What are the criteria for the selection?

ARMC1 was one of the top hits in a pilot RIP-seq experiment (IP versus input and IP versus IgG IP). In the actual RIP-seq experiment with DKO HAP1 cells instead of IgG IP as a negative control, we found ARMC1 as an enriched hit, although it was not among the top 5 hits. The results from the 2nd RIP-seq further confirmed the validity of ARMC1 as an L1TD1interacting transcript. YY2 was of potential biological relevance as an L1TD1 target due to the fact that it is a processed pseudogene originating from YY1 mRNA as a result of retrotransposition. This is mentioned on page 6 of the revised manuscript.

Response: Appreciated!

(10) (P16) L1 is the only protein-coding transposon that is active in humans. This is perhaps too generalized of a statement as written. Other examples are readily found in the literature.

Please clarify.

We will tone down this statement in the revised manuscript.

Response: Appreciated! To further clarify, the term "active" when it comes to transposable elements, has not been solidified. It can span "retrotransposition competent" to "transcripts can be recovered". There are quite a few reports of GAG transcripts and protein from various ERV/LTR subfamilies in various cells and tissues (in mouse and human at least), however whether they contribute to new insertions is actively researched.

(11) In both the abstract and last sentence in the discussion section (P17), embryogenesis is mentioned, but this is not addressed at all in the manuscript. Please refrain from implying normal biological functions based on the results of this study unless appropriate samples are used to support them.

Much of the published data on L1TD1 function are related to embryonic stem cells [3- 7].

Therefore, it is important to discuss our findings in the context of previous reports.

Response: It is well established that embryonic stem cells are not a perfect or direct proxies for the inner cell mass of embryos, as multiple reports have demonstrated transcriptomic, epigenetic, chromatin accessibility differences. The exact origin of ES cells is also considered controversial. We maintain that the distinction between embryos/embryogenesis and the results presented in the manuscript are not yet interchangeable. An important exception would be complex models of embryogenesis such as embryoids, (or synthetic/artificial embryo models that have been carefully been termed as such so as to not suggest direct implications to embryos). https://www.nature.com/articles/ncb2965  

https://link.springer.com/article/10.1007/s00018-018-2965-y  

https://www.cell.com/developmental-cell/abstract/S1534-5807(24)00363-0?_returnURL=https%3A%2F%2Flinkinghub.elsevier.com%2Fretrieve%2Fpii%2FS1534580724003630%3Fshowall%3Dtrue

We have deleted the corresponding paragraph in the Discussion.

(12) Figure 3E: The format of Figures 1A and 3E are internally inconsistent. Please present similar data/images in a cohesive way throughout the manuscript. We show now consistent IF Figures in the revised manuscript.

Response: Thanks

Minor:

In general:

Still need checking for typos, mostly in Materials and Methods section; Please keep a consistent writing style throughout the whole manuscript. If you use L1 ORF1p, then please use L1 instead of LINE-1, or if you keep LINE-1 in your manuscript, then you should use LINE-1 ORF1p.

A lab member from the US checked again the Materials and Methods section for typos. We keep the short version L1 ORF1p.

(1) Intro:

- Is L1Td1 in mice and Humans? How "conserved" is it and does this suggest function? Murine and human L1TD1 proteins share 44% identity on the amino acid level and it was suggested that the corresponding genes were under positive selection during evolution with functions in transposon control and maintenance of pluripotency [8].

- Why HAP1? (Haploid?) The importance of this cell line is not clear.

HAP1 is a nearly haploid human cancer cell line derived from the KBM-7 chronic myelogenous leukemia (CML) cell line [9, 10]. Due to its haploidy is perfectly suited and widely used for loss-of-function screens and gene editing. After gene editing cells can be used in the nearly haploid or in the diploid state. We usually perform all experiments with diploid HAP1 cell lines. Importantly, in contrast to other human tumor cell lines, this cell line tolerates ablation of DNMT1. We have included a corresponding explanation in the revised manuscript on page 5, first paragraph.

- Global methylation status in DNMT1 KO? (Methylations near L1 insertions, for example?)

The HAP1 DNMT1 KO cell line with a 20 bp deletion in exon 4 used in our study was validated in the study by Smits et al. [11]. The authors report a significant reduction in overall DNA methylation. However, we are not aware of a DNA methylome study on this cell line. We show now data on the methylation of L1 elements in HAP1 cells and upon DNMT1 deletion in the revised manuscript in Suppl. Figure S1B.

Response: Looks great!

(2) Figure 1:

- Figure 1C. Why is LMNB used instead of Actin (Fig1D)?

We show now beta-actin as loading control in the revised manuscript.

- Figure 1G shows increased Caspase 3 in KO, while the matching sentence in the result section skips over this. It might be more accurate to mention this and suggest that the single KO has perhaps an intermediate phenotype (Figure 1F shows a slight but not significant trend).

We fully agree with the reviewer and have changed the sentence on page 6, 2nd paragraph accordingly.

- Would 96 hrs trend closer to significance? An interpretation is that L1TD1 loss could speed up this negative consequence.

We thank the reviewer for the suggestion. We have performed a time course experiment with 6 biological replicas for each time point up to 96 hours and found significant changes in the viability upon loss of DNMT1 and again significant reduction in viability upon additional loss of L1TD1 (shown in Figure 1F). These data suggest that as expected loss of DNMT1 leads to significant reduction viability and that additional ablation of L1TD1 further enhances this effect.

Response: Looks good!

- What are the "stringent conditions" used to remove non-specific binders and artifacts (negative control subtraction?)

Yes, we considered only hits from both analyses, L1TD1 IP in KO versus input and L1TD1 IP in KO versus L1TD1 IP in DKO. This is now explained in more detail in the revised manuscript on page 6, 3rd paragraph.

(3) Figure 2:

- Figure 2A is a bit too small to read when printed.

We have changed this in the revised manuscript.

- Since WT and DKO lack detectable L1TD1, would you expect any difference in RIP-Seq results between these two?

Due to the lack of DNMT1 and the resulting DNA hypomethylation, DKO cells are more similar to KO cells than WT cells with respect to the expressed transcripts.

- Legend says selected dots are in green (it appears blue to me). We have changed this in the revised manuscript.

- Would you recover L1 ORF1p and its binding partners in the KO? (Is the antibody specific in the absence of L1TD1 or can it recognize L1?) I noticed an increase in ORF1p in the KO in Figure 3C.

Thank you for the suggestion. Yes, L1 ORF1p shows slightly increased expression in the proteome analysis and we have marked the corresponding dot in the Volcano plot (Figure 3A).

- Should the figure panel reference near the (Rosspopoff & Trono) reference instead be Sup S1C as well? Otherwise, I don't think S1C is mentioned at all.

- What are the red vs. green dots in 2D? Can you highlight ERV and ALU with different colors?

We added the reference to Suppl. Figure S1C (now S3C) in the revised manuscript. In Figure 2D L1 elements are highlighted in green, ERV elements in yellow, and other associated transposon transcripts in red.

Response: Much better, thanks!

- Which L1 subfamily from Figure 2D is represented in the qRT-PCR in 2E "LINE-1"? Do the primers match a specific L1 subfamily? If so, which? We used primers specific for the human L1.2 subfamily.

- Pulling down SINE element transcripts makes some sense, as many insertions "borrow" L1 sequences for non-autonomous retro transposition, but can you speculate as to why ERVs are recovered? There should be essentially no overlap in sequence.

In the L1TD1 evolution paper [8], a potential link between L1TD1 and ERV elements was discussed:

"Alternatively, L1TD1 in sigmodonts could play a role in genome defense against another element active in these genomes. Indeed, the sigmodontine rodents have a highly active family of ERVs, the mysTR elements [46]. Expansion of this family preceded the death of L1s, but these elements are very active, with 3500 to 7000 speciesspecific insertions in the L1-extinct species examined [47]. This recent ERV amplification in Sigmodontinae contrasts with the megabats (where L1TD1 has been lost in many species); there are apparently no highly active DNA or RNA elements in megabats [48]. If L1TD1 can suppress retroelements other than L1s, this could explain why the gene is retained in sigmodontine rodents but not in megabats."

Furthermore, Jin et al. report the binding of L1TD1 to repetitive sequences in transcripts [12]. It is possible that some of these sequences are also present in ERV RNAs.

Response: Interesting, thanks for sharing

- Is S2B a screenshot? (the red underline).

No, it is a Powerpoint figure, and we have removed the red underline.

(4) Figure 3:

- Text refers to Figure 3B as a western blot. Figure 3B shows a volcano plot. This is likely 3C but would still be out of order (3A>3C>3B referencing). I think this error is repeated in the last result section.

- Figure and legends fail to mention what gene was used for ddCT method (actin, gapdh, etc.).

- In general, the supplemental legends feel underwritten and could benefit from additional explanations. (Main figures are appropriate but please double-check that all statistical tests have been mentioned correctly).

Thank you for pointing this out. We have corrected these errors in the revised manuscript.

(5) Discussion:

- Aluy connection is interesting. Is there an "Alu retrotransposition reporter assay" to test whether L1TD1 enhances this as well?

Thank you for the suggestion. There is indeed an Alu retrotransposition reporter assay reported be Dewannieux et al. [13]. The assay is based on a Neo selection marker. We have previously tested a Neo selection-based L1 retrotransposition reporter assay, but this system failed to properly work in HAP1 cells, therefore we switched to a blasticidin based L1 retrotransposition reporter assay. A corresponding blasticidin-based Alu retrotransposition reporter assay might be interesting for future studies (mentioned in the Discussion, page 11 paragraph 4 of the revised manuscript.

(6) Material and Methods :

- The number of typos in the materials and methods is too numerous to list. Instead, please refer to the next section that broadly describes the issues seen throughout the manuscript.

Writing style

(1) Keep a consistent style throughout the manuscript: for example, L1 or LINE-1 (also L1 ORF1p or LINE-1 ORF1p); per or "/"; knockout or knock-out; min or minute; 3 times or three times; media or medium. Additionally, as TE naming conventions are not uniform, it is important to maintain internal consistency so as to not accidentally establish an imprecise version.

(2) There's a period between "et al" and the comma, and "et al." should be italic.

(3) The authors should explain what the key jargon is when it is first used in the manuscript, such as "retrotransposon" and "retrotransposition".

(4) The authors should show the full spelling of some acronyms when they use it for the first time, such as RNA Immunoprecipitation (RIP).

(5) Use a space between numbers and alphabets, such as 5 μg. (6) 2.0 × 105 cells, that's not an "x".

(7) Numbers in the reference section are lacking (hard to parse).

(8) In general, there are a significant number of typos in this draft which at times becomes distracting. For example, (P3) Introduction: Yet, co-option of TEs thorough (not thorough, it should be through) evolution has created so-called domesticated genes beneficial to the gene network in a wide range of organisms. Please carefully revise the entire manuscript for these minor issues that collectively erode the quality of this submission. Thank you for pointing out these mistakes. We have corrected them in the revised manuscript. A native speaker from our research group has carefully checked the paper. In summary, we have added Supplementary Figure S7C and have changed Figures 1C, 1E, 1F, 2A, 2D, 3A, 4B, S3A-D, S4B and S6A based on these comments.

Response: Thank you for taking these comments on board!

Author response:

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

Public Review:

Reviewer #2 (Public Review): 

Regarding reviewer #2 public review, we update here our answers to this public review with new analysis and modification done in the manuscript. 

This manuscript is missing a direct phenotypic comparison of control cells to complement that of cells expressing RhoGEF2-DHPH at "low levels" (the cells that would respond to optogenetic stimulation by retracting); and cells expressing RhoGEF2-DHPH at "high levels" (the cells that would respond to optogenetic stimulation by protruding). In other words, the authors should examine cell area, the distribution of actin and myosin, etc in all three groups of cells (akin to the time zero data from figures 3 and 5, with a negative control). For example, does the basal expression meaningfully affect the PRG low-expressing cells before activation e.g. ectopic stress fibers? This need not be an optogenetic experiment, the authors could express RhoGEF2DHPH without SspB (as in Fig 4G). 

Updated answer: We thank reviewer #2 for this suggestion. PRG-DHPH overexpression is known to affect the phenotype of the cell as shown in Valon et al., 2017. In our experiments, we could not identify any evidence of a particular phenotype before optogenetic activation apart from the area and spontaneous membrane speed that were already reported in our manuscript (Fig 2E and SuppFig 2). Regarding the distribution of actin and myosin, we did not observe an obvious pattern that will be predictive of the protruding/retracting phenotype. Trying to be more quantitative, we have classified (by eye, without knowing the expression level of PRG nor the future phenotype) the presence of stress fibers, the amount of cortical actin, the strength of focal adhesions, and the circularity of cells. As shown below, when these classes are binned by levels of expression of PRG (two levels below the threshold and two above) there is no clear determinant. Thus, we concluded that the main driver of the phenotype was the PRG basal expression rather than any particularity of the actin cytoskeleton/cell shape.

Author response image 1.

Author response image 2.

Relatedly, the authors seem to assume ("recruitment of the same DH-PH domain of PRG at the membrane, in the same cell line, which means in the same biochemical environment." supplement) that the only difference between the high and low expressors are the level of expression. Given the chronic overexpression and the fact that the capacity for this phenotypic shift is not recruitmentdependent, this is not necessarily a safe assumption. The expression of this GEF could well induce e.g. gene expression changes. 

Updated answer: We agree with reviewer #2 that there could be changes in gene expression. In the next point of this supplementary note, we had specified it, by saying « that overexpression has an influence on cell state, defined as protein basal activity or concentration before activation. »  We are sorry if it was not clear, and we changed this sentence in the revised manuscript (in red in the supp note). 

One of the interests of the model is that it does not require any change in absolute concentrations, beside the GEF. The model is thought to be minimal and fits well and explains the data with very few parameters. We do not show that there is no change in concentration, but we show that it is not required to invoke it. We revised a sentence in the new version of the manuscript to include this point.

Additional answer: During the revision process, we have been looking for an experimental demonstration of the independence of the phenotypic switch to any change in global gene expression pattern due to the chronic overexpression of PRG. Our idea was to be in a condition of high PRG overexpression such that cells protrude upon optogenetic activation, and then acutely deplete PRG to see if cells where then retracting. To deplete PRG in a timescale that prevent any change of gene expression, we considered the recently developed CATCHFIRE (PMID: 37640938) chemical dimerizer. We designed an experiment in which the PRG DH-PH domain was expressed in fusion with a FIRE-tag and co-expressing the FIRE-mate fused to TOM20 together with the optoPRG tool. Upon incubation with the MATCH small molecule, we should be able to recruit the overexpressed PRG to the mitochondria within minutes, hereby preventing it to form a complex with active RhoA in the vicinity of the plasma membrane. Unfortunately, despite of numerous trials we never achieved the required conditions: we could not have cells with high enough expression of PRGFIRE-tag (for protrusive response) and low enough expression of optoPRG (for retraction upon PRGFIRE-tag depletion). We still think this would be a nice experiment to perform, but it will require the establishment of a stable cell line with finely tuned expression levels of the CATCHFIRE system that goes beyond the timeline of our present work.      

Concerning the overall model summarizing the authors' observations, they "hypothesized that the activity of RhoA was in competition with the activity of Cdc42"; "At low concentration of the GEF, both RhoA and Cdc42 are activated by optogenetic recruitment of optoPRG, but RhoA takes over. At high GEF concentration, recruitment of optoPRG lead to both activation of Cdc42 and inhibition of already present activated RhoA, which pushes the balance towards Cdc42."

These descriptions are not precise. What is the nature of the competition between RhoA and Cdc42? Is this competition for activation by the GEFs? Is it a competition between the phenotypic output resulting from the effectors of the GEFs? Is it competition from the optogenetic probe and Rho effectors and the Rho biosensors? In all likelihood, all of these effects are involved, but the authors should more precisely explain the underlying nature of this phenotypic switch. Some of these points are clarified in the supplement, but should also be explicit in the main text. 

Updated answer: We consider the competition between RhoA and Cdc42 as a competition between retraction due to the protein network triggered by RhoA (through ROCK-Myosin and mDia-bundled actin) and the protrusion triggered by Cdc42 (through PAK-Rac-ARP2/3-branched Actin). We made this point explicit in the main text.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):  

Major 

- why this is only possible for such few cells. Can the authors comment on this in the discussion? Does the model provide any hints? 

As said in our answer to the public comment or reviewer #1, we think that the low number of cells being able to switch can be explained by two different reasons: 

(1) First, we were looking for clear inversions of the phenotype, where we could see clear ruffles in the case of the protrusion, and clear retractions in the other case. Thus, we discarded cells that would show in-between phenotypes, because we had no quantitative parameter to compare how protrusive or retractile they were. This reduced the number of switching cells 

(2) Second, we had a limitation due to the dynamic of the optogenetic dimer used here. Indeed, the control of the frequency was limited by the dynamic of unbinding of the optogenetic dimer. This dynamic of recruitment (~20s) is comparable to the dynamics of the deactivation of RhoA and Cdc42. Thus, the differences in frequency are smoothed and we could not vary enough the frequency to increase the number of switches. Thanks to the model, we can predict that increasing the unbinding rate of the optogenetic tool (shorter dimer lifetime) should allow us to increase the number of switching cells. 

We have added a sentence in the discussion to make this second point explicit.

- I would encourage the authors to discuss this molecular signaling switch in the context of general design principles of switches. How generalizable is this network/mechanism? Is it exclusive to activating signaling proteins or would it work with inhibiting mechanisms? Is the competition for the same binding site between activators and effectors a common mechanism in other switches? 

The most common design principle for molecular switches is the bistable switch that relies on a nonlinear activation (for example through cooperativity) with a linear deactivation. Such a design allows the switch between low and high levels. In our case, there is no need for a non-linearity since the core mechanism is a competition for the same binding site on active RhoA of the activator and the effectors. Thus, the design principle would be closer to the notion of a minimal “paradoxical component” (PMID: 23352242) that both activate and limit signal propagation, which in our case can be thought as a self-limiting mechanism to prevent uncontrolled RhoA activation by the positive feedback. Yet, as we show in our work, this core mechanism is not enough for the phenotypic switch to happen since the dual activation of RhoA and Cdc42 is ultimately required for the protrusion phenotype to take over the retracting one. Given the particularity of the switch we observed here, we do not feel comfortable to speculate on any general design principles in the main text, but we thank reviewer #1 for his/her suggestion.

- Supplementary figures - there is a discrepancy between the figures called in the text and the supplementary files, which only include SF1-4. 

We apologize for this error and we made the correction. 

- In the text, the authors use Supp Figure 7 to show that the phenotype could not be switched by varying the fold increase of recruitment through changing the intensity/duration of the light pulse. Aside from providing the figure, could you give an explanation or speculation of why? Does the model give any prediction as to why this could be difficult to achieve experimentally (is the range of experimentally feasible fold change of 1.1-3 too small? Also, could you clarify why the range is different than the 3 to 10-fold mentioned at the beginning of the results section? 

We thank the reviewer for this question, and this difference between frequency and intensity can be indeed understood in a simple manner through the model. 

All the reactions in our model were modeled as linear reactions. Thus, at any timepoint, changing the intensity of the pulse will only change proportionally the amount of the different components (amount of active RhoA, amount of sequestered RhoA, and amount of active Cdc42). This explains why we cannot change the balance between RhoA activity and Cdc42 activity only through the pulse strength. We observed the same experimentally: when we changed the intensity of the pulses, the phenotype would be smaller/stronger, but would never switch, supporting our hypothesis on the linearity of all biochemical reactions. 

On the contrary, changing the frequency has an effect, for a simple reason: the dynamics of RhoA and Cdc42 activation are not the same as the dynamics of inhibition of RhoA by the PH domain (see

Figure 4). The inhibition of RhoA by the PH is almost instantaneous while the activation of RhoGTPases has a delay (sets by the deactivation parameter k_2). Intuitively, increasing the frequency will lead to sustained inhibition of RhoA, promoting the protrusion phenotype. Decreasing the frequency – with a stronger pulse to keep the same amount of recruited PRG – restricts this inhibition of RhoA to the first seconds following the activation. The delayed activation of RhoA will then take over. 

We added two sentences in the manuscript to explain in greater details the difference between intensity and frequency.  

Regarding the difference between the 1.3-3 fold and the 3 to 10 fold, the explanation is the following: the 3 to 10 fold referred to the cumulative amount of proteins being recruited after multiple activations (steady state amount reached after 5 minutes with one activation every 30s); while the 1.3-3 fold is what can be obtained after only one single pulse of activation.  

- The transient expression achieves a large range of concentration levels which is a strength in this case. To solve the experimental difficulties associated with this, i.e. finding transfected cells at low cell density, the authors developed a software solution (Cell finder). Since this approach will be of interest for a wide range of applications, I think it would deserve a mention in the discussion part. 

We thank the reviewer for his/her interest in this small software solution.

We developed the description of the tool in the Method section. The Cell finder is also available with comments on github (https://github.com/jdeseze/cellfinder) and usable for anyone using Metamorph or Micromanager imaging software. 

Minor 

- Can the authors describe what they mean with "cell state"? It is used multiple times in the manuscript and can be interpreted as various things. 

We now explain what we mean by ‘cell state’ in the main text :

“protein basal activities and/or concentrations - which we called the cell state”

- “(from 0% to 45%, Figure 2D)", maybe add here: "compare also with Fig. 2A". 

We completed the sentence as suggested, which clarifies the data for the readers.

- The sentence "Given that the phenotype switch appeared to be controlled by the amount of overexpressed optoPRG, we hypothesized that the corresponding leakiness of activity could influence the cell state prior to any activation." might be hard to understand for readers unfamiliar with optogenetic systems. I suggest adding a short sentence explaining dark-state activity/leakiness before putting the hypothesis forward. 

We changed this whole beginning of the paragraph to clarify.

- Figure 2E and SF2A. I would suggest swapping these two panels as the quantification of the membrane displacement before activation seems more relevant in this context. 

We thank reviewer #1 for this suggestion and we agree with it (we swapped the two panels)

- Fig. 2B is missing the white frames in the mixed panels. 

We are sorry for this mistake, we changed it in the new version.  

- In the text describing the experiment of Fig. 4G, it would again be helpful to define what the authors mean by cell state, or to state the expected outcome for both hypotheses before revealing the result.

We added precisions above on what we meant by cell state, which is the basal protein activities and/or concentrations prior to optogenetic activation. We added the expectation as follow: 

To discriminate between these two hypotheses, we overexpressed the DH-PH domain alone in another fluorescent channel (iRFP) and recruited the mutated PH at the membrane. “If the binding to RhoA-GTP was only required to change the cell state, we would expect the same statistics than in Figure 2D, with a majority of protruding cells due to DH-PH overexpression. On the contrary, we observed a large majority of retracting phenotype even in highly expressing cells (Figure 4G), showing that the PH binding to RhoA-GTP during recruitment is a key component of the protruding phenotype.”

- Figure 4H,I: "of cells that overexpress PRG, where we only recruit the PH domain" doesn't match with the figure caption. Are these two constructs in the same cell? If not please clarify the main text. 

We agree that it was not clear. Both constructs are in the same cell, and we changed the figure caption accordingly.  

- "since RhoA dominates Cdc42" is this concluded from experiments (if yes, please refer to the figure) or is this known from the literature (if yes, please cite). 

The assumption that RhoA dominates Cdc42 comes from the fact that we see retraction at low PRG concentration. We assumed that RhoA is responsible for the retraction phenotype. Our assumption is based on the literature (Burridge 2004 as an example of a review, confirmed by many experiments, such as the direct recruitment of RhoA to the membrane, see Berlew 2021) and is supported by our observations of immediate increase of RhoA activity at low PRG. We modified the text to clarify it is an assumption.

- Fig. 6G  o left: is not intuitive, why are the number of molecules different to start with? 

The number of molecules is different because they represent the active molecules: increasing the amount of PRG increases the amount of active RhoA and active Cdc42. We updated the figure to clarify this point.

o right: the y-axis label says "phenotype", maybe change it to "activity" or add a second y-axis on the right with "phenotype"? 

We updated the figure following reviewer #1 suggestion.

- Discussion: "or a retraction in the same region" sounds like in the same cell. Perhaps rephrase to state retraction in a similar region? 

Sorry for the confusion, we change it to be really clear: “a protrusion in the activation region when highly expressed, or a retraction in the activation region when expressed at low concentrations.”

Typos: 

- "between 3 and 10 fold" without s. 

- Fig. 1H, y-axis label. 

- "whose spectrum overlaps" with s. 

- "it first decays, and then rises" with s. 

- Fig 4B and Fig 6B. Is the time in sec or min? (Maybe double-check all figures). 

- "This result suggests that one could switch the phenotype in a single cell by selecting it for an intermediate expression level of the optoPRG.". 

- "GEF-H1 PH domain has almost the same inhibition ability as PRG PH domain". 

We corrected all these mistakes and thank the reviewer for his careful reading of the manuscript.

Reviewer #2 (Recommendations For The Authors): 

Likewise, the model assumes that at high PRG GEF expression, the "reaction is happening far from saturation ..." and that "GTPases activated with strong stimuli -giving rise to strong phenotypic changes- lead to only 5% of the proteins in a GTP-state, both for RhoA and Cdc42". Given the high levels of expression (the absolute value of which is not known) this assumption is not necessarily safe to assume. The shift to Cdc42 could indeed result from the quantitative conversion of RhoA into its active state. 

We agree with the reviewer that the hypothesis that RhoA is fully converted into its active state cannot be completely ruled out. However, we think that the two following points can justify our choice.

- First, we see that even in the protruding phenotype, RhoA activity is increasing upon optoPRG recruitment (Figure 3). This means that RhoA is not completely turned into its active GTP-loaded state. The biosensor intensity is rising by a factor 1.5 after 5 minutes (and continue to increase, even if not shown here). For sure, it could be explained by the relocation of RhoA to the place of activation, but it still shows that cells with high PRG expression are not completely saturated in RhoA-GTP. 

- We agree that linearity (no saturation) is still an hypothesis and very difficult to rule out, because it is not only a question of absolute concentrations of GEFs and RhoA, but also a question of their reaction kinetics, which are unknow parameters in vivo. Yet, adding a saturation parameter would mean adding 3 unknown parameters (absolute concentrations of RhoA, as well as two reaction constants). The fact that there are not needed to fit the complex curves of RhoA as we do with only one parameter tends to show that the minimal ingredients representing the interaction are captured here.  

The observed "inhibition of RhoA by the PH domain of the GEF at high concentrations" could result from the ability of the probe to, upon membrane recruitment, bind to active RhoA (via its PH domain) thereby outcompeting the RhoA biosensor (Figure 4A-C). This reaction is explicitly stated in the supplemental materials ("PH domain binding to RhoA-GTP is required for protruding phenotype but not sufficient, and it is acting as an inhibitor of RhoA activity."), but should be more explicit in the main text. Indeed, even when PRG DHPH is expressed at high concentrations, it does activate RhoA upon recruitment (figure 3GH). Not only might overexpression of this active RhoA-binding probe inhibit the cortical recruitment of the RhoA biosensor, but it may also inhibit the ability of active RhoA to activate its downstream effectors, such as ROCK, which could explain the decrease in myosin accumulation (figure 3D-F). It is not clear that there is a way to clearly rule this out, but it may impact the interpretation. 

This hypothesis is actually what we claim in the manuscript. We think that the inhibition of RhoA by the PH domain is explained by its direct binding. We may have missed what Reviewer #2 wanted to say, but we think that we state it explicitly in the main text :

“Knowing that the PH domain of PRG triggers a positive feedback loop thanks to its binding to active RhoA 18, we hypothesized that this binding could sequester active RhoA at high optoPRG levels, thus being responsible for its inhibition.”

And also in the Discussion:

“However, this feedback loop can turn into a negative one for high levels of GEF: the direct interaction between the PH domain and RhoA-GTP prevents RhoA-GTP binding to effectors through a competition for the same binding site.”

We may have not been clear, but we think that this is what is happening: the PH domain prevents the binding to effectors and decreases RhoA activity (as was shown in Chen et al. 2010).  

The X-axis in Figure 4C time is in seconds not minutes. The Y-axis in Figure 4H is unlabeled. 

We are sorry for the mistake of Figure 4C. We changed the Y-axis in the Figure 4h.  

Although this publication cites some of the relevant prior literature, it fails to cite some particularly relevant works. For example, the authors state, "The LARG DH domain was already used with the iLid system" and refers to a 2018 paper (ref 19), whereas that domain was first used in 2016 (PMID 27298323). Indeed, the authors used the plasmid from this 2016 paper to build their construct. 

We thank the reviewer for pointing out this error, we have corrected the citation and put the seminal one in the revised version.

An analogous situation pertains to previous work that showed that an optogenetic probe containing the DH and PH domains in RhoGEF2 is somewhat toxic in vivo (table 6; PMID 33200987). Furthermore, it has previously been shown that mutation of the equivalent of F1044A and I1046E eliminates this toxicity (table 6; PMID 33200987) in vivo. This is particularly important because the Rho probe expressing RhoGEF2-DHPH is in widespread usage (76 citations in PubMed). The ability of this probe to activate Cdc42 may explain some of the phenotypic differences described resulting from the recruitment of RhoGEF2-DHPH and LARG-DH in a developmental context (PMID 29915285, 33200987). 

We thank reviewer #2 for these comments, and added a small section in the discussion, for optogenetic users: 

This underlines the attention that needs to be paid to the choice of specific GEF domains when using optogenetic tools. Tools using DH-PH domains of PRG have been widely used, both in mammalian cells and in Drosophila (with the orthologous gene RhoGEF2), and have been shown to be toxic in some contexts in vivo 28. Our study confirms the complex behavior of this domain which cannot be reduced to a simple RhoA activator.   

Concerning the experiment shown in 4D, it would be informative to repeat this experiment in which a non-recruitable DH-PH domain of PRG is overexpressed at high levels and the DH domain of LARG is recruited. This would enable the authors to distinguish whether the protrusion response is entirely dependent on the cell state prior to activation or the combination of the cell state prior to activation and the ability of PRG DHPH to also activate Cdc42. 

We thank the reviewer for his suggestion. Yet, we think that we have enough direct evidence that the protruding phenotype is due to both the cell state prior to activation and the ability of PRG DHPH to also activate Cdc42. First, we see a direct increase in Cdc42 activity following optoPRG recruitment (see Figure 6). This increase is sustained in the protruding phenotype and precedes Rac1 and RhoA activity, which shows that it is the first of these three GTPases to be activated. Moreover, we showed that inhibition of PAK by the very specific drug IPA3 is completely abolishing only the protruding phenotype, which shows that PAK, a direct effector of Cdc42 and Rac1, is required for the protruding phenotype to happen. We know also that the cell state prior to activation is defining the phenotype, thanks to the data presented in Figure 2. 

We further showed in Figure 1 that LARG DH-PH domain was not able to promote protrusion. The proposed experiment would be interesting to confirm that LARG does not have the ability to activate another GTPase, even in a different cell state with overexpressed PRG. However, we are not sure it would bring any substantial findings to understand the mechanism we describe here, given the facts provided above.  

Similarly, as PRG activates both Cdc42 and Rho at high levels, it would be important to determine the extent to which the acute Rho activation contributes to the observed phenotype (e.g. with Rho kinase inhibitor). 

We agree with the reviewer that it would be interesting to know whether RhoA activation contributes to the observed phenotype, and we have tried such experiments. 

For Rho kinase inhibitor, we tried with Y-27632 and we could never prevent the protruding phenotype to happen. However, we could not completely abolish the retracting phenotype either (even when the effect on the cells was quite strong and visible), which could be due to other effectors compensating for this inhibition. As RhoA has many other effectors, it does not tell us that RhoA is not required for protrusion. 

We also tried with C3, which is a direct inhibitor of RhoA. However, it had too much impact on the basal state of the cells, making it impossible to recruit (cells were becoming round and clearly dying. As both the basal state and optogenetic activation require the activation of RhoA, it is hard to conclude out of experiments where no cell is responding. 

The ability of PRG to activate Cdc42 in vivo is striking given the strong preference for RhoA over Cdc42 in vitro (2400X) (PMID 23255595). Is it possible that at these high expression levels, much of the RhoA in the cell is already activated, so that the sole effect that recruited PRG can induce is activation of Cdc42? This is related to the previous point pertaining to absolute expression levels.  

As discussed before, we think that it is not only a question of absolute expression levels, but also of the affinities between the different partners. But Reviewer #2 is right, there is a competition between the activation of RhoA and Cdc42 by optoPRG, and activation of Cdc42 probably happens at higher concentration because of smaller effective affinity.

Still, we know that activation of the Cdc42 by PRG DH-PH domain is possible in vivo, as it was very clearly shown in Castillo-Kauil et al., 2020 (PMID 33023908). They show that this activation requires the linker between DH and PH domain of PRG, as well as Gαs activation, which requires a change in PRG DH-PH conformation. This conformational switch does not happen in vitro, which might explain why the affinity against Cdc42 was found to be very low. 

Minor points 

In both the abstract and the introduction the authors state, "we show that a single protein can trigger either protrusion or retraction when recruited to the plasma membrane, polarizing the cell in two opposite directions." However, the cells do not polarize in opposite directions, ie the cells that retract do not protrude in the direction opposite the retraction (or at least that is not shown). Rather a single protein can trigger either protrusion or retraction when recruited to the plasma membrane, depending upon expression levels. 

We thank the reviewer for this remark, and we agree that we had not shown any data supporting a change in polarization. We solved this issue, by showing now in Supplementary Figure 1 the change in areas in both the activated and in the not activated region. The data clearly show that when a protrusion is happening, the cell retracts in the non-activated region. On the other hand, when the cell retracts, a protrusion happens in the other part of the cell, while the total area is staying approximately constant. 

We added the following sentence to describe our new figure:

Quantification of the changes in membrane area in both the activated and non-activated part of the cell (Supp Figure 1B-C) reveals that the whole cell is moving, polarizing in one direction or the other upon optogenetic activation.

While the authors provide extensive quantitative data in this manuscript and quantify the relative differences in expression levels that result in the different phenotypes, it would be helpful to quantify the absolute levels of expression of these GEFs relative to e.g. an endogenously expressed GEF. 

We agree with the reviewer comment, and we also wanted to have an idea of the absolute level of expression of GEFs present in these cells to be able to relate fluorescent intensities with absolute concentrations. We tried different methods, especially with the purified fluorescent protein, but having exact numbers is a hard task.

We ended up quantifying the amount of fluorescent protein within a stable cell line thanks to ELISA and comparing it with the mean fluorescence seen under the microscope. 

We estimated that the switch concentration was around 200nM, which is 8 times more than the mean endogenous concentration according to https://opencell.czbiohub.org/, but should be reachable locally in wild type cell, or globally in mutated cancer cells. 

Given the numerical data (mostly) in hand, it would be interesting to determine whether RhoGEF2 levels, cell area, the pattern of actin assembly, or some other property is most predictive of the response to PRG DHPH recruitment. 

We think that the manuscript made it clear that the concentration of PRG DHPH is almost 100% predictive of the response to PRG DHPH. We believe that other phenotypes such as the cell area or the pattern of actin assembly would only be consequences of this. Interestingly, as experimentators we were absolutely not able to predict the behavior by only seeing the shape of the cell, event after hundreds of activation experiments, and we tried to find characteristics that would distinguish both populations with the data in our hands and could not find any.

There is some room for general improvement/editing of the text. 

We tried our best to improve the text, following reviewers suggestions.

Author response:

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

Reviewer #2:

(1) The use of two m⁵C reader proteins is likely a reason for the high number of edits introduced by the DRAM-Seq method. Both ALYREF and YBX1 are ubiquitous proteins with multiple roles in RNA metabolism including splicing and mRNA export. It is reasonable to assume that both ALYREF and YBX1 bind to many mRNAs that do not contain m⁵C.

To substantiate the author's claim that ALYREF or YBX1 binds m⁵C-modified RNAs to an extent that would allow distinguishing its binding to non-modified RNAs from binding to m⁵C-modified RNAs, it would be recommended to provide data on the affinity of these, supposedly proven, m⁵C readers to non-modified versus m⁵C-modified RNAs. To do so, this reviewer suggests performing experiments as described in Slama et al., 2020 (doi: 10.1016/j.ymeth.2018.10.020). However, using dot blots like in so many published studies to show modification of a specific antibody or protein binding, is insufficient as an argument because no antibody, nor protein, encounters nanograms to micrograms of a specific RNA identity in a cell. This issue remains a major caveat in all studies using so-called RNA modification reader proteins as bait for detecting RNA modifications in epitranscriptomics research. It becomes a pertinent problem if used as a platform for base editing similar to the work presented in this manuscript.

The authors have tried to address the point made by this reviewer. However, rather than performing an experiment with recombinant ALYREF-fusions and m⁵C-modified to unmodified RNA oligos for testing the enrichment factor of ALYREF in vitro, the authors resorted to citing two manuscripts. One manuscript is cited by everybody when it comes to ALYREF as m⁵C reader, however none of the experiments have been repeated by another laboratory. The other manuscript is reporting on YBX1 binding to m⁵C-containing RNA and mentions PAR-CLiP experiments with ALYREF, the details of which are nowhere to be found in doi: 10.1038/s41556-019-0361-y.<br /> Furthermore, the authors have added RNA pull-down assays that should substitute for the requested experiments. Interestingly, Figure S1E shows that ALYREF binds equally well to unmodified and m⁵C-modified RNA oligos, which contradicts doi:10.1038/cr.2017.55, and supports the conclusion that wild-type ALYREF is not specific m⁵C binder. The necessity of including always an overexpression of ALYREF-mut in parallel DRAM experiments, makes the developed method better controlled but not easy to handle (expression differences of the plasmid-driven proteins etc.)

Thank you for pointing this out. First, we would like to correct our previous response: the binding ability of ALYREF to m⁵C-modified RNA was initially reported in doi: 10.1038/cr.2017.55, (and not in doi: 10.1038/s41556-019-0361-y), where it was observed through PAR-CLIP analysis that the K171 mutation weakens its binding affinity to m⁵C -modified RNA.

Our previous experimental approach was not optimal: the protein concentration in the INPUT group was too high, leading to overexposure in the experimental group. Additionally, we did not conduct a quantitative analysis of the results at that time. In response to your suggestion, we performed RNA pull-down experiments with YBX1 and ALYREF, rather than with the pan-DRAM protein, to better validate and reproduce the previously reported findings. Our quantitative analysis revealed that both ALYREF and YBX1 exhibit a stronger affinity for m⁵C -modified RNAs. Furthermore, mutating the key amino acids involved in m⁵C recognition significantly reduced the binding affinity of both readers. These results align with previous studies (doi: 10.1038/cr.2017.55 and doi: 10.1038/s41556-019-0361-y), confirming that ALYREF and YBX1 are specific readers of m⁵C -modified RNAs. However, our detection system has certain limitations. Despite mutating the critical amino acids, both readers retained a weak binding affinity for m⁵C, suggesting that while the mutation helps reduce false positives, it is still challenging to precisely map the distribution of m⁵C modifications. To address this, we plan to further investigate the protein structure and function to obtain a more accurate m⁵C sequencing of the transcriptome in future studies. Accordingly, we have updated our results and conclusions in lines 294-299 and discuss these limitations in lines 109-114.

In addition, while the m⁵C assay can be performed using only the DRAM system alone, comparing it with the DRAM^mutC control enhances the accuracy of m⁵C region detection. To minimize the variations in transfection efficiency across experimental groups, it is recommended to use the same batch of transfections. This approach not only ensures more consistent results but also improve the standardization of the DRAM assay, as discussed in the section added on line 308-312.

(2) Using sodium arsenite treatment of cells as a means to change the m⁵C status of transcripts through the downregulation of the two major m⁵C writer proteins NSUN2 and NSUN6 is problematic and the conclusions from these experiments are not warranted. Sodium arsenite is a chemical that poisons every protein containing thiol groups. Not only do NSUN proteins contain cysteines but also the base editor fusion proteins. Arsenite will inactivate these proteins, hence the editing frequency will drop, as observed in the experiments shown in Figure 5, which the authors explain with fewer m⁵C sites to be detected by the fusion proteins.

The authors have not addressed the point made by this reviewer. Instead the authors state that they have not addressed that possibility. They claim that they have revised the results section, but this reviewer can only see the point raised in the conclusions. An experiment would have been to purify base editors via the HA tag and then perform some kind of binding/editing assay in vitro before and after arsenite treatment of cells.

We appreciate the reviewer’s insightful comment. We fully agree with the concern raised. In the original manuscript, our intention was to use sodium arsenite treatment to downregulate NSUN mediated m⁵C levels and subsequently decrease DRAM editing efficiency, with the aim of monitoring m⁵C dynamics through the DRAM system. However, as the reviewer pointed out, sodium arsenite may inactivate both NSUN proteins and the base editor fusion proteins, and any such inactivation would likely result in a reduced DRAM editing. This confounds the interpretation of our experimental data.

As demonstrated in Appendix A, western blot analysis confirmed that sodium arsenite indeed decreased the expression of fusion proteins. In addition, we attempted in vitro fusion protein purification using multiple fusion tags (HIS, GST, HA, MBP) for DRAM fusion protein expression, but unfortunately, we were unable to obtain purified proteins. However, using the Promega TNT T7 Rapid Coupled In Vitro Transcription/Translation Kit, we successfully purified the DRAM protein (Appendix B). Despite this success, subsequent in vitro deamination experiments did not yield the expected mutation results (Appendix C), indicating that further optimization is required. This issue is further discussed in line 314-315.

Taken together, the above evidence supports that the experiment of sodium arsenite treatment was confusing and we determined to remove the corresponding results from the main text of the revised manuscript.

Author response image 1.

(3) The authors should move high-confidence editing site data contained in Supplementary Tables 2 and 3 into one of the main Figures to substantiate what is discussed in Figure 4A. However, the data needs to be visualized in another way then excel format. Furthermore, Supplementary Table 2 does not contain a description of the columns, while Supplementary Table 3 contains a single row with letters and numbers.

The authors have not addressed the point made by this reviewer. Figure 3F shows the screening process for DRAM-seq assays and principles for screening high-confidence genes rather than the data contained in Supplementary Tables 2 and 3 of the former version of this manuscript.

Thank you for your valuable suggestion. We have visualized the data from Supplementary Tables 2 and 3 in Figure 4A as a circlize diagram (described in lines 213-216), illustrating the distribution of mutation sites detected by the DRAM system across each chromosome. Additionally, to improve the presentation and clarity of the data, we have revised Supplementary Tables 2 and 3 by adding column descriptions, merging the DRAM-ABE and DRAM-CBE sites, and including overlapping m⁵C genes from previous datasets.

Author response:

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

Public Reviews:

Reviewer #2 (Public Review):

Summary:

The manuscript by Kelbert et al. presents results on the involvement of the yeast transcription factor Sfp1 in the stabilisation of transcripts whose synthesis it stimulates. Sfp1 is known to affect the synthesis of a number of important cellular transcripts, such as many of those that code for ribosomal proteins. The hypothesis that a transcription factor can remain bound to the nascent transcript and affect its cytoplasmic half-life is attractive. However, the association of Sfp1 with cytoplasmic transcripts remains to be validated, as explained in the following comments:

A two-hybrid based assay for protein-protein interactions identified Sfp1, a transcription factor known for its effects on ribosomal protein gene expression, as interacting with Rpb4, a subunit of RNA polymerase II. Classical two-hybrid experiments depend on the presence of the tested proteins in the nucleus of yeast cells, suggesting that the observed interaction occurs in the nucleus. Unfortunately, the two-hybrid method cannot determine whether the interaction is direct or mediated by nucleic acids. The revised version of the manuscript now states that the observed interaction could be indirect.

To understand to which RNA Sfp1 might bind, the authors used an N-terminally tagged fusion protein in a cross-linking and purification experiment. This method identified 264 transcripts for which the CRAC signal was considered positive and which mostly correspond to abundant mRNAs, including 74 ribosomal protein mRNAs or metabolic enzyme-abundant mRNAs such as PGK1. The authors did not provide evidence for the specificity of the observed CRAC signal, in particular what would be the background of a similar experiment performed without UV cross-linking. This is crucial, as Figure S2G shows very localized and sharp peaks for the CRAC signal, often associated with over-amplification of weak signal during sequencing library preparation.

(1) To rule out possible PCR artifacts, we used a UMI (Unique Molecular Identifier) scan. UMIs are short, random sequences added to each molecule by the 5’ adapter to uniquely tag them. After PCR amplification and alignment to the reference genome, groups of reads with identical UMIs represent only one unique original molecule. Thus, UMIs allow distinguishing between original molecules and PCR duplicates, effectively eliminating the duplicates.

(2) Looking closely at the peaks using the IGV browser, we noticed that the reads are by no means identical. Each carrying a mutation [probably due to the cross-linking] in a different position and having different length. Note that the reads are highly reproducible in two replicate.

(3) CRAC+ genes do not all fall into the category of highly transcribed genes.  On the contrary, as depicted in Figure 6A (green dots), it is evident that CRAC+ genes exhibit a diverse range of Rpb3 ChIP and GRO signals. Furthermore, as illustrated in Figure 7A, when comparing CRAC+ to Q1 (the most highly transcribed genes), it becomes evident that the Rpb4/Rpb3 profile of CRAC+ genes is not a result of high transcription levels.

(4) Only a portion of the RiBi mRNAs binds Sfp1, despite similar expression of all RiBi.

(5) The CRAC+ genes represent a distinct group with many unique features. Moreover, many CRAC+ genes do not fall into the category of highly transcribed genes.

(6) The biological significance of the 262 CRAC+ mRNAs was demonstrated by various experiments; all are inconsistent with technical flaws. Some examples are:

a) Fig. 2a and B show that most reads of CRAC+ mRNA were mapped to specific location – close the pA sites.

b) Fig. 2C shows that most reads of CRAC+ mRNA were mapped to specific RNA motif.

c) Most RiBi CRAC+ promoter contain Rap1 binding sites (p= 1.9x10-22), whereas the vast majority of RiBi CRAC- promoters do not contain Rap1 binding site. (Fig. 3C).

d) Fig. 4A shows that RiBi CRAC+ mRNAs become destabilized due to Sfp1 deletion, whereas RiBi CRAC- mRNAs do not. Fig. 4B shows similar results due to

e) Fig. 6B shows that the impact of Sfp1 on backtracking is substantially higher for CRAC+ than for CRAC- genes. This is most clearly visible in RiBi genes.

f) Fig. 7A shows that the Sfp1-dependent changes along the transcription units is substantially more rigorous for CRAC+ than for CRAC-.

g) Fig. S4B Shows that chromatin binding profile of Sfp1 is different for CRAC+ and CRAC- genes

In a validation experiment, the presence of several mRNAs in a purified SFP1 fraction was measured at levels that reflect the relative levels of RNA in a total RNA extract. Negative controls showing that abundant mRNAs not found in the CRAC experiment were clearly depleted from the purified fraction with Sfp1 would be crucial to assess the specificity of the observed protein-RNA interactions (to complement Fig. 2D).

GPP1, a highly expressed genes, is not to be pulled down by Sfp1 (Fig. 2D). GPP1 (alias RHR2) was included in our Table S2 as one of the 264 CRAC+ genes, having a low CRAC value. However, when we inspected GPP1 results using the IGV browser, we realized that the few reads mapped to GPP1 are actually anti-sense to GPP1 (perhaps they belong to the neighboring RPL34B genes, which is convergently transcribed to GPP1) (see Fig. 1 at the bottom of the document). Thus, GPP1 is not a CRAC+ gene and would now serve as a control. See  We changed the text accordingly (see page 11 blue sentences). In light of this observation, we checked other CRAC genes and found that, except for ALG2, they all contain sense reads (some contain both sense and anti-sense reads). ALG2 and GPP1 were removed leaving 262 CRAC+ genes.

The CRAC-selected mRNAs were enriched for genes whose expression was previously shown to be upregulated upon Sfp1 overexpression (Albert et al., 2019). The presence of unspliced RPL30 pre-mRNA in the Sfp1 purification was interpreted as a sign of co-transcriptional assembly of Sfp1 into mRNA, but in the absence of valid negative controls, this hypothesis would require further experimental validation. Also, whether the fraction of mRNA bound by Sfp1 is nuclear or cytoplasmic is unclear.

Further experimental validation was provided in some of our figures (e.g., Fig. 5C, Fig. 3B).

We argue that Sfp1 binds RNA co-transcriptionally and accompanies the mRNA till its demise in the cytoplasm: Co-transcriptional binding is shown in: (I) a drop in the Sfp1 ChIP-exo signal that coincides with the position of Sfp1 binding site in the RNA (Fig. 5C), demonstrating a movement of Sfp1 from chromatin to the transcript, (II) the dependence of Sfp1 RNA-binding on the promoter (Fig. 3B) and binding of intron-containing RNA. Taken together these 3 different experiments demonstrate that Sfp1 binds Pol II transcript co-transcriptionally.  Association of Sfp1 with cytoplasmic mRNAs is shown in the following experiments: (I) Figure 2D shows that Sfp1 pulled down full length RNA, strongly suggesting that these RNA are mature cytoplasmic mRNAs. (II) mRNA encoding ribosomal proteins, which belong to the CRAC+ mRNAs group are degraded by Xrn1 in the cytoplasm (Bresson et al., Mol Cell 2020). The capacity of Sfp1 to regulates this process (Fig. 4A-D) is therefore consistent with cytoplasmic activity of Sfp1. (III) The effect of Sfp1 on deadenylation (Fig. 4D), a cytoplasmic process, is also consistent with cytoplasmic activity of Sfp1. 

To address the important question of whether co-transcriptional assembly of Spf1 with transcripts could alter their stability, the authors first used a reporter system in which the RPL30 transcription unit is transferred to vectors under different transcriptional contexts, as previously described by the Choder laboratory (Bregman et al. 2011). While RPL30 expressed under an ACT1 promoter was barely detectable, the highest levels of RNA were observed in the context of the native upstream RPL30 sequence when Rap1 binding sites were also present. Sfp1 showed better association with reporter mRNAs containing Rap1 binding sites in the promoter region. Removal of the Rap1 binding sites from the reporter vector also led to a drastic decrease in reporter mRNA levels. Co-purification of reporter RNA with Sfp1 was only observed when Rap1 binding sites were included in the reporter. Negative controls for all the purification experiments might be useful.

In the swapping experiment, the plasmid lacking RapBS serves as the control for the one with RapBS and vice versa (see Bregman et al., 2011). Remember, that all these contracts give rise to identical RNA. Indeed, RabBS affects both mRNA synthesis and decay, therefore the controls are not ideal. However, see next section.

More importantly, in Fig. 3B “Input” panel, one can see that the RNA level of “construct F” was higher than the level of “construct E”. Despite this difference, only the RNA encoded by construct E was detected in the IP panel. This clearly shows that the detection of the RNA was not merely a result of its expression level.

To complement the biochemical data presented in the first part of the manuscript, the authors turned to the deletion or rapid depletion of SFP1 and used labelling experiments to assess changes in the rate of synthesis, abundance and decay of mRNAs under these conditions. An important observation was that in the absence of Sfp1, mRNAs encoding ribosomal protein genes not only had a reduced synthesis rate, but also an increased degradation rate. This important observation needs careful validation,

Indeed, we do provide validations in Fig. 4C Fig. 4D Fig. S3A and during the revision we included an  additional validation as Fig. S3B. Of note, we strongly suspect that GRO is among the most reliable approaches to determine half-lives (see our response in the first revision letter).

As genomic run-on experiments were used to measure half-lives, and this particular method was found to give results that correlated poorly with other measures of half-life in yeast (e.g. Chappelboim et al., 2022 for a comparison). As an additional validation, a temperature shift to 42{degree sign}C was used to show that , for specific ribosomal protein mRNA, the degradation was faster, assuming that transcription stops at that temperature. It would be important to cite and discuss the work from the Tollervey laboratory showing that a temperature shift to 42{degree sign}C leads to a strong and specific decrease in ribosomal protein mRNA levels, probably through an accelerated RNA degradation (Bresson et al., Mol Cell 2020, e.g. Fig 5E).

This was cited. Thank you. 

Finally, the conclusion that mRNA deadenylation rate is altered in the absence of Sfp1, is difficult to assess from the presented results (Fig. 3D).

This type of experiment was popular in the past. The results in the literature are similar to ours (in fact, ours are nicer). Please check the papers cited in our MS and a number of papers by Roy Parker.

The effects of SFP1 on transcription were investigated by chromatin purification with Rpb3, a subunit of RNA polymerase, and the results were compared with synthesis rates determined by genomic run-on experiments. The decrease in polII presence on transcripts in the absence of SFP1 was not accompanied by a marked decrease in transcript output, suggesting an effect of Sfp1 in ensuring robust transcription and avoiding RNA polymerase backtracking. To further investigate the phenotypes associated with the depletion or absence of Sfp1, the authors examined the presence of Rpb4 along transcription units compared to Rpb3. An effect of spf1 deficiency was that this ratio, which decreased from the start of transcription towards the end of transcripts, increased slightly. To what extent this result is important for the main message of the manuscript is unclear.

Suggestions: a) please clearly indicate in the figures when they correspond to reanalyses of published results.

This was done.

b) In table S2, it would be important to mention what the results represent and what statistics were used for the selection of "positive" hits. 

This was discussed in the text.

Strengths:

- Diversity of experimental approaches used.

- Validation of large-scale results with appropriate reporters.

Weaknesses:

- Lack of controls for the CRAC results and lack of negative controls for the co-purification experiments that were used to validate specific mRNA targets potentially bound by Sfp1.

- Several conclusions are derived from complex correlative analyses that fully depend on the validity of the aforementioned Sfp1-mRNA interactions.

We hope that our responses to Reviewer 2's thoughtful comments have rulled out concerns regarding the lack of controls.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Please review the text for spelling errors. While not mandatory, wig or begraph files for the CRAC results would be very useful for the readers.

Author response image 1.

A snapshot of IGV GPP1 locus showing that all the reads are anti-sense (pointing at the opposite direction of the gene (the gene arrows [white arrows over blue, at the bottom] are pointing to the right whereas the reads’ orientations are pointing to the left).

Author Response

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

eLife assessment

This research advance arctile describes a valuable image analysis method to identify individual cells (neurons) within a population of fluorescently labeled cells in the nematode C. elegans. The findings are solid and the method succeeds to identify cells with high precision. The method will be valuable to the C. elegans research community.

Public Reviews:

Reviewer #1 (Public Review):

In this paper, the authors developed an image analysis pipeline to automatically identify individual neurons within a population of fluorescently tagged neurons. This application is optimized to deal with multi-cell analysis and builds on a previous software version, developed by the same team, to resolve individual neurons from whole-brain imaging stacks. Using advanced statistical approaches and several heuristics tailored for C. elegans anatomy, the method successfully identifies individual neurons with a fairly high accuracy. Thus, while specific to C. elegans, this method can become instrumental for a variety of research directions such as in-vivo single-cell gene expression analysis and calcium-based neural activity studies.

The analysis procedure depends on the availability of an accurate atlas that serves as a reference map for neural positions. Thus, when imaging a new reporter line without fair prior knowledge of the tagged cells, such an atlas may be very difficult to construct. Moreover, usage of available reference atlases, constructed based on other databases, is not very helpful (as shown by the authors in Fig 3), so for each new reporter line a de-novo atlas needs to be constructed.

We thank the reviewer for pointing out a place where we can use some clarification. While in principle that every new reporter line would need fair prior knowledge, atlases are either already available or not difficult to construct. If one can make the assumption that the anatomy of a particular line is similar to existing atlases (Yemini 2021,Nejatbakhsh 2023,Toyoshima 2020), the cell ID can be immediately performed. Even in the case that one suspects the anatomy may have changes from existing atlases (e.g. in the case of examining mutants), existing atlases can serve as a starting point to provide a draft ID, which facilitates manual annotation. Once manual annotations on ~5 animals are available as we have shown in this work (which is a manageable number in practice), this new dataset can be used to build an updated atlas that can be used for future inferences. We have added this discussion in the manuscript: “If one determines that the anatomy of a particular animal strain is substantially different from existing atlases, new atlases can be easily constructed using existing atlases as starting points.” (page 18).

I have a few comments that may help to better understand the potential of the tool to become handy.

1. I wonder the degree by which strain mosaicism affects the analysis (Figs 1-4) as it was performed on a non-integrated reporter strain. As stated, for constructing the reference atlas, the authors used worms in which they could identify the complete set of tagged neurons. But how senstiive is the analysis when assaying worms with different levels of mosaicism? Are the results shown in the paper stem from animals with a full neural set expression? Could the authors add results for which the assayed worms show partial expression where only 80%, 70%, 50% of the cells population are observed, and how this will affect idenfication accuracy? This may be important as many non-integrated reporter lines show high mosaic patterns and may therefore not be suitable for using this analytic method. In that sense, could the authors describe the mosaic degree of their line used for validating the method.

We appreciate the reviewer for this comment. We want to clarify that most of the worms used in the construction of the atlas are indeed affected by mosaicism and thus do not express the full set of candidate neurons. We have added such a plot as requested (Figure 3 – figure supplement 2, copied below). Our data show that there is no correlation between the fraction of cells expressed in a worm and neuron ID correspondence. We agree with the reviewer this additional insight may be helpful; we have modified the text to include this discussion: “Note that we observed no correlation between the degree of mosaicism and neuron ID correspondence (Figure 3- figure supplement 2).” (page 10).

Author response image 1.

No correlation between the degree of mosaicism (fraction of cells expressed in the worm) and neuron ID correspondence.

1. For the gene expression analysis (Fig 5), where was the intensity of the GFP extracted from? As it has no nuclear tag, the protein should be cytoplasmic (as seen in Fig 5a), but in Fig 5c it is shown as if the region of interest to extract fluorescence was nuclear. If fluorescence was indeed extracted from the cytoplasm, then it will be helpful to include in the software and in the results description how this was done, as a huge hurdle in dissecting such multi-cell images is avoiding crossreads between adjacent/intersecting neurons.

For this work, we used nuclear-localized RFP co-expressed in the animal, and the GFP intensities were extracted from the same region RFP intensities were extracted. If cytosolic reporters are used, one would imagine a membrane label would be necessary to discern the border of the cells. We clarified our reagents and approach in the text: “The segmentation was done on the nuclear-localized mCherry signals, and GFP intensities were extracted from the same region.” (page21).

1. In the same mater: In the methods, it is specified that the strain expressing GCAMP was also used in the gene expression analysis shown in Figure 5. But the calcium indicator may show transient intensities depending on spontaneous neural activity during the imaging. This will introduce a significant variability that may affect the expression correlation analysis as depicted in Figure 5.

We apologize for the error in text. The strain used in the gene expression analysis did not express GCaMP. We did not analyze GCaMP expression in figure 5. We have corrected the error in the methods.

Reviewer #2 (Public Review):

The authors succeed in generalizing the pre-alignment procedure for their cell idenfication method to allow it to work effectively on data with only small subsets of cells labeled. They convincingly show that their extension accurately identifies head angle, based on finding auto fluorescent tissue and looking for a symmetric l/r axis. They demonstrate that the method works to identify known subsets of neurons with varying accuracy depending on the nature of underlying atlas data. Their approach should be a useful one for researchers wishing to identify subsets of head neurons in C. elegans, for example in whole brain recording, and the ideas might be useful elsewhere.

The authors also strive to give some general insights on what makes a good atlas. It is interesting and valuable to see (at least for this specific set of neurons) that 5-10 ideal examples are sufficient. However, some critical details would help in understanding how far their insights generalize. I believe the set of neurons in each atlas version are matched to the known set of cells in the sparse neuronal marker, however this critical detail isn't explicitly stated anywhere I can see.

This is an important point. We have made text modifications to make it clear to the readers that for all atlases, the number of entities (candidate list) was kept consistent as listed in the methods. In the results section under “CRF_ID 2.0 for automatic cell annotation in multi-cell images,” we added the following sentence: “Note that a truncated candidate list can be used for subse-tspecific cell ID if the neuronal expression is known” (page 3). In the methods section, we added the following sentence: “For multi-cell neuron predictions on the glr-1 strain, a truncated atlas containing only the above 37 neurons was used to exclude neuron candidates that are irrelevant for prediction” (Page 20).

In addition, it is stated that some neuron positions are missing in the neuropal data and replaced with the (single) position available from the open worm atlas. It should be stated how many neurons are missing and replaced in this way (providing weaker information).

We modified the text in the result section as follows: “Eight out of 37 candidate neurons are missing in the neuroPAL atlas, which means 40% of the pairwise relationships of neurons expressing the glr-1p::NLS-mcherry transgene were not augmented with the NeuroPAL data but were assigned the default values from the OpenWorm atlas” (page 10).

It also is not explicitly stated that the putative identities for the uncertain cells (designated with Greek letters) are used to sample the neuropal data. Large numbers of openworm single positions or if uncertain cells are misidentified forcing alignment against the positions of nearby but different cells would both handicap the neuropal atlas relative to the matched florescence atlas. This is an important question since sufficient performance from an ideal neuropal atlas (subsampled) would avoid the need for building custom atlases per strain.

The putative identities are not used to sample the NeuroPAL data. They were used in the glr-1 multi-cell case to indicate low confidence in manual identification/annotation. For all steps of manual annotation and CRF_ID predictions, we used real neuron labels, and the Greek labels were used for reporting purposes only. It is true that the OpenWorm values (40% of the atlas) would be a handicap for the neuroPAL atlas. This is mainly due to the difficulty of obtaining NeuroPAL data as it requires 3-color fluorescence microscopy and significant time and labor to annotate the large set of neurons. This is one reason to take a complementary approach as we do in this paper.

Reviewer #1 (Recommendations For The Authors):

1. Figure 3, there is a confusion in the legend relating to panels c-e (e.g. panel c is neuron ID accuracy but it is described per panel e in the legend.

We made the necessary changes.

1. Figure 3, were statistical tests performed for panels d-e? if so, and the outcome was not significant, then it might be good to indicate this in the legend.

We have added results of statistical tests in the legend as the following sentence: “All distributions in panel d and e had a p-value of less than 0.0001 for one sample t-test against zero.” One sample t-tests were performed because what is plotted already represents each atlas’ differences to the glr-1 25 dataset atlas, we didn’t think the statistical analyses between the other atlases would add significant value.

1. Figure 4, no asterisks are shown in the figure so it is possible to remove the sentence in the legend describing what the asterisk stands for.

Thank you. We made the necessary changes.

Reviewer #2 (Recommendations For The Authors):

Comparison with deep learning approaches could be more nuanced and structured, the authors (prior) approach extended here combines a specific set of comparative relationship measurements with a general optimization approach for matching based on comparative expectations. Other measurements could be used whether explicit (like neighbor expectations) or learned differences in embeddings. These alternate measurements would both need to be extensively re-calibrated for different sets of cells but might provide significant performance gains. In addition deep learning approaches don't solve the optimization part of the matching problem, so the authors approach seems to bring something strong to the table even if one is committed to learned methods (necessary I suspect for human level performance in denser cell sets than the relatively small number here). A more complete discussion of these themes might better frame the impact of the work and help readers think about the advantages and disadvantages or different methods for their own data.

We thank the reviewer for bringing up this point. We apologize perhaps not making the point clearer in the original submission. This extension of the original work (Chaudhary et al) is not changing the CRF-based framework, but only augmenting the approach with a better defined set of axes (solely because in multicell and not whole-brain datasets, the sparsity of neurons degrades the axis definition and consequently the neuron ID predictions). We are not fundamentally changing the framework, and therefore all the advantages (over registration-based approaches for example) also apply here. The other purpose of this paper is to demonstrate a couple of use-cases for gene expression analysis, which is common in studies in C. elegans (and other organisms). We hope that by showing a use-case others can see how this approach is useful for their own applications.

We have clarified these points in the paper (page 18). “The fundamental framework has not been changed from CRF_ID 1.0, and therefore the advantages of CRF_ID outlined in the original work apply for CRF_ID 2.0 as well.”

The atribution of anatomical differences to strain is interesting, but seems purely speculative, and somewhat unlikely. I would suspect the fundamentally more difficult nature of aligning N items to M>>N items in an atlas accounts for the differences in using the neuroPAL vs custom atlas here. If this is what is meant, it could be stated more clearly.

It is important to note that the same neuron candidate list (listed in methods) was used for all atlases, so there is no difference among the atlases in terms of the number of cells in the query vs. candidate list. In other words, the same values for M and for N are used regardless of the reference atlas used.

We have preliminary data indicating differences between the NeuroPAL and custom atlas. For instance, the NeuroPAL atlas scales smaller than the custom glr-1 atlas. Since direct comparisons of the different atlases are beyond the scope of this paper, we will leave the exact comparisons for future work. We suspect that the differences are from a combination of differences in anatomy and imaging conditions. While NeuroPAL atlas may not be exactly fitting for the custom dataset, it can serve as a good starting point for guesses when no custom atlases are available, as we have discussed earlier (response to Public Comments from Reviewer 1 Point 1). As explained earlier, we have added these discussions in the paper (see page 18).

I was also left wondering if the random removal of landmarks had to be adjusted in this work given it is (potentially) helping cope with not just occasional weak cells but the systematic loss of most of the cells in the atlas. If the parameters of this part of the algorithm don't influence the success for N to M>>N alignment (here when the neuroPAL or OpenWorm atlas is used) this seems interesting in itself and worth discussing. Conversely, if these parameters were opitmized for the matched atlas and used for the others, this would seem to bias performance results.

We may have failed to make this clear in the main text. As we have stated in our responses in the public review section, we do systematically limit the neuron labels in the candidate list to neurons that are known to be expressed by the promotor. The candidate list, which is kept consistent for all atlases, has more neurons than cells in the query, so it is always an N-to-M matching where M>N. We did not use landmarks, but such usage is possible and will only improve the matching.

We have attempted to clarify these points in the manuscript. In the results section under “CRF_ID 2.0 for automatic cell annotation in multi-cell images,” we added the following sentence: “Note that a truncated candidate list can be used for subset-specific cell ID if the neuronal expression is known” (page 3). In the methods section, we added the following sentence: “For multi-cell neuron predictions on the glr-1 strain, a truncated atlas containing only the above 37 neurons was used to exclude neuron candidates that are irrelevant for prediction” (Page 20).

Author response:

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

New Experiments

(1) Activation-dependent dynamics of PKA with the RIα regulatory subunit, adding to the answer to Reviewers 1 and 2. To determine the dynamics of all PKA isoforms, we have added experiments that used PKA-RIα as the regulatory subunit. We found differential translocation between PKA-C (co-expressed with PKA-RIα) and PKA-RIα (Figure 1–figure supplement 3), similar to the results when PKA-RIIα or PKA-RIβ was used.

(2) PKA-C dynamics elicited by a low concentration of norepinephrine, addressing Reviewer 3’s comment. We have found that PKA-C (co-expressed with RIIα) exhibited similar translocation into dendritic spines in the presence of a 5x lowered concentration (2 μM) of norepinephrine, suggesting that the translocation occurs over a wide range of stimulus strengths (Figure 1-figure supplement 2).

Reviewer #1 (Public Review):

Summary:

This is a short self-contained study with a straightforward and interesting message. The paper focuses on settling whether PKA activation requires dissociation of the catalytic and regulatory subunits. This debate has been ongoing for ~ 30 years, with renewed interest in the question following a publication in Science, 2017 (Smith et al.). Here, Xiong et al demonstrate that fusing the R and C subunits together (in the same way as Smith et al) prevents the proper function of PKA in neurons. This provides further support for the dissociative activation model - it is imperative that researchers have clarity on this topic since it is so fundamental to building accurate models of localised cAMP signalling in all cell types. Furthermore, their experiments highlight that C subunit dissociation into spines is essential for structural LTP, which is an interesting finding in itself. They also show that preventing C subunit dissociation reduces basal AMPA receptor currents to the same extent as knocking down the C subunit. Overall, the paper will interest both cAMP researchers and scientists interested in fundamental mechanisms of synaptic regulation.

Strengths:

The experiments are technically challenging and well executed. Good use of control conditions e.g untransfected controls in Figure 4.

We thank the reviewer for their accurate summarization of the position of the study in the field and for the positive evaluation of our study.

Weaknesses:

The novelty is lessened given the same team has shown dissociation of the C subunit into dendritic spines from RIIbeta subunits localised to dendritic shafts before (Tillo et al., 2017). Nevertheless, the experiments with RII-C fusion proteins are novel and an important addition.

We thank the reviewer for noticing our earlier work. The first part of the current work is indeed an extension of previous work, as we have articulated in the manuscript. However, this extension is important because recent studies suggested that the majority of PKA-RIIβ are axonal localized. The primary PKA subtypes in the soma and dendrite are likely PKA-RIβ or PKA-RIIα. Although it is conceivable that the results from PKA-RIIβ can be extended to the other subunits, given the current debate in the field regarding PKA dissociation (or not), it remains important to conclusively demonstrate that these other regulatory subunit types also support PKA dissociation within intact cells in response to a physiological stimulant. To complete the survey for all PKA-R isoforms, we have now added data for PKA-RIα (New Experiment #1), as they are also expressed in the brain (e.g., https://www.ncbi.nlm.nih.gov/gene/5573). Additionally, as the reviewer points out, our second part is a novel addition to the literature.

Reviewer #2 (Public Review):

Summary:

PKA is a major signaling protein that has been long studied and is vital for synaptic plasticity. Here, the authors examine the mechanism of PKA activity and specifically focus on addressing the question of PKA dissociation as a major mode of its activation in dendritic spines. This would potentially allow us to determine the precise mechanisms of PKA activation and address how it maintains spatial and temporal signaling specificity.

Strengths:

The results convincingly show that PKA activity is governed by the subcellular localization in dendrites and spines and is mediated via subunit dissociation. The authors make use of organotypic hippocampal slice cultures, where they use pharmacology, glutamate uncaging, and electrophysiological recordings.

Overall, the experiments and data presented are well executed. The experiments all show that at least in the case of synaptic activity, the distribution of PKA-C to dendritic spines is necessary and sufficient for PKA-mediated functional and structural plasticity.

The authors were able to persuasively support their claim that PKA subunit dissociation is necessary for its function and localization in dendritic spines. This conclusion is important to better understand the mechanisms of PKA activity and its role in synaptic plasticity.

We thank the reviewer for their positive evaluation of our study.

Weaknesses:

While the experiments are indeed convincing and well executed, the data presented is similar to previously published work from the Zhong lab (Tillo et al., 2017, Zhong et al 2009). This reduces the novelty of the findings in terms of re-distribution of PKA subunits, which was already established. A few alternative approaches for addressing this question: targeting localization of endogenous PKA, addressing its synaptic distribution, or even impairing within intact neuronal circuits, would highly strengthen their findings. This would allow us to further substantiate the synaptic localization and re-distribution mechanism of PKA as a critical regulator of synaptic structure, function, and plasticity.

We thank the reviewer for noticing our earlier work. The first part of the current work is indeed an extension of previous work, as we have articulated in the manuscript. However, this extension is important because recent studies suggested that the majority of PKA-RIIβ are axonal localized. The primary PKA subtypes in the soma and dendrite are likely PKA-RIβ or PKA-RIIα. Although it is conceivable that the results from PKA-RIIβ can be extended to the other subunits, given the current debate in the field regarding PKA dissociation (or not), it remains important to conclusively demonstrate that these other regulatory subunit types also support PKA dissociation within intact cells in response to a physiological stimulant. To complete the survey for all PKA-R isoforms, we have now added data for PKA-RIα (New Experiment #1), as they are also expressed in the brain (e.g., https://www.ncbi.nlm.nih.gov/gene/5573). Additionally, as Reviewer 1 points out, our second part is a novel addition to the literature.

We also thank the reviewer for suggesting the experiments to examine PKA’s synaptic localization and dynamics as a key mechanism underlying synaptic structure and function. We agree that this is a very interesting topic. At the same time, we feel that this mechanistic direction is open ended at this time and beyond what we try to conclude within this manuscript: prevention of PKA dissociation in neurons affects synaptic function. Therefore, we will save the suggested direction for future studies. We hope the reviewer understand.

Reviewer #3 (Public Review):

Summary:

Xiong et al. investigated the debated mechanism of PKA activation using hippocampal CA1 neurons under pharmacological and synaptic stimulations. Examining the two PKA major isoforms in these neurons, they found that a portion of PKA-C dissociates from PKA-R and translocates into dendritic spines following norepinephrine bath application. Additionally, their use of a non-dissociable form of PKC demonstrates its essential role in structural long-term potentiation (LTP) induced by two-photon glutamate uncaging, as well as in maintaining normal synaptic transmission, as verified by electrophysiology. This study presents a valuable finding on the activation-dependent re-distribution of PKA catalytic subunits in CA1 neurons, a process vital for synaptic functionality. The robust evidence provided by the authors makes this work particularly relevant for biologists seeking to understand PKA activation and its downstream effects essential for synaptic plasticity.

Strengths:

The study is methodologically robust, particularly in the application of two-photon imaging and electrophysiology. The experiments are well-designed with effective controls and a comprehensive analysis. The credibility of the data is further enhanced by the research team's previous works in related experiments. The conclusions of this paper are mostly well supported by data. The research fills a significant gap in our understanding of PKA activation mechanisms in synaptic functioning, presenting valuable insights backed by empirical evidence.

We thank the reviewer for their positive evaluation of our study.

Weaknesses:

The physiological relevance of the findings regarding PKA dissociation is somewhat weakened by the use of norepinephrine (10 µM) in bath applications, which might not accurately reflect physiological conditions. Furthermore, the study does not address the impact of glutamate uncaging, a well-characterized physiologically relevant stimulation, on the redistribution of PKA catalytic subunits, leaving some questions unanswered.

We agreed with the Reviewer that testing under physiological conditions is critical especially given the current debate in the literature. That is why we tested PKA dynamics induced by the physiological stimulant, norepinephrine. It has been suggested that, near the release site, local norepinephrine concentrations can be as high as tens of micromolar (Courtney and Ford, 2014). Based on this study, we have chosen a mid-range concentration (10 μM). At the same time, in light of the Reviewer’s suggestion, we have now also tested PKA-RIIα dissociation at a 5x lower concentration of norepinephrine (2 μM; New Experiment #2). The activation and translocation of PKA-C is also readily detectible under this condition to a degree comparable to when 10 μM norepinephrine was used.

Regarding the suggested glutamate uncaging experiment, it is extremely challenging because of finite signal-to-noise ratios in our experiments. From our past studies, we know that activated PKA-C can diffuse three dimensionally, with a fraction as membrane-associated proteins and the other as cytosolic proteins. Although we have evidence that its membrane affinity allows it to become enriched in dendritic spines, it is not known (and is unlikely) that activated PKA-C is selectively targeted to a particular spine. Glutamate uncaging of a single spine presumably would locally activate a small number of PKA-C. It will be very difficult to trace the 3D diffusion of these small number of molecules in the presence of surrounding resting-state PKA-C molecules. Finally, we hope the reviewer agrees that, regardless of the result of the glutamate uncaging experiment, the above new experiment (New Experiment #2) already indicate that certain physiologically relevant stimuli can drive PKA-C dissociation from PKA-R and translocation to spines, supporting our conclusion.

Reviewer #2 (Recommendations For The Authors):

It was a pleasure reading your paper, and the results are well-executed and well-presented.

My main and only recommendations are two ways to further expand the scope of the findings.

First, I believe addressing the endogenous localization of PKA-C subunit before and after PKA activation would be highly important to validate these claims. Overexpression of tagged proteins often shows vastly different subcellular distribution than their endogenous counterparts. Recent technological advances with CRISPR/Cas9 gene editing (Suzuki et al Nature 2016 and Gao et al Neuron 2019 for example) which the Zhong lab recently contributed to (Zhong et al 2021 eLife) allow us to tag endogenous proteins and image them in fixed or live neurons. Any experiments targeting endogenous PKA subunits that support dissociation and synaptic localization following activation would be very informative and greatly increase the novelty and impact of their findings.

We agreed that addressing the endogenous PKA dynamics is important. However, despite recent progress, endogenous labeling using CRISPR-based methods remains challenging and requires extensive optimization. This is especially true for signaling proteins whose endogenous abundance is often low. We have tried to label PKA catalytic subunits and regulatory subunits using both the homologous recombination-based method SLENDR and our own non-homologous end joining-based method CRISPIE. We did not succeed, in part because it is very difficult to see any signal under wide-field fluorescence conditions, which makes it difficult to screen different constructs for optimizing parameters. It is also possible that, at the endogenous abundance, the label is just not bright enough to be seen. Nevertheless, for both PKA type Iβ and type IIα that we studied in this manuscript, we have correlated the measured parameters (specifically, Spine Enrichment Index or SEI) with the overexpression level (Figure 1-figure supplement 1). We found that they are not strongly correlated with the expression level under our conditions. By extrapolating to non-overexpression conditions, our conclusion remains valid.

To overcome the inability to label endogenous PKA subunits using CRISPR-based methods, we have also attempted a conditional knock-in method call ENABLED that we previously developed to label PKA-Cα. In preliminary results, we found that endogenously label PKA were very dim. However, in a subset of cells that are bright enough to be quantified, the PKA catalytic subunit indeed translocated to dendritic spines upon stimulation (see Additional Fig. 1 in the next page), corroborating our results using overexpression. These results, however, are not ready to be published because characterization of the mouse line takes time and, at this moment, the signal-to-noise ratio remains low. We hope that the reviewer can understand.

Author response image 1.

Endogeneous PKA-Cα translocate to dendritic spines upon activation.

Second, experiments which would advance and validate these findings in vivo would be highly valuable. This could be achieved in a number of ways - one would be overexpression of tagged PKA versions and examining sub-cellular distribution before and after physiological activation in vivo. Another possibility is in vivo perturbation - one would speculate that disruption or tethering of PKA subunits to the dendrite would lead to cell-specific functional and structural impairments. This could be achieved in a similar manner to the in vitro experiments, with a PKA KO and replacement strategy of the tethered C-R plasmid, followed by structural or functional examination of neurons.

I would like to state that these experiments are not essential in my opinion, but any improvements in one of these directions would greatly improve and extend the impact and findings of this paper.

We thank the reviewer for the suggestion and the understanding. The suggested in vivo experiments are fascinating. However, in vivo imaging of dendritic spine morphology is already in itself challenging. The difficulty greatly increases when trying to detect partial, likely transient translocation of a signaling protein. It is also very difficult to knock down endogenous PKA while simultaneously expressing the R-C construct in a large number of cells to achieve detectable circuit or behavioral effect (and hope that compensation does not happen over weeks). We hope the reviewer agrees that these experiments would be their own project and go beyond the time and scope of the current study.

Reviewer #3 (Recommendations For The Authors):

Please elaborate on the methods used to visualize PKA-RIIα and PKA-RIβ subunits.

As suggested, we have now included additional details for visualizing PKA-Rs in the text. Specifically, we write (pg. 5): “…, as visualized using expressed PKA-R-mEGFP in separate experiments (Figs. 1A-1C).”.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

This is an interesting study investigating the mechanisms underlying membrane targeting of the NLRP3 inflammasome and reporting a key role for the palmitoylation-depalmitoylation cycle of cys130 in NRLP3. The authors identify ZDHHC3 and APT2 as the specific ZDHHC and APT/ABHD enzymes that are responsible for the s-acylation and de-acylation of NLRP3, respectively. They show that the levels of ZDHHC3 and APT2, both localized at the Golgi, control the level of palmitoylation of NLRP3. The S-acylation-mediated membrane targeting of NLRP3 cooperates with polybasic domain (PBD)-mediated PI4P-binding to target NLRP3 to the TGN under steady-state conditions and to the disassembled TGN induced by the NLRP3 activator nigericin.

However, the study has several weaknesses in its current form as outlined below.

(1) The novelty of the findings concerning cys130 palmitoylation in NLRP3 is unfortunately compromised by recent reports on the acylation of different cysteines in NLRP3 (PMID: 38092000), including palmitoylation of the very same cys130 in NLRP3 (Yu et al https://doi.org/10.1101/2023.11.07.566005), which was shown to be relevant for NLRP3 activation in cell and animal models. What remains novel and intriguing is the finding that NLRP3 activators induce an imbalance in the acylation-deacylation cycle by segregating NLRP3 in late Golgi/endosomes from de-acylating enzymes confined in the Golgi. The interesting hypothesis put forward by the authors is that the increased palmitoylation of cys130 would finally contribute to the activation of NLRP3. However, the authors should clarify the trafficking pathway of acylated-NLRP3. This pathway should, in principle, coincide with that of TGN46 which constitutively recycles from the TGN to the plasma membrane and is trapped in endosomes upon treatment with nigericin. 

We think the data presented in our manuscript are consistent with the majority of S-acylated NLRP3 remaining on the Golgi via S-acylation in both untreated and nigericin treated cells. We have performed an experiment with BrefeldinA (BFA), a fungal metabolite that disassembles the Golgi without causing dissolution of early endosomes, that further supports the conclusion that NLRP3 predominantly resides on Golgi membranes pre and post activation. Treatment of cells with BFA prevents recruitment of NLRP3 to the Golgi in untreated cells and blocks the accumulation of NLRP3 on the structures seen in the perinuclear area after nigericin treatment (see new Supplementary Figure 4A-D). We do see some overlap of NLRP3 signal with TGN46 in the perinuclear area after nigericin treatment (see new Supplementary Figure 2E), however this likely represents TGN46 at the Golgi rather than endosomes given that the NLRP3 signal in this area is BFA sensitive.  As with 2-BP and GFP-NLRP3C130S, GFP-NLRP3 spots also form in BFA / nigericin co-treated cells but not with untagged NLRP3. These spots also do not show any co-localisation with EEA1, suggesting that under these conditions, endosomes don’t appear to represent a secondary site of NLRP3 recruitment in the absence of an intact Golgi. However, we cannot completely rule out that some NLRP3 may recruited to endosomes at some point during its activation.

(2) To affect the S-acylation, the authors used 16 hrs treatment with 2-bromopalmitate (2BP). In Figure 1f, it is quite clear that NLRP3 in 2-BP treated cells completely redistributed in spots dispersed throughout the cells upon nigericin treatment. What is the Golgi like in those cells? In other words, does 2-BP alter/affect Golgi morphology? What about PI4P levels after 2-BP treatment? These are important missing pieces of data since both the localization of many proteins and the activity of one key PI4K in the Golgi (i.e. PI4KIIalpha) are regulated by palmitoylation.

We thank the reviewer for highlighting this point and agree that it is possible the observed loss of NLRP3 from the Golgi might be due to an adverse effect of 2-BP on Golgi morphology or PI4P levels. We have tested the effect of 2-BP on the Golgi markers GM130, p230 and TGN46. 2BP has marginal effects on Golgi morphology with cis, trans and TGN markers all present at similar levels to untreated control cells (Supplementary Figure 2B-D). We also tested the effect of 2-BP on PI4P levels using mCherry-P4M, a PI4P biosensor. Surprisingly, as noted by the reviewer, despite recruitment of PI4K2A being dependent on S-acylation, PI4P was still present on the Golgi after 2-BP treatment, suggesting that a reduction in Golgi PI4P levels does not underly loss of NLRP3 from the Golgi (Supplementary Figure 2A). The pool of PI4P still present on the Golgi following 2-BP treatment is likely generated by other PI4K enzymes that localise to the Golgi independently of S-acylation, such as PI4KIIIB. We have included this data in our manuscript as part of a new Supplementary Figure 2. 

(3) The authors argue that the spots observed with NLRP-GFP result from non-specific effects mediated by the addition of the GFP tag to the NLRP3 protein. However, puncta are visible upon nigericin treatment, as a hallmark of endosomal activation. How do the authors reconcile these data? Along the same lines, the NLRP3-C130S mutant behaves similarly to wt NLRP3 upon 2-BP treatment (Figure 1h). Are those NLRP3-C130S puncta positive for endosomal markers? Are they still positive for TGN46? Are they positive for PI4P?

This is a fair point given the literature showing overlap of NLRP3 puncta formed in response to nigericin with endosomal markers and the similarity of the structures we see in terms of size and distribution to endosomes after 2BP + nigericin treatment. We have tested whether these puncta overlap with EEA1, TGN46 or PI4P (Supplementary Figure 2A, E-G). The vast majority of spots formed by GFP-NLRP3 co-treated with 2-BP and nigericin do not co-localise with EEA1, TGN46 or PI4P. This is consistent with these spots potentially being an artifact, although it has recently been shown that human NLRP3 unable to bind to the Golgi can still respond to nigericin (Mateo-Tórtola et al., 2023). These puncta might represent a conformational change cytosolic NLRP3 undergoes in response to stimulation, although our results suggest that this doesn’t appear to happen on endosomes.

(4) The authors expressed the minimal NLRP3 region to identify the domain required for NLRP3 Golgi localization. These experiments were performed in control cells. It might be informative to perform the same experiments upon nigericin treatment to investigate the ability of NLRP3 to recognize activating signals. It has been reported that PI4P increases on Golgi and endosomes upon NG treatment. Hence, all the differences between the domains may be lost or preserved. In parallel, also the timing of such recruitment upon nigericin treatment (early or late event) may be informative for the dynamics of the process and of the contribution of the single protein domains.

This is an interesting point which we thank the reviewer for highlighting. However, we think that each domain on its own is not capable of responding to nigericin as shown by the effect of mutations in helix115-125 or the PB region in the full-length NLRP3 protein. NLRP3HF, which still contains a functional PB region, isn’t capable of responding to nigericin in the same way as wild type NLRP3 (Supplementary Figure 6C-D). Similarly, mutations in the PB region of full length NLRP3 that leave helix115-125 intact show that helix115-125 is not sufficient to allow enhanced recruitment of NLRP3 to Golgi membranes after nigericin treatment (Supplementary Figure 9A). We speculate that helix115-125, the PB region and the LRR domain all need to be present to provide maximum affinity of NLRP3 for the Golgi prior to encounter with and S-acylation by ZDHHC3/7. Mutation or loss of any one of the PB region, helix115-125 or the LRR lowers NLRP3 membrane affinity, which is reflected by reduced levels of NLRP3 captured on the Golgi by S-acylation at steady state and in response to nigericin. 

(5) As noted above for the chemical inhibitors (1) the authors should check the impact of altering the balance between acyl transferase and de-acylases on the Golgi organization and PI4P levels. What is the effect of overexpressing PATs on Golgi functions?

We have checked the effect of APT2 overexpression on Golgi morphology and can show that it has no noticeable effect, ruling out an impact of APT on Golgi integrity as the reason for loss of NLRP3 from the Golgi in the presence of overexpressed APT2. We have included these images as Supplementary Figure 11H-J. 

It is plausible that the effects of ZDHHC3 or ZDHHC7 on enhanced recruitment of NLRP3 to the Golgi may be via an effect on PI4P levels since, as mentioned above, both enzymes are involved in recruitment of PI4K2A to the Golgi and have previously been shown to enhance levels of PI4K2A and PI4P on the Golgi when overexpressed (Kutchukian et al., 2021). However, NLRP3 mutants with most of the charge removed from the PB region, which are presumably unable to interact with PI4P or other negatively charged lipids, are still capable of being recruited to the Golgi by excess ZDHHC3. This would suggest that the effect of overexpressed ZDHHC3 on NLRP3 is largely independent of changes in PI4P levels on the Golgi and instead driven by helix115-125 and S-acylation at Cys-130. The latter point is supported by the observation that NLRP3HF and NLRP3Cys130 are insensitive to ZDHHC3 overexpression.

At the levels of HA-ZDHHC3 used in our experiments with NLRP3 (200ng pEF-Bos-HAZDHHC3 / c.a. 180,000 cells) we don’t see any adverse effect on Golgi morphology (Author response image 1), although it has been noted previously by others that higher levels of ZDHHC3 can have an impact on TGN46 (Ernst et al., 2018). ZDHHC3 overexpression surprisingly has no adverse effects on Golgi function and in fact enhances secretion from the Golgi (Ernst et al., 2018).  

Author response image 1.

Overexpression of HA-ZDHHC3 does not impact Golgi morphology. A) Representative confocal micrographs of HeLaM cells transfected with 200 ng HA-ZDHHC3 fixed and stained with antibodies to STX5 or TGN46. Scale bars = 10 µm. 

Reviewer #2 (Public Review):

Summary:

This paper examines the recruitment of the inflammasome seeding pattern recognition receptor NLRP3 to the Golgi. Previously, electrostatic interactions between the polybasic region of NLRP3 and negatively charged lipids were implicated in membrane association. The current study reports that reversible S-acylation of the conserved Cys-130 residue, in conjunction with upstream hydrophobic residues plus the polybasic region, act together to promote Golgi localization of NLRP3, although additional parts of the protein are needed for full Golgi localization. Treatment with the bacterial ionophore nigericin inhibits membrane traffic and prevents Golgi-associated thioesterases from removing the acyl chain, causing NLRP3 to become immobilized at the Golgi. This mechanism is put forth as an explanation for how NLRP3 is activated in response to nigericin.

Strengths:

The experiments are generally well presented. It seems likely that Cys-130 does indeed play a previously unappreciated role in the membrane association of NLRP3.

Weaknesses:

The interpretations about the effects of nigericin are less convincing. Specific comments follow.

(1) The experiments of Figure 4 bring into question whether Cys-130 is S-acylated. For Cys130, S-acylation was seen only upon expression of a severely truncated piece of the protein in conjunction with overexpression of ZDHHC3. How do the authors reconcile this result with the rest of the story?

Providing direct evidence of S-acylation at Cys-130 in the full-length protein proved difficult. We attempted to detect S-acylation of this residue by mass spectrometry. However, the presence of the PB region and multiple lysines / arginines directly after Cys-130 made this approach technically challenging and we were unable to convincingly detect S-acylation at Cys-130 by M/S. However, Cys-130 is clearly important for membrane recruitment as its mutation abolishes the localisation of NLRP3 to the Golgi. It is feasible that it is the hydrophobic nature of the cysteine residue itself which supports localisation to the Golgi, rather than S-acylation of Cys-130. A similar role for cysteine residues present in SNAP-25 has been reported (Greaves et al., 2009). However, the rest of our data are consistent with Cys-130 in NLRP3 being S-acylated. We also refer to another recently published study which provides additional biochemical evidence that mutation of Cys-130 impacts the overall levels of NLRP3 S-acylation (Yu et al., 2024). 

(2) Nigericin seems to cause fragmentation and vesiculation of the Golgi. That effect complicates the interpretations. For example, the FRAP experiment of Figure 5 is problematic because the authors neglected to show that the FRAP recovery kinetics of nonacylated resident Golgi proteins are unaffected by nigericin. Similarly, the colocalization analysis in Figure 6 is less than persuasive when considering that nigericin significantly alters Golgi structure and could indirectly affect colocalization. 

We agree that it is likely that the behaviour of other Golgi resident proteins are altered by nigericin. This is in line with a recent proteomics study showing that nigericin alters the amount of Golgi resident proteins associated with the Golgi (Hollingsworth et al., 2024) and other work demonstrating that changes in organelle pH can influence the membrane on / off rates of Rab GTPases (Maxson et al., 2023). However, Golgi levels of other peripheral membrane proteins

that associate with the Golgi through S-acylation, such as N-Ras, appear unaltered (Author response image 2.), indicating a degree of selectivity in the proteins affected. Our main point here is that NLRP3 is amongst those proteins whose behaviour on the Golgi is sensitive to nigericin and that this change in behaviour may be important to the NLRP3 activation process, although this requires further investigation and will form the basis of future studies. 

The reduction in co-localisation between NLRP3 and APT2, due to alterations in Golgi organisation and trafficking, was the point we were trying to make with this figure, and we apologise if this was not clear. We think that the changes in Golgi structure and function caused by nigericin potentially affect the ability of APT2 to encounter NLRP3 and de-acylate it. We have added a new paragraph to the results section to hopefully explain this more clearly. We recognise that our results supporting this hypothesis are at present limited and we have toned down the language used in the results section to reflect the nature of these findings..  

Author response image 2.

S-acylated peripheral membrane proteins show differential sensitivity to nigericin. A) Representative confocal micrographs of HeLaM cells coexpressing GFP-NRas and an untagged NLRP3 construct. Cells were left untreated or treated with 10 µM nigericin for 1 hour prior to fixation. Scale bars = 10 µm. B) Quantification of GFP-NRas or NLRP3 signal in the perinuclear region of cells treated with or without nigericin

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

(1) Does overnight 2-BP treatment potentially have indirect effects that could prevent NLRP3 recruitment? It would be useful here to show some sort of control confirming that the cells are not broadly perturbed.

Please see our response to point (2) raised by reviewer #1 which is along similar lines. 

(2) In Figure 5, "Veh" presumably is short for "Vehicle". This term should be defined in the legend.

We have now corrected this.

References

Ernst, A.M., S.A. Syed, O. Zaki, F. Bottanelli, H. Zheng, M. Hacke, Z. Xi, F. Rivera-Molina, M. Graham, A.A. Rebane, P. Bjorkholm, D. Baddeley, D. Toomre, F. Pincet, and J.E. Rothman. 2018. SPalmitoylation Sorts Membrane Cargo for Anterograde Transport in the Golgi. Dev Cell. 47:479-493 e477.

Greaves, J., G.R. Prescott, Y. Fukata, M. Fukata, C. Salaun, and L.H. Chamberlain. 2009. The hydrophobic cysteine-rich domain of SNAP25 couples with downstream residues to mediate membrane interactions and recognition by DHHC palmitoyl transferases. Mol Biol Cell. 20:1845-1854.

Hollingsworth, L.R., P. Veeraraghavan, J.A. Paulo, J.W. Harper, and I. Rauch. 2024. Spatiotemporal proteomic profiling of cellular responses to NLRP3 agonists. bioRxiv.

Kutchukian, C., O. Vivas, M. Casas, J.G. Jones, S.A. Tiscione, S. Simo, D.S. Ory, R.E. Dixon, and E.J. Dickson. 2021. NPC1 regulates the distribution of phosphatidylinositol 4-kinases at Golgi and lysosomal membranes. EMBO J. 40:e105990.

Mateo-Tórtola, M., I.V. Hochheiser, J. Grga, J.S. Mueller, M. Geyer, A.N.R. Weber, and A. TapiaAbellán. 2023. Non-decameric NLRP3 forms an MTOC-independent inflammasome. bioRxiv:2023.2007.2007.548075.

Maxson, M.E., K.K. Huynh, and S. Grinstein. 2023. Endocytosis is regulated through the pHdependent phosphorylation of Rab GTPases by Parkinson’s kinase LRRK2. bioRxiv:2023.2002.2015.528749.

Yu, T., D. Hou, J. Zhao, X. Lu, W.K. Greentree, Q. Zhao, M. Yang, D.G. Conde, M.E. Linder, and H. Lin. 2024. NLRP3 Cys126 palmitoylation by ZDHHC7 promotes inflammasome activation. Cell Rep. 43:114070.

Author Response

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

We sincerely thank the reviewers for their in-depth consideration of our manuscript and their helpful reviews. Their efforts have made the paper much better. We have responded to each point. The previously provided public responses have been updated they are included after the private response for convenience.

Reviewer #1 (Recommendations For The Authors):

1. In general, the manuscript will benefit from copy editing and proof reading. Some obvious edits;

2. Page 6 line 140. Do the authors mean Cholera toxin B?

Response: We corrected this error and went through the entire paper carefully correcting for grammar and increased clarity.

• Page 8 line 173. Methylbetacyclodextrin is misspelled.

Response: Yes, corrected.

• Figure 4c is missing representative traces for electrophysiology data.

• Figure 4. Please check labeling ordering in figure legend as it does not match the panels in the figure.

Thank you for the correction and we apologize for the confusion in figure 4. We uploaded an incomplete figure legend, and the old panel ‘e’ was not from an experiment that was still in the figure. It was removed and the figure legends are now corrected.

• Please mention the statistical analysis used in all figure legends.

Response: Thank you for pointing out this omission, statistics have been added.

• Although the schematics in each figure helps guide readers, they are very inconsistent and sometimes confusing. For example, in Figure 5 the gating model is far-reaching without conclusive evidence, whereas in Figure 6 it is over simplified and unclear what the image is truly representing (granted that the downstream signaling mechanism and channel is not known).

Response: Figure 5d is the summary figure for the entire paper. We have made this clearer in the figure legend and we deleted the title above the figure that gave the appearance that the panel relates to swell only. It is the proposed model based on what we show in the paper and what is known about the activation mechanism of TREK-1.

Figure 6 is supposed to be simple. It is to help the reader understand that when PA is low mechanical sensitivity is high. Without the graphic, previous reviewers got confused about threshold going down and mechanosensitivity going up and how the levels of PA relate. Low PA= high sensitivity. We’ve added a downstream effector to the right side of the panel to avoid any biased to a putative downstream channel effector. The purpose of the experiment is to show PLD has a mechanosensitive phenotype in vivo.

Reviewer #2 (Recommendations For The Authors):

This manuscript outlines some really interesting findings demonstrating a mechanism by which mechanically driven alterations in molecular distributions can influence a) the activity of the PLD2 molecule and subsequently b) the activation of TREK-1 when mechanical inputs are applied to a cell or cell membrane.

The results presented here suggest that this redistribution of molecules represents a modulatory mechanism that alters either the amplitude or the sensitivity of TREK-1 mediated currents evoked by membrane stretch. While the authors do present values for the pressure required to activate 50% of channels (P50), the data presented provides incomplete evidence to conclude a shift in threshold of the currents, given that many of the current traces provided in the supplemental material do not saturate within the stimulus range, thus limiting the application of a Boltzmann fit to determine the P50. I suggest adding additional context to enable readers to better assess the limitations of this use of the Boltzmann fit to generate a P50, or alternately repeating the experiments to apply stimuli up to lytic pressures to saturate the mechanically evoked currents, enabling use of the Boltzmann function to fit the data.

Response: We thank the reviewer for pointing this out. We agree the currents did not reach saturation. Hence the term P50 could be misleading, so we have removed it from the paper. We now say “half maximal” current measured from non-saturating pressures of 0-60 mmHg. We also deleted the xPLD data in supplemental figure 3C since there is insufficient current to realistically estimate a half maximal response.

In my opinion, the conclusions presented in this manuscript would be strengthened by an assessment of the amount of TREK-1 in the plasma membrane pre and post application of shear. While the authors do present imaging data in the supplementary materials, these data are insufficiently precise to comment on expression levels in the membrane. To strengthen this conclusion the authors could conduct cell surface biotinylation assays, as a more sensitive and quantitative measure of membrane localisation of the proteins of interest.

1. Response: as mentioned previously, we do not have an antibody to the extracellular domain. Nonetheless to better address this concern we directly compared the levels of TREK-1, PIP2, and GM1; in xPLD2, mPLD2, enPLD2 with and without shear. The results are in supplemental figure 2. PLD2 is known to increase endocytosis1 and xPLD2 is known to block both agonist induced and constitutive endocytosis of µ-opioid receptor2. The receptor is trapped on the surface. This is true of many proteins including Rho3, ARF4, and ACE21 among others. In agreement with this mechanism, in Figure S2C,G we show that TREK increases with xPLD and the localization can clearly be seen at the plasma membrane just like in all of the other publications with xPLD overexpression. xPLD2 would be expected to inhibit the basal current but we presume the increased expression likely has compensated and there is sufficient PA and PG from other sources to allow for the basal current. It is in this state that we then conduct our ephys and monitor with a millisecond time resolution and see no activation. We are deriving conclusion from a very clear response—Figure 1b shows almost no current, even at 1-10 ms after applying pressure. There is little pressure current when we know the channel is present and capable of conducting ion (Figure 1d red bar). After shear there is a strong decrease in TREK-1 currents on the membrane in the presence of xPLD2. But it is not less than TREK-1 expression with mPLD2. And since mouse PLD2 has the highest basal current and pressure activation current. The amount of TREK-1 present is sufficient to conduct large current. To have almost no detective current would require at least a 10 fold reduction compared to mPLD2 levels before we would lack the sensitivity to see a channel open. Lasty endocytosis typically in on the order of seconds to minutes, no milliseconds.

2. We have shown an addition 2 independent ways that TREK-1 is on the membrane during our stretch experiments. Figure 1d shows the current immediately prior to applying pressure for wt TREK-1. When catalytically dead PLD is present (xPLD2) there is almost normal basal current. The channel is clearly present. And then in figure 1a we show within a millisecond there is no pressure current. As a control we added a functionally dead TREK-1 truncation (xTREK). Compared to xPLD2 there is clearly normal basal current. If this is not strong evidence the channel was available on the surface for mechanical activation please help us understand why. And if you think within 2.1 ms 100% of the channel is gone by endocytosis please provide some evidence that this is possible so we can reconsider.

3. We have TIRF super resolution imaging with ~20 nm x-y resolution and ~ 100nm z resolution and Figure 2b clearly shows the channel on the membrane. When we apply pressure in 1b, the channel is present.

4. Lastly, In our previous studies we showed activation of PLD2 by anesthetics was responsible for all of TREK-1’s anesthetic sensitivity and this was through PLD2 binding to the C-terminus of TREK-15. We showed this was the case by transferring anesthetic sensitivity to an anesthetic insensitive homolog TRAAK. This established conclusively the basic premise of our mechanism. Here we show the same C-terminal region and PLD2 are responsible for the mechanical current observed by TREK-1. TRAAK is already mechanosensitive so the same chimera will not work for our purposes here. But anesthetic activation and mechanical activation are dramatically different stimuli, and the fact that the role of PLD is robustly observed in both should be considered.

The authors discuss that the endogenous levels of TREK-1 and PLD2 are "well correlated: in C2C12 cells, that TREK-1 displayed little pair correlation with GM1 and that a "small amount of TREK-1 trafficked to PIP2". As such, these data suggest that the data outlined for HEK293T cells may be hampered by artefacts arising from overexpression. Can TREK-1 currents be activated by membrane stretch in these cells C2C12 cells and are they negatively impacted by the presence of xPLD2? Answering this question would provide more insight into the proposed mechanism of action of PLD2 outlined by the authors in this manuscript. If no differences are noted, the model would be called into question. It could be that there are additional cell-specific factors that further regulate this process.

Response: The low pair correlation of TREK-1 and GM1 in C2C12 cells was due to insufficient levels of cholesterol in the cell membrane to allow for robust domain formation. In Figure 4b we loaded C2C12 cells with cholesterol using the endogenous cholesterol transport protein apoE and serum (an endogenous source of cholesterol). As can be seen in Fig. 4b, the pair correlation dramatically increased (purple line). This was also true in neuronal cells (N2a) (Fig 4d, purple bar). And shear (3 dynes/cm2) caused the TREK-1 that was in the GM1 domains to leave (red bar) reversing the effect of high cholesterol. This demonstrates our proposed mechanism is working as we expect with endogenously expressed proteins.

There are many channels in C2C12 cells, it would be difficult to isolate TREK-1 currents, which is why we replicated the entire system (ephys and dSTORM) in HEK cells. Note, in figure 4c we also show that adding cholesterol inhibits TREK-1 whole cell currents in HEK293cells.

As mentioned in the public review, the behavioural experiments in D. melanogaster can not solely be attributed to a change in threshold. While there may be a change in the threshold to drive a different behaviour, the writing is insufficiently precise to make clear that conclusions cannot be drawn from these experiments regarding the functional underpinnings of this outcome. Are there changes in resting membrane potential in the mutant flys? Alterations in Nav activity? Without controlling for these alternate explanations it is difficult to see what this last piece of data adds to the manuscript, particularly given the lack of TREK-1 in this organism. At the very least, some editing of the text to more clearly indicate that these data can only be used to draw conclusions on the change in threshold for driving the behaviour not the change in threshold of the actual mechanotransduction event (i.e. conversion of the mechanical stimulus into an electrochemical signal).

Response: We agree; features other than PLDs direct mechanosensitivity are likely contributing. This was shown in figure 6g left side. We have an arrow going to ion channel and to other downstream effectors. We’ve added the putative alteration to downstream effectors to the right side of the panel. This should make it clear that we no more speculate the involvement of a channel than any of the other many potential downstream effectors. As mentioned above, the figure helps the reader coordinate low PA with increased mechanosensitivity. Without the graphic reviewers got confused that PA increased the threshold which corresponds to a decreased sensitivity to pain. Nonetheless we removed our conclusion about fly thresholds from the abstract and made clearer in the main text the lack of mechanism downstream of PLD in flies including endocytosis. Supplemental Figure S2H also helps emphasize this. .

Nav channels are interesting, and since PLD contribute to endocytosis and Nav channels are also regulated by endocytosis there is likely a PLD specific effect using Nav channels. There are many ways PA likely regulates mechanosensitive thresholds, but we feel Nav is beyond the scope of our paper. Someone else will need to do those studies. We have amended a paragraph in the conclusion which clearly states we do not know the specific mechanism at work here with the suggestions for future research to discover the role of lipid and lipid-modifying enzymes in mechanosensitive neurons.

There may be fundamental flaws in how the statistics have been conducted. The methods section indicates that all statistical testing was performed with a Student's t-test. A visual scan of many of the data sets in the figures suggests that they are not normally distributed, thus a parametric test such as a Student's t-test is not valid. The authors should assess if each data set is normally distributed, and if not, a non-parametric statistical test should be applied. I recommend assessing the robustness of the statistical analyses and adjusting as necessary.

Response: We thank the reviewer for pointing this out, indeed there is some asymmetry in Figure 6C-d. The p values with Mann Whitney were slightly improved p=0.016 and p=0.0022 for 6c and 6d respectively. For reference, the students t-test had slightly worse statistics p=0.040 and p=0.0023. The score remained the same 1 and 2 stars respectively.

The references provided for the statement regarding cascade activation of the TRPs are incredibly out of date. While it is clear that TRPV4 can be activated by a second messenger cascade downstream of osmotic swelling of cells, TRPV4 has also been shown to be activated by mechanical inputs at the cell-substrate interface, even when the second messenger cascade is inhibited. Recommend updating the references to reflect more current understanding of channel activation.

Response: We thank the reviewer for pointing this out. We have updated the references and changed the comment to “can be” instead of “are”. The reference is more general to multiple ion channel types including KCNQ4. This should avoid any perceived conflict with the cellsubstrate interface mechanism which we very much agree is a correct mechanism for TRP channels.

Minor comments re text editing etc:

The central messages of the manuscript would benefit from extensive work to increase the precision of the writing of the manuscript and the presentation of data in the figures, such textual changes alone would help address a number of the concerns outlined in this review, by clarifying some ambiguities. There are numerous errors throughout, ranging from grammatical issues, ambiguities with definitions, lack of scale bars in images, lack of labels on graph axes, lack of clarity due to the mode of presentation of sample numbers (it would be far more precise to indicate specific numbers for each sample rather than a range, which is ambiguous and confusing), unnecessary and repeat information in the methods section. Below are some examples but this list is not exhaustive.

Response: Thank you, reviewer # 1 also had many of these concerns. We have gone through the entire paper and improved the precision of the writing of the manuscript. We have also added the missing error bar to Figure 6. And axis labels have been added to the inset images. The redundancy in cell culture methods has been removed. Where a range is small and there are lots of values, the exact number of ‘n’ are graphically displayed in the dot plot for each condition.

Text:

I recommend considering how to discuss the various aspects of channel activation. A convention in the field is to use mechanical activation or mechanical gating to describe that process where the mechanical stimulus is directly coupled to the channel gating mechanism. This would be the case for the activation of TREK-1 by membrane stretch alone. The increase in activation by PLD2 activity then reflects a modulation of the mechanical activation of the channel, because the relevant gating stimulus is PA, rather than force/stretch. The sum of these events could be described as shear-evoked or mechanically-evoked, TREK-1 mediated currents (thus making it clear that the mechanical stimulus initiates the relevant cascade, but the gating stimulus may be other than direct mechanical input.) Given the interesting and compelling data offered in this manuscript regarding the sensitisation of TREK-1 dependent mechanicallyevoked currents by PLD2, an increase in the precision of the language would help convey the central message of this work.

Response; We agree there needs to be convention. We have taken the suggestion of mechanically evoked and we suggest the following definitions:

1. Mechanical activation of PLD2: direct force on the lipids releasing PLD2 from nonactivating lipids.

2. Mechanical activation/gating of TREK1: direct force from lipids from either tension or hydrophobic mismatch that opens the channel.

3. Mechanically evoked: a mechanical event that leads to a downstream effect. The effect is mechanically “evoked”.

4. Spatial patterning/biochemistry: nanoscopic changes in the association of a protein with a nanoscopic lipid cluster or compartment.

An example of where discussion of mechanical activation is ambiguous in the text is found at line 109: "channel could be mechanically activated by a movement from GM1 to PIP2 lipids." In this case, the sentence could be suggesting that the movement between lipids provides the mechanical input that activates the channel, which is not what the data suggest.

Response: Were possible we have replaced “movement” with “spatial patterning” and “association” and “dissociation” from specific lipid compartment. This better reflects the data we have in this paper. However, we do think that a movement mechanically activates the channel, GM1 lipids are thick and PIP2 lipids are thin, so movement between the lipids could activate the channel through direct lipid interaction. We will address this aspect in a future paper.

Inconsistencies with usage:

• TREK1 versus TREK-1

Response: corrected to TREK-1

• mPLD2 versus PLD2

Response: where PLD2 represents mouse this has been corrected.

• K758R versus xPLD2

Response: we replaced K758R in the methods with xPLD2.

• HEK293T versus HEK293t Response: we have changed all instances to read HEK293T.

• Drosophila melanogaster and D. melanogaster used inconsistently and in many places incorrectly

Response: we have read all to read the common name Drosophila.

Line 173: misspelled methylbetacyclodextrin

Response corrected

Line 174: degree symbol missing

Response corrected

Line 287: "the decrease in cholesterol likely evolved to further decrease the palmate order in the palmitate binding site"... no evidence, no support for this statement, falsely attributes intention to evolutionary processes .

Response: we have removed the reference to evolution at the request of the reviewer, it is not necessary. But we do wish to note that to our knowledge, all biological function is scientifically attributed to evolution. The fact that cholesterol decreases in response to shear is evidence alone that the cell evolved to do it.

Line 307: grammatical error

Response: the redundant Lipid removed.

Line 319: overinterpreted - how is the mechanosensitivy of GPCRs explained by this translocation?

Response: all G-alpha subunits of the GPCR complex are palmitoylated. We showed PLD (which has the same lipidation) is mechanically activated. If the palmitate site is disrupted for PLD2, then it is likely disrupted for every G-alpha subunit as well.

Line 582: what is the wild type referred to here?

Response: human full length with a GFP tag.

Methods:

• Sincere apologies if I missed something but I do not recall seeing any experiments using purified TREK-1 or flux assays. These details should be removed from the methods section

Response: Removed.

• There is significant duplication of detail across the methods (three separate instances of electrophysiology details) these could definitely be consolidated.

Response: Duplicates removed.

Figures:

• Figure 2- b box doesn't correspond to inset. Bottom panel should provide overview image for the cell that was assessed with shear. In bottom panel, circle outlines an empty space.

Response: We have widened the box slightly to correspond so the non shear box corresponds to the middle panel. We have also added the picture for the whole cell to Fig S2g and outlined the zoom shown in the bottom panel of Fig 2b as requested. The figure is of the top of a cell. We also added the whole cell image of a second sheared cell.

Author response image 1.

• Figure 3 b+c: inset graph lacking axis labels

Response; the inset y axis is the same as the main axis. We added “pair corr. (5nM)” and a description in the figure legend to make this clearer. The purpose of the inset is to show statistical significance at a single point. The contrast has been maximized but without zooming in points can be difficult to see.

• Figure 5: replicate numbers missing and individual data points lacking in panels b + c, no labels of curve in b + c, insets, unclear what (5 nm) refers to in insets.

Response: Thank you for pointing out these errors. The N values have been added. Similar to figure 3, the inset is a bar graph of the pair correlation data at 5 nm. A better explanation of the data has been added to the figure legend.

• Figure 6: no scale bar, no clear membrane localization evident from images presented, panel g offers virtually nothing in terms of insight

Response: We have added scale bars to figure 6b. Figure 6g is intentionally simplistic, we found that correlating decreased threshold with increased pain was confusing. A previous reviewer claimed our data was inconsistent. The graphic avoids this confusion. We also added negative effects of low PA on downstream effects to the right panel. This helps graphically show we don’t know the downstream effects.

Reviewer #3 (Recommendations For The Authors):

Minor suggestions:

1. line 162, change 'heat' to 'temperature'.

Response: changed.

1. in figure 1, it would be helpful to keep the unit for current density consistent among different panels. 1e is a bit confusing: isn't the point of Figure 1 that most of TREK1 activation is not caused by direct force-sensing?

Response: Yes, the point of figure 1 is to show that in a biological membrane over expressed TREK-1 is a downstream effector of PLD2 mechanosensation which is indirect. We agree the figure legend in the previous version of the paper is very confusing.

There is almost no PLD2 independent current in our over expressed system, which is represented by no ions in the conduction pathway of the channel despite there being tension on the membrane.

Purified TREK-1 is only mechanosensitive in a few select lipids, primarily crude Soy PC. It was always assumed that HEK293 and Cos cells had the correct lipids since over expressed TREK-1 responded to mechanical force in these lipids. But that does not appear to be correct, or at least only a small amount of TREK-1 is in the mechanosensitive lipids. Figure 1e graphically shows this. The arrows indicate tension, but the channel isn’t open with xPLD2 present. We added a few sentences to the discussion to further clarify.

Panels c has different units because the area of the tip was measured whereas in d the resistance of the tip was measured. They are different ways for normalizing for small differences in tip size.

1. line 178, ~45 of what?

Response: Cells were fixed for ~30 sec.

1. line 219 should be Figure 4f?

Response: thank you, yes Figure 4f.

Previous public reviews with minor updates.

Reviewer #1 (Public Review):

Force sensing and gating mechanisms of the mechanically activated ion channels is an area of broad interest in the field of mechanotransduction. These channels perform important biological functions by converting mechanical force into electrical signals. To understand their underlying physiological processes, it is important to determine gating mechanisms, especially those mediated by lipids. The authors in this manuscript describe a mechanism for mechanically induced activation of TREK-1 (TWIK-related K+ channel. They propose that force induced disruption of ganglioside (GM1) and cholesterol causes relocation of TREK-1 associated with phospholipase D2 (PLD2) to 4,5-bisphosphate (PIP2) clusters, where PLD2 catalytic activity produces phosphatidic acid that can activate the channel. To test their hypothesis, they use dSTORM to measure TREK-1 and PLD2 colocalization with either GM1 or PIP2. They find that shear stress decreases TREK-1/PLD2 colocalization with GM1 and relocates to cluster with PIP2. These movements are affected by TREK-1 C-terminal or PLD2 mutations suggesting that the interaction is important for channel re-location. The authors then draw a correlation to cholesterol suggesting that TREK-1 movement is cholesterol dependent. It is important to note that this is not the only method of channel activation and that one not involving PLD2 also exists. Overall, the authors conclude that force is sensed by ordered lipids and PLD2 associates with TREK-1 to selectively gate the channel. Although the proposed mechanism is solid, some concerns remain.

1) Most conclusions in the paper heavily depend on the dSTORM data. But the images provided lack resolution. This makes it difficult for the readers to assess the representative images.

Response: The images were provided are at 300 dpi. Perhaps the reviewer is referring to contrast in Figure 2? We are happy to increase the contrast or resolution.

As a side note, we feel the main conclusion of the paper, mechanical activation of TREK-1 through PLD2, depended primarily on the electrophysiology in Figure 1b-c, not the dSTORM. But both complement each other.

2) The experiments in Figure 6 are a bit puzzling. The entire premise of the paper is to establish gating mechanism of TREK-1 mediated by PLD2; however, the motivation behind using flies, which do not express TREK-1 is puzzling.

Response: The fly experiment shows that PLD mechanosensitivity is more evolutionarily conserved than TREK-1 mechanosensitivity. We have added this observation to the paper.

-Figure 6B, the image is too blown out and looks over saturated. Unclear whether the resolution in subcellular localization is obvious or not.

Response: Figure 6B is a confocal image, it is not dSTORM. There is no dSTORM in Figure 6. We have added the error bars to make this more obvious. For reference, only a few cells would fit in the field of view with dSTORM.

-Figure 6C-D, the differences in activity threshold is 1 or less than 1g. Is this physiologically relevant? How does this compare to other conditions in flies that can affect mechanosensitivity, for example?

Response: Yes, 1g is physiologically relevant. It is almost the force needed to wake a fly from sleep (1.2-3.2g). See ref 33. Murphy Nature Pro. 2017.

3) 70mOsm is a high degree of osmotic stress. How confident are the authors that a cell health is maintained under this condition and b. this does indeed induce membrane stretch? For example, does this stimulation activate TREK-1?

Response: Yes, osmotic swell activates TREK1. This was shown in ref 19 (Patel et al 1998). We agree the 70 mOsm is a high degree of stress. This needs to be stated better in the paper.

Reviewer #2 (Public Review):

This manuscript by Petersen and colleagues investigates the mechanistic underpinnings of activation of the ion channel TREK-1 by mechanical inputs (fluid shear or membrane stretch) applied to cells. Using a combination of super-resolution microticopy, pair correlation analysis and electrophysiology, the authors show that the application of shear to a cell can lead to changes in the distribution of TREK-1 and the enzyme PhospholipaseD2 (PLD2), relative to lipid domains defined by either GM1 or PIP2. The activation of TREK-1 by mechanical stimuli was shown to be sensi>zed by the presence of PLD2, but not a catalytically dead xPLD2 mutant. In addition, the activity of PLD2 is increased when the molecule is more associated with PIP2, rather than GM1 defined lipid domains. The presented data do not exclude direct mechanical activation of TREK-1, rather suggest a modulation of TREK-1 activity, increasing sensitivity to mechanical inputs, through an inherent mechanosensitivity of PLD2 activity. The authors additionally claim that PLD2 can regulate transduction thresholds in vivo using Drosophila melanogaster behavioural assays. However, this section of the manuscript overstates the experimental findings, given that it is unclear how the disruption of PLD2 is leading to behavioural changes, given the lack of a TREK-1 homologue in this organism and the lack of supporting data on molecular function in the relevant cells.

Response: We agree, the downstream effectors of PLD2 mechanosensitivity are not known in the fly. Other anionic lipids have been shown to mediate pain see ref 46 and 47. We do not wish to make any claim beyond PLD2 being an in vivo contributor to a fly’s response to mechanical force. We have removed the speculative conclusions about fly thresholds from the abstract.

That said we do believe we have established a molecular function at the cellular level. We showed PLD is robustly mechanically activated in a cultured fly cell line (BG2-c2) Figure 6a of the manuscript. And our previous publication established mechanosensation of PLD (Petersen et. al. Nature Com 2016) through mechanical disruption of the lipids. At a minimum, the experiments show PLDs mechanosensitivity is evolutionarily better conserved across species than TREK1.

This work will be of interest to the growing community of scientists investigating the myriad mechanisms that can tune mechanical sensitivity of cells, providing valuable insight into the role of functional PLD2 in sensi>zing TREK-1 activation in response to mechanical inputs, in some cellular systems.

The authors convincingly demonstrate that, post application of shear, an alteration in the distribution of TREK-1 and mPLD2 (in HEK293T cells) from being correlated with GM1 defined domains (no shear) to increased correlation with PIP2 defined membrane domains (post shear). These data were generated using super-resolution microticopy to visualise, at sub diffraction resolution, the localisation of labelled protein, compared to labelled lipids. The use of super-resolution imaging enabled the authors to visualise changes in cluster association that would not have been achievable with diffraction limited microticopy. However, the conclusion that this change in association reflects TREK-1 leaving one cluster and moving to another overinterprets these data, as the data were generated from sta>c measurements of fixed cells, rather than dynamic measurements capturing molecular movements.

When assessing molecular distribution of endogenous TREK-1 and PLD2, these molecules are described as "well correlated: in C2C12 cells" however it is challenging to assess what "well correlated" means, precisely in this context. This limitation is compounded by the conclusion that TREK-1 displayed little pair correlation with GM1 and the authors describe a "small amount of TREK-1 trafficked to PIP2". As such, these data may suggest that the findings outlined for HEK293T cells may be influenced by artefacts arising from overexpression.

The changes in TREK-1 sensitivity to mechanical activation could also reflect changes in the amount of TREK-1 in the plasma membrane. The authors suggest that the presence of a leak currently accounts for the presence of TREK-1 in the plasma membrane, however they do not account for whether there are significant changes in the membrane localisation of the channel in the presence of mPLD2 versus xPLD2. The supplementary data provide some images of fluorescently labelled TREK-1 in cells, and the authors state that truncating the c-terminus has no effect on expression at the plasma membrane, however these data provide inadequate support for this conclusion. In addition, the data reporting the P50 should be noted with caution, given the lack of saturation of the current in response to the stimulus range.

Response: We thank the reviewer for his/her concern about expression levels. We did test TREK-1 expression. mPLD decreases TREK-1 expression ~two-fold (see Author response image 2 below). We did not include the mPLD data since TREK-1 was mechanically activated with mPLD. For expression to account for the loss of TREK-1 stretch current (Figure 1b), xPLD would need to block surface expression of TREK-1 prior to stretch. The opposite was true, xPLD2 increased TREK-1 expression (see Figure S2c). Furthermore, we tested the leak current of TREK-1 at 0 mV and 0 mmHg of stretch. Basal leak current was no different with xPLD2 compared to endogenous PLD (Figure 1d; red vs grey bars respectively) suggesting TREK-1 is in the membrane and active when xPLD2 is present. If anything, the magnitude of the effect with xPLD would be larger if the expression levels were equal.

Author response image 2.

TREK expression at the plasma membrane. TREK-1 Fluorescence was measured by GFP at points along the plasma membrane. Over expression of mouse PLD2 (mPLD) decrease the amount of full-length TREK-1 (FL TREK) on the surface more than 2-fold compared to endogenously expressed PLD (enPLD) or truncated TREK (TREKtrunc) which is missing the PLD binding site in the C-terminus. Over expression of mPLD had no effect on TREKtrunc.

Finally, by manipulating PLD2 in D. melanogaster, the authors show changes in behaviour when larvae are exposed to either mechanical or electrical inputs. The depletion of PLD2 is concluded to lead to a reduction in activation thresholds and to suggest an in vivo role for PA lipid signaling in setting thresholds for both mechanosensitivity and pain. However, while the data provided demonstrate convincing changes in behaviour and these changes could be explained by changes in transduction thresholds, these data only provide weak support for this specific conclusion. As the authors note, there is no TREK-1 in D. melanogaster, as such the reported findings could be accounted for by other explanations, not least including potential alterations in the activation threshold of Nav channels required for action potential generation. To conclude that the outcomes were in fact mediated by changes in mechanotransduction, the authors would need to demonstrate changes in receptor potential generation, rather than deriving conclusions from changes in behaviour that could arise from alterations in resting membrane potential, receptor potential generation or the activity of the voltage gated channels required for action potential generation.

Response: We are willing to restrict the conclusion about the fly behavior as the reviewers see fit. We have shown PLD is mechanosensitivity in a fly cell line, and when we knock out PLD from a fly, the animal exhibits a mechanosensation phenotype. We tried to make it clear in the figure and in the text that we have no evidence of a particular mechanism downstream of PLD mechanosensation.

This work provides further evidence of the astounding flexibility of mechanical sensing in cells. By outlining how mechanical activation of TREK-1 can be sensitised by mechanical regulation of PLD2 activity, the authors highlight a mechanism by which TREK-1 sensitivity could be regulated under distinct physiological conditions.

Reviewer #3 (Public Review):

The manuscript "Mechanical activation of TWIK-related potassium channel by nanoscopic movement and second messenger signaling" presents a new mechanism for the activation of TREK-1 channel. The mechanism suggests that TREK1 is activated by phosphatidic acids that are produced via a mechanosensitive motion of PLD2 to PIP2-enriched domains. Overall, I found the topic interesting, but several typos and unclarities reduced the readability of the manuscript. Additionally, I have several major concerns on the interpretation of the results. Therefore, the proposed mechanism is not fully supported by the presented data. Lastly, the mechanism is based on several previous studies from the Hansen lab, however, the novelty of the current manuscript is not clearly stated. For example, in the 2nd result section, the authors stated, "fluid shear causes PLD2 to move from cholesterol dependent GM1 clusters to PIP2 clusters and this activated the enzyme". However, this is also presented as a new finding in section 3 "Mechanism of PLD2 activation by shear."

For PLD2 dependent TREK-1 activation. Overall, I found the results compelling. However, two key results are missing.

1. Does HEK cells have endogenous PLD2? If so, it's hard to claim that the authors can measure PLD2-independent TREK1 activation.

Response: yes, there is endogenous PLD (enPLD). We calculated the relative expression of xPLD2 vs enPLD. xPLD2 is >10x more abundant (Fig. S3d of Pavel et al PNAS 2020, ref 14 of the current manuscript). Hence, as with anesthetic sensitivity, we expect the xPLD to out compete the endogenous PLD, which is what we see. We added the following sentence and reference : “The xPLD2 expression is >10x the endogenous PLD2 (enPLD2) and out computes the TREK-1 binding site for PLD25.”

1. Does the plasma membrane trafficking of TREK1 remain the same under different conditions (PLD2 overexpression, truncation)? From Figure S2, the truncated TREK1 seem to have very poor trafficking. The change of trafficking could significantly contribute to the interpretation of the data in Figure 1.

Response: If the PLD2 binding site is removed (TREK-1trunc), yes, the trafficking to the plasma membrane is unaffected by the expression of xPLD and mPLD (Author response image 2 above). For full length TREK1 (FL-TREK-1), co-expression of mPLD decreases TREK expression (Author response image 2) and coexpression with xPLD increases TREK expression (Figure S2f). This is exactly opposite of what one would expect if surface expression accounted for the change in pressure currents. Hence, we conclude surface expression does not account for loss of TREK-1 mechanosensitivity with xPLD2. A few sentences was added to the discussion. We also performed dSTORM on the TREKtruncated using EGFP. TREK-truncated goes to PIP2 (see figure 2 of 6)

Author response image 3.

To better compare the levels of TREK-1 before and after shear, we added a supplemental figure S2f where the protein was compared simultaneously in all conditions. 15 min of shear significantly decreased TREK-1 except with mPLD2 where the levels before shear were already lowest of all the expression levels tested.

For shear-induced movement of TREK1 between nanodomains. The section is convincing, however I'm not an expert on super-resolution imaging. Also, it would be helpful to clarify whether the shear stress was maintained during fixation. If not, what is the >me gap between reduced shear and the fixed state. lastly, it's unclear why shear flow changes the level of TREK1 and PIP2.

Response: Shear was maintained during the fixing. xPLD2 blocks endocytosis, presumably endocytosis and or release of other lipid modifying enzymes affect the system. The change in TREK-1 levels appears to be directly through an interaction with PLD as TREK trunc is not affected by over expression of xPLD or mPLD.

For the mechanism of PLD2 activation by shear. I found this section not convincing. Therefore, the question of how does PLD2 sense mechanical force on the membrane is not fully addressed. Par>cularly, it's hard to imagine an acute 25% decrease cholesterol level by shear - where did the cholesterol go? Details on the measurements of free cholesterol level is unclear and additional/alternative experiments are needed to prove the reduction in cholesterol by shear.

Response: The question “how does PLD2 sense mechanical force on the membrane” we addressed and published in Nature Comm. In 2016. The title of that paper is “Kinetic disruption of lipid rafts is a mechanosensor for phospholipase D” see ref 13 Petersen et. al. PLD is a soluble protein associated to the membrane through palmitoylation. There is no transmembrane domain, which narrows the possible mechanism of its mechanosensation to disruption.

The Nature Comm. reviewer identified as “an expert in PLD signaling” wrote the following of our data and the proposed mechanism:

“This is a provocative report that identi0ies several unique properties of phospholipase D2 (PLD2). It explains in a novel way some long established observations including that the enzyme is largely regulated by substrate presentation which 0its nicely with the authors model of segregation of the two lipid raft domains (cholesterol ordered vs PIP2 containing). Although PLD has previously been reported to be involved in mechanosensory transduction processes (as cited by the authors) this is the 0irst such report associating the enzyme with this type of signaling... It presents a novel model that is internally consistent with previous literature as well as the data shown in this manuscript. It suggests a new role for PLD2 as a force transduction tied to the physical structure of lipid rafts and uses parallel methods of disrup0on to test the predic0ons of their model.”

Regarding cholesterol. We use a fluorescent cholesterol oxidase assay which we described in the methods. This is an appropriate assay for determining cholesterol levels in a cell which we use routinely. We have published in multiple journals using this method, see references 28, 30, 31. Working out the metabolic fate of cholesterol after sheer is indeed interesting but well beyond the scope of this paper. Furthermore, we indirectly confirmed our finding using dSTORM cluster analysis (Figure 3d-e). The cluster analysis shows a decrease in GM1 cluster size consistent with our previous experiments where we chemically depleted cholesterol and saw a similar decrease in cluster size (see ref 13). All the data are internally consistent, and the cholesterol assay is properly done. We see no reason to reject the data.

Importantly, there is no direct evidence for "shear thinning" of the membrane and the authors should avoid claiming shear thinning in the abstract and summary of the manuscript.

Response: We previously established a kinetic model for PLD2 activation see ref 13 (Petersen et al Nature Comm 2016). In that publication we discussed both entropy and heat as mechanisms of disruption. Here we controlled for heat which narrowed that model to entropy (i.e., shear thinning) (see Figure 3c). We provide an overall justification below. But this is a small refinement of our previous paper, and we prefer not to complicate the current paper. We believe the proper rheological term is shear thinning. The following justification, which is largely adapted from ref 13, could be added to the supplement if the reviewer wishes.

Justification: To establish shear thinning in a biological membrane, we initially used a soluble enzyme that has no transmembrane domain, phospholipase D2 (PLD2). PLD2 is a soluble enzyme and associated with the membrane by palmitate, a saturated 16 carbon lipid attached to the enzyme. In the absence of a transmembrane domain, mechanisms of mechanosensation involving hydrophobic mismatch, tension, midplane bending, and curvature can largely be excluded. Rather the mechanism appears to be a change in fluidity (i.e., kinetic in nature). GM1 domains are ordered, and the palmate forms van der Waals bonds with the GM1 lipids. The bonds must be broken for PLD to no longer associate with GM1 lipids. We established this in our 2016 paper, ref 13. In that paper we called it a kinetic effect, however we did not experimentally distinguish enthalpy (heat) vs. entropy (order). Heat is Newtonian and entropy (i.e., shear thinning) is non-Newtonian. In the current study we paid closer attention to the heat and ruled it out (see Figure 3c and methods). We could propose a mechanism based on kinetic disruption, but we know the disruption is not due to melting of the lipids (enthalpy), which leaves shear thinning (entropy) as the plausible mechanism.

The authors should also be aware that hypotonic shock is a very dirty assay for stretching the cell membrane. Ouen, there is only a transient increase in membrane tension, accompanied by many biochemical changes in the cells (including acidification, changes of concentration etc). Therefore, I would not consider this as definitive proof that PLD2 can be activated by stretching membrane.

Response: Comment noted. We trust the reviewer is correct. In 1998 osmotic shock was used to activate the channel. We only intended to show that the system is consistent with previous electrophysiologic experiments.

References cited:

1 Du G, Huang P, Liang BT, Frohman MA. Phospholipase D2 localizes to the plasma membrane and regulates angiotensin II receptor endocytosis. Mol Biol Cell 2004;15:1024–30. htps://doi.org/10.1091/mbc.E03-09-0673.

2 Koch T, Wu DF, Yang LQ, Brandenburg LO, Höllt V. Role of phospholipase D2 in the agonist-induced and constistutive endocytosis of G-protein coupled receptors. J Neurochem 2006;97:365–72. htps://doi.org/10.1111/j.1471-4159.2006.03736.x.

3 Wheeler DS, Underhill SM, Stolz DB, Murdoch GH, Thiels E, Romero G, et al. Amphetamine activates Rho GTPase signaling to mediate dopamine transporter internalization and acute behavioral effects of amphetamine. Proc Natl Acad Sci U S A 2015;112:E7138–47. htps://doi.org/10.1073/pnas.1511670112.

4 Rankovic M, Jacob L, Rankovic V, Brandenburg L-OO, Schröder H, Höllt V, et al. ADP-ribosylation factor 6 regulates mu-opioid receptor trafficking and signaling via activation of phospholipase D2. Cell Signal 2009;21:1784–93. htps://doi.org/10.1016/j.cellsig.2009.07.014.

5 Pavel MA, Petersen EN, Wang H, Lerner RA, Hansen SB. Studies on the mechanism of general anesthesia. Proc Natl Acad Sci U S A 2020;117:13757–66. htps://doi.org/10.1073/pnas.2004259117.

6 Call IM, Bois JL, Hansen SB. Super-resolution imaging of potassium channels with genetically encoded EGFP. BioRxiv 2023. htps://doi.org/10.1101/2023.10.13.561998.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, James Lee, Lu Bai, and colleagues use a multifaceted approach to investigate the relationship between transcription factor condensate formation, transcription, and 3D gene clustering of the MET regulon in the model organism S. cerevisiae. This study represents a second clear example of inducible transcriptional condensates in budding yeast, as most evidence for transcriptional condensates arises from studies of mammalian systems. In addition, this study links the genomic location of transcriptional condensates to the potency of transcription of a reporter gene regulated by the master transcription factor contained in the condensate. The strength of evidence supporting these two conclusions is strong. Less strong is evidence supporting the claim that Met4-containing condensates mediate the clustering of genes in the MET regulon.

Strengths:

The manuscript is for the most part clearly written, with the overriding model and specific hypothesis being tested clearly explained. Figure legends are particularly well written. An additional strength of the manuscript is that most of the main conclusions are supported by the data. This includes the propensity of Met4 and Met32 to form puncta-like structures under inducing conditions, formation of Met32-containing LLPS-like droplets in vitro (within which Met4 can colocalize), colocalization of Met4-GFP with Met4-target genes under inducing conditions, enhanced transcription of a Met3pr-GFP reporter when targeted within 1.5 - 5 kb of select Met4 target genes, and most impressively, evidence that several MET genes appear to reposition under transcriptionally inducing conditions. The latter is based on a recently reported novel in vivo methylation assay, MTAC, developed by the Bai lab.

Weaknesses:

My principal concern is that the authors fail to show convincing evidence for a key conclusion, highlighted in the title, that nuclear condensates per se drive MET gene clustering. Figure 4E demonstrates that Met4 molecules, not condensates per se, are necessary for fostering distant cis and trans interactions between MET6 and three other Met4 targets under -met inducing conditions. In addition, the paper would be strengthened by discussing a recent study conducted in yeast that comes to many of the same conclusions reported here, including the role of inducible TF condensates in driving 3D genome reorganization (Chowdhary et al, Mol. Cell 2022).

Following the reviewer’s advice, we carried out MTAC with the VP near MET6 in WT Met4 and ΔIDR2.3 strains (results shown below). The conclusions are somewhat ambiguous. For long-distance interactions with MUP1, YKG9, STR3, and MET13, we indeed observe decreased MTAC signals close to background levels in the ΔIDR2.3 strain, which aligns with the model suggesting that Met4 condensation promotes clustering among Met4 targeted genes. However, we also noticed significant decreases in the local MTAC signals (HIS3 and MET6). It is possible that the changes in Met4 condensates alter the chromosomal folding near MET6, thereby affecting the local MTAC signals. Alternatively, LacI-M.CviPI (the methyltransferase) could be induced to a lesser extent in the ΔIDR2.3 strain, leading to a genome-wide decrease in MTAC signals. Due to this ambiguity, we decided not to include the following plot in the main figure.

Author response image 1.

We discussed Hsf1 and added the suggested reference on page 13.

Other concerns:

(1) A central premise of the study is that the inducible formation of condensates underpins the induction of MET gene transcription and MET gene clustering. Yet, Figure 1 suggests (and the authors acknowledge) that puncta-like Met4-containing structures pre-exist in the nuclei of non-induced cells. Thus, the transcription and gene reorganization observed is due to a relatively modest increase in condensate-like structures. Are we dealing with two different types of Met4 condensates? (For example, different combinations of Met4 with its partners; Mediator- or Pol II-lacking vs. Mediator- or Pol II-containing; etc.?) At the very least, a comment to this effect is necessary.

Although Met4 can form smaller puncta in the +met condition (Figure 1A), it cannot be recruited to its target genes due to the absence of its sequence-specific binding partners, Met31 and Met32 (these two factors are actively degraded in the +met condition). Consistently, in the +met condition, Met4 shows extremely low genome-wide ChIP signals (Figure 3C). Therefore, these Met4 puncta in +met do not have organize the 3D genome or have gene regulatory functions. This discussion is added on page 12.

(2) Using an in vitro assay, the authors demonstrate that Met4 colocalizes with Met32 LLPS droplets (Figure 2F). Is the same true in vivo - that is, is Met32 required for Met4 condensation? This could be readily tested using auxin-induced degradation of Met32. Along similar lines, the claim that Met32 is required for MET gene clustering (line 250) requires auxin-induced degradation of this protein.

As the reviewer pointed out above, cells in the +met condition also show small Met4 puncta. In this condition, Met32 is essentially undetectable (Met31 level is even lower and remains undetectable even in the -met conditions). Therefore, Met4 does not strictly require the presence of Met32 in vivo (may require other factors or modifications). Met4 does not have DNA-binding activity, and therefore it cannot target and organize chromosomes on its own. Although we did not do the Met32 degradation experiment, we measured the 3D genome conformation in +met and showed that there are no detectable interactions among Met4 target genes.

(3) The authors use a single time point during -met induction (2 h) to evaluate TF clustering, transcription (mRNA abundance), and 3D restructuring. It would be informative to perform a kinetic analysis since such an analysis could reveal whether TF clustering precedes transcriptional induction or MET gene repositioning. Do the latter two phenomena occur concurrently or does one precede the other?

We appreciate the reviewer’s insightful question. It is indeed intriguing to consider whether TF clustering precedes transcriptional induction and MET gene clustering. However, as mentioned on page 12 of our manuscript, this experiment poses significant challenges. The low intensities of the Met4 and Met32 signals necessitate high excitation for imaging, which also makes them prone to photo-bleaching. Consequently, we have been unable to measure the dynamics of Met4 and Met32 puncta in vivo, let alone co-image them with DNA/RNA. Undertaking this experiment will require considerable effort, which we plan to pursue in the future.

(4) Based on the MTAC assay, MET13 does not appear to engage in trans interactions with other Met4 targets, whereas MET6 does (Figures 4C and 4E). Does this difference stem from the greater occupancy of Met4 at MET6 vs. MET13, greater association of another Met co-factor with the chromatin of MET6 vs. MET13, or something else?

We were also surprised by this result, given that MET13 emerged as one of the strongest transcriptional hotspots in our previous screen. It also exhibits one of the highest Met4 ChIP signals and is closely associated with the nuclear pore complex. Our earlier findings indicate that DNA dynamics near the VP significantly influence the MTAC signal; specifically, a VP with constrained motion is less effective at methylating interacting sites (Li et al., 2024). Therefore, it is plausible that MET13 is associated with a large Met4 condensate, which constrains the motion of nearby chromatin and diminishes MTAC efficiency.

Reviewer #2 (Public Review):

Summary:

This manuscript combines live yeast cell imaging and other genomic approaches to study how transcription factor (TF) condensates might help organize and enhance the transcription of the target genes in the methionine starvation response pathway. The authors show that the TFs in this response can form phase-separated condensates through their intrinsically disordered regions (IDRs), and mediate the spatial clustering of the related endogenous genes as well as reporter inserted near the endogenous target loci.

Strengths:

This work uses rigorous experimental approaches, such as imaging of endogenously labeled TFs, determining expression and clustering of endogenous target genes, and reporter integration near the endogenous target loci. The importance of TFs is shown by rapid degradation. Single-cell data are combined with genomic sequencing-based assays. Control loci engineered in the same way are usually included. Some of these controls are very helpful in showing the pathway-specific effect of the TF condensates in enhancing transcription.

Weaknesses:

Perhaps the biggest weakness of this work is that the role of IDR and phase separation in mediating the target gene clustering is unclear. This is an important question. TF IDRs may have many functions including mediating phase separation and binding to other transcriptional molecules (not limited to proteins and may even include RNAs). The effect of IDR deletion on reduced Fano number in cells could come from reduced binding with other molecules. This should be tested on phase separation of the purified protein after IDR deletion. Also, the authors have not shown IDR deletion affects the clustering of the target genes, so IDR deletion may affect the binding of other molecules (not the general transcription machinery) that are specifically important for target gene transcription. If the self-association of the IDR is the main driving force of the clustering and target gene transcription enhancement, can one replace this IDR with totally unrelated IDRs that have been shown to mediate phase separation in non-transcription systems and still see the gene clustering and transcription enhancement effects? This work has all the setup to test this hypothesis.

We thank the reviewer for raising this point, and we tried more in vitro and in vivo experiments with Met4 IDR deletions. See the answer to Reviewer 1 for the in vivo 3D mapping experiment.

We purified Met4-ΔIDR2 with an MBP tag, but its low yield made labeling and conducting thorough experiments challenging. At concentrations above ~10 μM, the protein tends to aggregate, while at lower concentrations, it remains diffusive in solution and does not form condensates. When we mixed purified Met4-ΔIDR2 with Met32, we observed reduced partitioning inside Met32 condensates compared to the full-length Met4. As the reviewer noted, this diminished interaction may contribute to the decreased puncta formation observed in vivo. This result is added to the manuscript on page 11 and supplementary figure 5.

The Met4 protein was tagged with MBP but Met 32 was not. MBP tag is well known to enhance protein solubility and prevent phase separation. This made the comparison of their in vitro phase behavior very different and led the authors to think that maybe Met32 is the scaffold in the co-condensates. If MBP was necessary to increase yield and solubility during expression and purification, it should be cleaved (a protease cleavage site should be engineered) to allow phase separation in vitro.

Following the reviewer’s advice, we purified Met4-TEV-MBP so that the MBP can be cleaved off. Unfortunately, concentrated Met4-TEV-MBP needs to be stored at high salt (400mM) to be soluble. When exchanged into a suitable buffer for TEV cleavage (≤200 mM NaCl), nearly all soluble protein aggregates. Attempts to digest the protein in storage buffer results in observable aggregation before significant cleavage (see below).  

Author response image 2.

Are ATG36 and LDS2 also supposed to be induced by -met? This should be explained clearly. The signals are high at -met.

Genomic loci ATG36 and LDS2 were chosen as controls because they are not bound by Met TFs (ChIP-seq tracks) and their expressions are not induced by -met (RNA-seq data). This information is added to the manuscript on page 9. When MET3pr-GFP reporter is inserted into these loci, GFP is induced by -met (because it is driven by the MET3 promoter), but the induction level is less than the same reporter inserted into the transcriptional hotspot like MET13 and MET6 (Figure 6E, also see Du et al., Plos Genetics, 2017).

ChIP-seq data:

Author response image 3.

RNA-seq counts:

Author response table 1.

Figure 6B, the Met4-GFP seems to form condensates at all three loci without a very obvious difference, though 6C shows a difference. 6C is from only one picture each. The authors should probably quantify the signals from a large number of randomly selected pictures (cells) and do statistics.

If we understand this comment correctly, the reviewer is referring to the fact that all three loci in Figure 6B appear to show a peak in GFP intensity. This pattern emerges because these images are averaged among many cells (number of cells analyzed in 6B has been added to the Figure legends). GFP intensities near the center will always be higher because peripheral pixels are more likely to fall outside the nuclei boundaries, where Met4 signals are absent (same as in Figure 3F). Importantly, MET6 locus shows higher intensity near the center in comparison to PUT1 and ATG36, indicating its co-localization with Met4 condensates.

Reviewer #3 (Public Review):

Summary:

In this study, the authors probe the connections between clustering of the Met4/32 transcription factors (TFs), clustering of their regulatory targets, and transcriptional regulation. While there is an increasing number of studies on TF clustering in vitro and in vivo, there is an important need to probe whether clustering plays a functional role in gene expression. Another important question is whether TF clustering leads to the clustering of relevant gene targets in vivo. Here the authors provide several lines of evidence to make a compelling case that Met4/32 and their target genes cluster and that this leads to an increase in transcription of these genes in the induced state. First, they found that, in the induced state, Met4/32 forms co-localized puncta in vivo. This is supported by in vitro studies showing that these TFs can form condensates in vitro with Med32 being the driver of these condensates. They found that two target genes, MET6 and MET13 have a higher probability of being co-localized with Met4 puncta compared with non-target loci. Using a targeted DNA methylation assay, they found that MET13 and MET6 show Met4-dependent long-range interactions with other Met4-regulated loci, consistent with the clustering of at least some target genes under induced conditions. Finally, by inserting a Met4-regulated reporter gene at variable distances from MET6, they provide evidence that insertion near this gene is a modest hotspot for activity.

Weaknesses:

(1) Please provide more information on the assay for puncta formation (Figure 1). It's unclear to me from the description provided how this assay was able to quantitate the number of puncta in cells.

Due to the variation in puncta size and intensity (as illustrated in Figure 1A), counting the number of puncta would be highly subjective with arbitrary cutoffs. Therefore, we chose to calculate the CV and Fano values instead, which are unbiased measures. Proteins that form puncta will exhibit greater pixel-to-pixel variations in GFP intensity, resulting in higher CV and Fano values.

(2) How does the number of puncta in cells correspond with the number of Met-regulated genes? What are the implications of this calculation?

As previously mentioned, defining the exact number of Met4 puncta is challenging. The number of puncta does not necessarily have one-to-one correspondence to the number of Met4 target genes. Some puncta may not be associated with chromosomes, while others may interact with multiple genes.

(3) A control for chromosomal insertion of the Met-regulated reporter was a GAL4 promoter derivative reporter. However, this control promoter seems 5-10 fold more active than the Met-regulated promoter (Figure 6). It's possible that the high activity from the control promoter overcomes some other limiting step such that chromosomal location isn't important. It would be ideal if the authors used a promoter with comparable activity to the Met-reporter as a control.

We agree with the reviewer that it will be better to use another promoter with comparable activity. Indeed, this was our rationale for selecting the attenuated GAL1 promoter over the WT version; however, it still exhibited substantially higher activity than the MET3pr. Unfortunately, we do not have a promoter from a different pathway that is calibrated to match the activity level of MET3pr. Nonetheless, MET17pr has much higher activity (~3 fold) than MET3pr, and we observed similar degree of stimulus from the hotspot in comparison to the control locus for both promoters (1.5-2-fold increase in GFP expression) (Figure 6E & F). This suggests that the observed effects are more likely to depend on the activation pathway and TF identity rather than the promoter strength.

(4) It seems like transcription from a very large number of genes is altered in the Met4 IDR mutant (Figure 7F). Why is this and could this variability affect the conclusions from this experiment?

We agree with the reviewer that ΔIDR 2.3 truncation affects the expression of 2711 (P-adj <0.05) genes (1339 up,1372 down). We suspect that this is due to the decreased expression of Met4 target genes, leading to altered levels of methionine and other sulfur-containing metabolites. Such changes would have a global impact on gene expression. Importantly, despite the similar number of genes that show up vs down regulation in the ΔIDR 2.3 strain, almost all Met4 targets showed decreased expression (Fig 7F). This supports the model where Met4 condensates lead to increased expression in its target genes.

Recommendations for the authors:

Reviewer #1 (Recommendations for The Authors):

(1) The introduction contains multiple miscitations. Rather than gene clustering, most of the studies and reviews cited (e.g., lines 35-39) report interactions between genomic loci (E-E, E-P, and P-P). There are other claims not supported by the papers cited. Moreover, the authors lump together original research papers and reviews within a given group without distinguishing which is which.

We thank the reviewer for pointing this out. We reorganized the references in the introduction.

(2) One option to address the concern regarding the lack of evidence that nuclear condensates per se drive MET gene clustering is to test the impact of Met4 ΔIDR2.3 on MTAC signals.

We carried out the suggested experiment. See answer above (Reviewer #1, Question #1).

(3) Authors claim that there are significant differences between values depicted in Figures 1B and 3G. Statistical tests are necessary to show this.

Significance values were calculated in comparison to free GFP using two-tailed Student’s t-test in 1B,1C, and 3G. The corresponding figure legends are updated.

(4) How are the data in Figures 3F, G, and 6B, C generated? This is unclear from the information provided in the Figure legends and Materials and Methods.

For each cell, we projected the highest mCherry and GFP intensity at each pixel for all z positions onto a 2D plane (MIP). The MIP images were aligned with the mCherry dot at the center and averaged among all cells. To calculate the GFP intensities like in Figure 3G and 6C, a single line was drawn across the center and the GFP profile was analyzed by ImageJ. We now describe this in the corresponding figure legends, and the Materials and Methods are also updated.

(5) Typos/ unclear writing: lines 24, 58, 79, 82, 84, 96, 117, 121, 131, 142, 147, 161 (terminus, not "terminal"), 250, 325, 349, 761 (was, not "are"). For several of these: "condense" is not "condensate"; for many others: inappropriate use of "the". Supplementary Figure 1 legend: not "a single nuclei" instead "a single nucleus".

We thank the reviewer for pointing this out. We tried our best to correct grammatical errors.

(6) Define GAL1Spr (Figure 6F).

The GAL1S promoter is an attenuated GAL1 promoter that lacks two out of the four Gal4 binding site. The original paper is now cited in the manuscript on page 10.  

(7) Figure 7B, C: there appears to be an inconsistency between the image and bar graph value for ΔIDR3.

The Fano values calculated in 7C are averaged among a population of cells (we added the cell numbers to the legend), while the image in 7B is an example of an individual nucleus. There is some cell-to-cell variability in how the Met4 appears. To be more representative, we chose a different image for ΔIDR3.

(8) Supplementary Tables: use descriptive titles for file names.

This is corrected.

Reviewer #2 (Recommendations For The Authors):

Minor:

Figure 4F is not cited in the text, and the color legend seems wrong for targeted and control.

Figure 4F is now cited in the text. The labels were corrected.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Mackie and colleagues compare chemosensory preferences between C. elegans and P. pacificus, and the cellular and molecular mechanisms underlying them. The nematodes have overlapping and distinct preferences for different salts. Although P. pacificus lacks the lsy-6 miRNA important for establishing asymmetry of the left/right ASE salt-sensing neurons in C. elegans, the authors find that P. pacificus ASE homologs achieve molecular (receptor expression) and functional (calcium response) asymmetry by alternative means. This work contributes an important comparison of how these two nematodes sense salts and highlights that evolution can find different ways to establish asymmetry in small nervous systems to optimize the processing of chemosensory cues in the environment.

Strengths:

The authors use clear and established methods to record the response of neurons to chemosensory cues. They were able to show clearly that ASEL/R are functionally asymmetric in P. pacificus, and combined with genetic perturbation establish a role for che-1-dependent gcy-22.3 in in the asymmetric response to NH₄Cl.

Weaknesses:

The mechanism of lsy-6-independent establishment of ASEL/R asymmetry in P. pacificus remains uncharacterized.

We thank the reviewer for recognizing the novel contributions of our work in revealing the existence of alternative pathways for establishing neuronal lateral asymmetry without the lsy-6 miRNA in a divergent nematode species. We are certainly encouraged now to search for genetic factors that alter the exclusive asymmetric expression of gcy-22.3.

Reviewer #2 (Public review):

Summary:

In this manuscript, Mackie et al. investigate gustatory behavior and the neural basis of gustation in the predatory nematode Pristionchus pacificus. First, they show that the behavioral preferences of P. pacificus for gustatory cues differ from those reported for C. elegans. Next, they investigate the molecular mechanisms of salt sensing in P. pacificus. They show that although the C. elegans transcription factor gene che-1 is expressed specifically in the ASE neurons, the P. pacificus che-1 gene is expressed in the Ppa-ASE and Ppa-AFD neurons. Moreover, che-1 plays a less critical role in salt chemotaxis in P. pacificus than C. elegans. Chemogenetic silencing of Ppa-ASE and Ppa-AFD neurons results in more severe chemotaxis defects. The authors then use calcium imaging to show that both Ppa-ASE and Ppa-AFD neurons respond to salt stimuli. Calcium imaging experiments also reveal that the left and right Ppa-ASE neurons respond differently to salts, despite the fact that P. pacificus lacks lsy-6, a microRNA that is important for ASE left/right asymmetry in C. elegans. Finally, the authors show that the receptor guanylate cyclase gene Ppa-gcy-23.3 is expressed in the right Ppa-ASE neuron (Ppa-ASER) but not the left Ppa-ASE neuron (Ppa-ASEL) and is required for some of the gustatory responses of Ppa-ASER, further confirming that the Ppa-ASE neurons are asymmetric and suggesting that Ppa-GCY-23.3 is a gustatory receptor. Overall, this work provides insight into the evolution of gustation across nematode species. It illustrates how sensory neuron response properties and molecular mechanisms of cell fate determination can evolve to mediate species-specific behaviors. However, the paper would be greatly strengthened by a direct comparison of calcium responses to gustatory cues in C. elegans and P. pacificus, since the comparison currently relies entirely on published data for C. elegans, where the imaging parameters likely differ. In addition, the conclusions regarding Ppa-AFD neuron function would benefit from additional confirmation of AFD neuron identity. Finally, how prior salt exposure influences gustatory behavior and neural activity in P. pacificus is not discussed.

Strengths:

(1) This study provides exciting new insights into how gustatory behaviors and mechanisms differ in nematode species with different lifestyles and ecological niches. The results from salt chemotaxis experiments suggest that P. pacificus shows distinct gustatory preferences from C. elegans. Calcium imaging from Ppa-ASE neurons suggests that the response properties of the ASE neurons differ between the two species. In addition, an analysis of the expression and function of the transcription factor Ppa-che-1 reveals that mechanisms of ASE cell fate determination differ in C. elegans and P. pacificus, although the ASE neurons play a critical role in salt sensing in both species. Thus, the authors identify several differences in gustatory system development and function across nematode species.

(2) This is the first calcium imaging study of P. pacificus, and it offers some of the first insights into the evolution of gustatory neuron function across nematode species.

(3) This study addresses the mechanisms that lead to left/right asymmetry in nematodes. It reveals that the ASER and ASEL neurons differ in their response properties, but this asymmetry is achieved by molecular mechanisms that are at least partly distinct from those that operate in C. elegans. Notably, ASEL/R asymmetry in P. pacificus is achieved despite the lack of a P. pacificus lsy-6 homolog.

Weaknesses:

(1) The authors observe only weak attraction of C. elegans to NaCl. These results raise the question of whether the weak attraction observed is the result of the prior salt environment experienced by the worms. More generally, this study does not address how prior exposure to gustatory cues shapes gustatory responses in P. pacificus. Is salt sensing in P. pacificus subject to the same type of experience-dependent modulation as salt sensing in C. elegans?

We tested if starving animals in the presence of a certain salt will result in those animals avoiding it. However, under our experimental conditions we were unable to detect experiencedependent modulation either in P. pacificus or in C. elegans.

Author response image 1.

(2) A key finding of this paper is that the Ppa-CHE-1 transcription factor is expressed in the PpaAFD neurons as well as the Ppa-ASE neurons, despite the fact that Ce-CHE-1 is expressed specifically in Ce-ASE. However, additional verification of Ppa-AFD neuron identity is required. Based on the image shown in the manuscript, it is difficult to unequivocally identify the second pair of CHE-1-positive head neurons as the Ppa-AFD neurons. Ppa-AFD neuron identity could be verified by confocal imaging of the CHE-1-positive neurons, co-expression of Ppa-che1p::GFP with a likely AFD reporter, thermotaxis assays with Ppa-che-1 mutants, and/or calcium imaging from the putative Ppa-AFD neurons.

In the revised manuscript, we provide additional and, we believe, conclusive evidence for our correct identification of Ppa-AFD neuron being another CHE-1 expressing neuron. Specifically, we have constructed and characterized 2 independent reporter strains of Ppa-ttx-1, a putative homolog of the AFD terminal selector in C. elegans. There are two pairs of ttx-1p::rfp expressing amphid neurons. The anterior neuronal pair have finger-like endings that are unique for AFD neurons compared to the dendritic endings of the 11 other amphid neuron pairs (no neuron type has a wing morphology in P. pacificus). Their cell bodies are detected in the newly tagged TTX-1::ALFA strain that co-localize with the anterior pair of che-1::gfp-expressing amphid neurons (n=15, J2-Adult).

We note that the identity of the posterior pair of amphid neurons differs between the ttx-1p::rfp promoter fusion reporter and TTX-1::ALFA strains– the ttx-1p::rfp posterior amphid pair overlaps with the gcy-22.3p::gfp reporter (ASER) but the TTX-1::ALFA posterior amphid pair do not overlap with the posterior pair of che-1::gfp-expressing amphid neurons (n=15). Given that there are 4 splice forms detected by RNAseq (Transcriptome Assembly Trinity, 2016; www.pristionchus.org), this discrepancy between the Ppa-ttx-1 promoter fusion reporter and the endogenous expression of the Ppa-TTX-1 C-terminally tagged to the only splice form containing Exon 18 (ppa_stranded_DN30925_c0_g1_i5, the most 3’ exon) may be due to differential expression of different splice variants in AFD, ASE, and another unidentified amphid neuron types.  

Although we also made reporter strains of two putative AFD markers, Ppa-gcy-8.1 (PPA24212)p::gfp; csuEx101 and Ppa-gcy-8.2 (PPA41407)p::gfp; csuEx100, neither reporter showed neuronal expression.

(3) Loss of Ppa-che-1 causes a less severe phenotype than loss of Ce-che-1. However, the loss of Ppa-che-1::RFP expression in ASE but not AFD raises the question of whether there might be additional start sites in the Ppa-che-1 gene downstream of the mutation sites. It would be helpful to know whether there are multiple isoforms of Ppa-che-1, and if so, whether the exon with the introduced frameshift is present in all isoforms and results in complete loss of Ppa-CHE-1 protein.

According to www.pristionchus.org (Transcriptome Assembly Trinity), there is only a single detectable splice form by RNAseq. Once we have a Ppa-AFD-specific marker, we would be able to determine how much of the AFD terminal effector identify (e.g. expression of gcy-8 paralogs) is effected by the loss of Ppa-che-1 function.

(4) The authors show that silencing Ppa-ASE has a dramatic effect on salt chemotaxis behavior. However, these data lack control with histamine-treated wild-type animals, with the result that the phenotype of Ppa-ASE-silenced animals could result from exposure to histamine dihydrochloride. This is an especially important control in the context of salt sensing, where histamine dihydrochloride could alter behavioral responses to other salts.

We have inadvertently left out this important control. Because the HisCl1 transgene is on a randomly segregating transgene array, we have scored worms with and without the transgene expressing the co-injection marker (Ppa-egl-20p::rfp, a marker in the tail) to show that the presence of the transgene is necessary for the histamine-dependent knockdown of NH₄Br attraction. This control is added as Figure S2.

(5) The calcium imaging data in the paper suggest that the Ppa-ASE and Ce-ASE neurons respond differently to salt solutions. However, to make this point, a direct comparison of calcium responses in C. elegans and P. pacificus using the same calcium indicator is required. By relying on previously published C. elegans data, it is difficult to know how differences in growth conditions or imaging conditions affect ASE responses. In addition, the paper would be strengthened by additional quantitative analysis of the calcium imaging data. For example, the paper states that 25 mM NH₄Cl evokes a greater response in ASEL than 250 mM NH₄Cl, but a quantitative comparison of the maximum responses to the two stimuli is not shown.

We understand that side-by-side comparisons with C. elegans using the same calcium indicator would lend more credence to the differences we observed in P. pacificus versus published findings in C. elegans from the past decades, but are not currently in a position to conduct these experiments in parallel.

(6) It would be helpful to examine, or at least discuss, the other P. pacificus paralogs of Ce-gcy22. Are they expressed in Ppa-ASER? How similar are the different paralogs? Additional discussion of the Ppa-gcy-22 gene expansion in P. pacificus would be especially helpful with respect to understanding the relatively minor phenotype of the Ppa-gcy-22.3 mutants.

In P. pacificus, there are 5 gcy-22-like paralogs and 3 gcy-7-like paralogs, which together form a subclade that is clearly distinct from the 1-1 Cel-gcy-22, Cel-gcy-5, and Cel-gcy-7 orthologs in a phylogenetic tree containing all rGCs in P. pacificus, C. elegans, and C. briggssae (Hong et al, eLife, 2019). In Ortiz et al (2006 and 2009), Cel-gcy-22 stands out from other ASER-type gcy genes (gcy-1, gcy-4, gcy-5) in being located on a separate chromosome (Chr. V) as well as in having a wider range of defects in chemoattraction towards salt ions. Given that the 5 P. pacificus gcy-22-like paralogs are located on 3 separate chromosomes without clear synteny to their C. elegans counterparts, it is likely that the gcy-22 paralogs emerged from independent and repeated gene duplication events after the separation of these Caenorhabditis and Pristionchus lineages. Our reporter strains for two other P. pacificus gcy-22-like paralogs either did not exhibit expression in amphid neurons (Ppa-gcy-22.1p::GFP, ) or exhibited expression in multiple neuron types in addition to a putative ASE neuron (Ppa-gcy-22.4p::GFP). We have expanded the discussion on the other P. pacificus gcy-22 paralogs.

(7) The calcium imaging data from Ppa-ASE is quite variable. It would be helpful to discuss this variability. It would also be helpful to clarify how the ASEL and ASER neurons are being conclusively identified during calcium imaging.

For each animal, the orientation of the nose and vulva were recorded and used as a guide to determine the ventral and dorsal sides of the worm, and subsequently, the left and right sides of the worm. Accounting for the plane of focus of the neuron pairs as viewed through the microscope, it was then determined whether the imaged neuron was the worm’s left or right neuron of each pair. We added this explanation to the Methods.

(8) More information about how the animals were treated prior to calcium imaging would be helpful. In particular, were they exposed to salt solutions prior to imaging? In addition, the animals are in an M9 buffer during imaging - does this affect calcium responses in Ppa-ASE and Ppa-AFD? More information about salt exposure, and how this affects neuron responses, would be very helpful.

Prior to calcium imaging, animals were picked from their cultivation plates (using an eyelash pick to minimize bacteria transfer) and placed in loading solution (M9 buffer with 0.1% Tween20 and 1.5 mM tetramisole hydrochloride, as indicated in the Method) to immobilize the animals until they were visibly completely immobilized.

(9) In Figure 6, the authors say that Ppa-gcy-22.3::GFP expression is absent in the Ppa-che1(ot5012) mutant. However, based on the figure, it looks like there is some expression remaining. Is there a residual expression of Ppa-gcy-22.3::GFP in ASE or possibly ectopic expression in AFD? Does Ppa-che-1 regulate rGC expression in AFD? It would be helpful to address the role of Ppa-che-1 in AFD neuron differentiation.

In Figure 6C, the green signal is autofluorescence in the gut, and there is no GFP expression detected in any of the 55 che-1(-) animals we examined. We are currently developing AFDspecific rGC markers (gcy-8 homologs) to be able to examine the role of Ppa-CHE-1 in regulating AFD identity.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Abstract: 'how does sensory diversity prevail within this neuronal constraint?' - could be clearer as 'numerical constraint' or 'neuron number constraint'.

We have clarified this passage as ‘…constraint in neuron number’.

(2) 'Sensory neurons in the Pristionchus pacificus' - should get rid of the 'the'.

We have removed the ‘the’.

(3) Figure 2: We have had some good results with the ALFA tag using a similar approach (tagging endogenous loci using CRISPR). I'm not sure if it is a Pristionchus thing, or if it is a result of our different protocols, but our staining appears stronger with less background. We use an adaptation of the Finney-Ruvkin protocol, which includes MeOH in the primary fixation with PFA, and overcomes the cuticle barrier with some LN2 cracking, DTT, then H2O2. No collagenase. If you haven't tested it already it might be worth comparing the next time you have a need for immunostaining.

We appreciate this suggestion. Our staining protocol uses paraformaldehyde fixation. We observed consistent and clear staining in only 4 neurons in CHE-1::ALFA animals but more background signals from TTX-1::ALFA in Figure 2I-J in that could benefit from improved immunostaining protocol.

(4) Page 6: 'By crossing the che-1 reporter transgene into a che-1 mutant background (see below), we also found that che-1 autoregulates its own expression (Figure 2F), as it does in C. elegans' - it took me some effort to understand this. It might make it easier for future readers if this is explained more clearly.

We understand this confusion and have changed the wording along with a supporting table with a more detailed account of che-1p::RFP expression in both ASE and AFD neurons in wildtype and che-1(-) backgrounds in the Results.

(5) Line numbers would make it easier for reviewers to reference the text.

We have added line numbers.

(6) Page 7: is 250mM NH₄Cl an ecologically relevant concentration? When does off-target/nonspecific activation of odorant receptors become an issue? Some discussion of this could help readers assess the relevance of the salt concentrations used.

This is a great question but one that is difficult to reconcile between experimental conditions that often use 2.5M salt as point-source to establish salt gradients versus ecologically relevant concentrations that are very heterogenous in salinity. Efforts to show C. elegans can tolerate similar levels of salinity between 0.20-0.30 M without adverse effects have been recorded previously (Hu et al., Analytica Chimica Acta 2015; Mah et al. Expedition 2017).

(7) It would be nice for readers to have a short orientation to the ecological relevance of the different salts - e.g. why Pristionchus has a particular taste for ammonium salts.

Pristionchus species are entomophilic and most frequently found to be associated with beetles in a necromenic manner. Insect cadavers could thus represent sources of ammonium in the soil. Additionally, ammonium salts could represent a biological signature of other nematodes that the predatory morphs of P. pacificus could interpret as prey. We have added the possible ecological relevance of ammonium salts into the Discussion.

(8) Page 11: 'multiple P. pacificus che-1p::GCaMP strains did not exhibit sufficient basal fluorescence to allow for image tracking and direct comparison'. 500ms exposure to get enough signal from RCaMP is slow, but based on the figures it still seems enough to capture things. If image tracking was the issue, then using GCaMP6s with SL2-RFP or similar in conjunction with a beam splitter enables tracking when the GCaMP signal is low. Might be an option for the future.

These are very helpful suggestions and we hope to eventually develop an improved che1p::GCaMP strain for future studies.

(9) Sometimes C. elegans genes are referred to as 'C. elegans [gene name]' and sometimes 'Cel [gene name]'. Should be consistent. Same with Pristionchus.

We have now combed through and corrected the inconsistencies in nomenclature.

(10) Pg 12 - '...supports the likelihood that AFD receives inputs, possibly neuropeptidergic, from other amphid neurons' - the neuropeptidergic part could do with some justification.

Because the AFD neurons are not exposed directly to the environment through the amphid channel like the ASE and other amphid neurons, the calcium responses to salts detected in the AFD likely originate from sensory neurons connected to the AFD. However, because there is no synaptic connection from other amphid neurons to the AFD neurons in P. pacificus (unlike in C. elegans; Hong et al, eLife, 2019), it is likely that neuropeptides connect other sensory neurons to the AFDs. To avoid unnecessary confusion, we have removed “possibly neuropeptidergic.”

(11) Pg16: the link to the Hallam lab codon adaptor has a space in the middle. Also, the paper should be cited along with the web address (Bryant and Hallam, 2021).

We have now added the proper link, plus in-text citation. https://hallemlab.shinyapps.io/Wild_Worm_Codon_Adapter/ (Bryant and Hallem, 2021)

Full citation:

Astra S Bryant, Elissa A Hallem, The Wild Worm Codon Adapter: a web tool for automated codon adaptation of transgenes for expression in non-Caenorhabditis nematodes, G3 Genes|Genomes|Genetics, Volume 11, Issue 7, July 2021, jkab146, https://doi.org/10.1093/g3journal/jkab146

Reviewer #2 (Recommendations for the authors):

(1) In Figure 1, the legend states that the population tested was "J4/L4 larvae and young adult hermaphrodites," whereas in the main text, the population was described as "adult hermaphrodites." Please clarify which ages were tested.

We have tested J4-Adult stage hermaphrodites and have made the appropriate corrections in the text.

(2) The authors state that "in contrast to C. elegans, we find that P. pacificus is only moderately and weakly attracted to NaCl and LiCl, respectively." However, this statement does not reflect the data shown in Figure 1, where there is no significant difference between C. elegans and P. pacificus - both species show at most weak attraction to NaCl.

Although there is no statistically significant difference in NaCl attraction between P. pacificus and C. elegans, NaCl attraction in P. pacificus is significantly lower than its attraction to all 3 ammonium salts when compared to C. elegans. We have rephrased this statement as relative differences in the Results and updated the Figure legend.

(3) In Figure 1, the comparisons between C. elegans and P. pacificus should be made using a two-way ANOVA rather than multiple t-tests. Also, the sample sizes should be stated (so the reader does not need to count the circles) and the error bars should be defined.

We performed the 2-way ANOVA to detect differences between C. elegans and P. pacificus for the same salt and between salts within each species. We also indicated the sample size on the figure and defined the error bars.

Significance:

For comparisons of different salt responses within the same species:

- For C. elegans, NH₄Br vs NH₄Cl (**p<0.01), NH₄Cl vs NH₄I (* p<0.05), and NH₄Cl vs NaCl (* p<0.05). All other comparisons are not significant.

- For P. pacificus, all salts showed (****p<0.0001) when compared to NaAc and to NH₄Ac, except for NH₄Ac and NaAc compared to each other (ns). Also, NH₄Cl showed (*p<0.05) and NH₄I showed (***p<0.001) when compared with LiCl and NaCl. All other comparisons are not significant.

For comparisons of salt responses between different species (N2 vs PS312):

- NH₄I and LiCl (*p<0.05); NaAc and NH₄Ac (****p<0.0001)

(4) It might be worth doing a power analysis on the data in Figure 3B. If the data are underpowered, this might explain why there is a difference in NH₄Br response with one of the null mutants but not the other.

For responses to NH₄Cl, since both che-1 mutants (rather than just one) showed significant difference compared to wildtype, we conducted a power analysis based on the effect size of that difference (~1.2; large). Given this effect size, the sample size for future experiments should be 12 (ANOVA).

For responses to NH₄Br and given the effect size of the difference seen between wildtype (PS312) and ot5012 (~0.8; large), the sample size for future experiments should be 18 (ANOVA) for a power value of 0.8. Therefore, it is possible that the sample size of 12 for the current experiment was too small to detect a possible difference between the ot5013 alleles and wildtype.

(5) It would be helpful to discuss why silencing Ppa-ASE might result in a switch from attractive to repulsive responses to some of the tested gustatory cues.

For similar assays using Ppa-odr-3p::HisCl1, increasing histamine concentration led to decreasing C.I. for a given odorant (myristate, a P. pacificus-specific attractant). It is likely that the amount of histamine treatment for knockdown to zero (i.e. without a valence change) will differ depending on the attractant.

(6) The statistical tests used in Figure 3 are not stated.

Figure 3 used Two-way ANOVA with Dunnett’s post hoc test. We have now added the test in the figure legend.

(7) It would be helpful to examine the responses of ASER to the full salt panel in the Ppa-gcy-22.3 vs. wild-type backgrounds.

We understand that future experiments examining neuron responses to the full salt panel for wildtype and gcy-22.3 mutants would provide further information about the salts and specific ions associated with the GCY-22.3 receptor. However, we have tested a broader range of salts (although not yet the full panel) for behavioral assays in wildtype vs gcy-22.3 mutants, which we have included as part of an added Figure 8.

(8) The controls shown in Figure S1 may not be adequate. Ideally, the same sample size would be used for the control, allowing differences between control worms and experimental worms to be quantified.

Although we had not conducted an equal number of negative controls using green light without salt stimuli due to resource constraints (6 control vs ~10-19 test), we provided individual recordings with stimuli to show that conditions we interpreted as having responses rarely showed responses resembling the negative controls. Similarly, those we interpreted as having no responses to stimuli mostly resembled the no-stimuli controls (e.g. WT to 25 mM NH₄Cl, gcy22.3 mutant to 250 mM NH₄Cl).

(9) An osmolarity control would be helpful for the calcium imaging experiments.

We acknowledge that future calcium imaging experiments featuring different salt concentrations could benefit from osmolarity controls.

(10) In Figure S7, more information about the microfluidic chip design is needed.

The chip design features a U-shaped worm trap to facilitate loading the worm head-first, with a tapered opening to ensure the worm fits snugly and will not slide too far forward during recording. The outer two chip channels hold buffer solution and can be switched open (ON) or closed (OFF) by the Valvebank. The inner two chip channels hold experimental solutions. The inner channel closer to the worm trap holds the control solution, and the inner channel farther from the worm trap holds the stimulant solution.

We have added an image of the chip in Figure S7 and further description in the legend.

(11) Throughout the manuscript, the discussion of the salt stimuli focuses on the salts more than the ions. More discussion of which ions are eliciting responses (both behavioral and neuronal responses) would be helpful.

In Figure 7, the gcy-22.3 defect resulted in a statistically significant reduction in response only towards NH₄Cl but not towards NaCl, which suggests ASER is the primary neuron detecting NH₄⁺ ions. To extend the description of the gcy-22.3 mutant defects to other ions, we have added a Figure 8: chemotaxis on various salt backgrounds. We found only a mild increase in attraction towards NH₄⁺ by both gcy-22.3 mutant alleles, but wild-type in their responses toward Cl^-, Na⁺, or I^-. The switch in the direction of change between the behavioral (enhanced) and calcium imaging result (reduced) suggests the behavioral response to ammonium ions likely involves additional receptors and neurons.

Minor comments:

(1) The full species name of "C. elegans" should be written out upon first use.

We have added ‘Caenorhabditis elegans’ to its first mention.

(2) In the legend of Figure 1, "N2" should not be in italics.

We have made the correction.

(3) The "che-1" gene should be in lowercase, even when it is at the start of the sentence.

We have made the correction.

(4) Throughout the manuscript, "HisCl" should be "HisCl1."

We have made these corrections to ‘HisCl1’.

(5) Figure 3A would benefit from more context, such as the format seen in Figure 7A. It would also help to have more information in the legend (e.g., blue boxes are exons, etc.).

(6) "Since NH₄I sensation is affected by silencing of che-1(+) neurons but is unaffected in che-1 mutants, ASE differentiation may be more greatly impacted by the silencing of ASE than by the loss of che-1": I don't think this is exactly what the authors mean. I would say, "ASE function may be more greatly impacted...".

We have changed ‘differentiation’ to ‘function’ in this passage.

(7) In Figure 7F-G, the AFD neurons are referred to as AFD in the figure title but AM12 in the graph. This is confusing.

Thank you for noticing this oversight. We have corrected “AM12” to “AFD”.

(8) In Figure 7, the legend suggests that comparisons within the same genotype were analyzed. I do not see these comparisons in the figure. In which cases were comparisons within the same genotype made?

Correct, we performed additional tests between ON and OFF states within the same genotypes (WT and mutant) but did not find significant differences. To avoid unnecessary confusion, we have removed this sentence.

(9) The nomenclature used for the transgenic animals is unconventional. For example, normally the calcium imaging line would be listed as csuEx93[Ppa-che-1p::optRCaMP] instead of Ppache-1p::optRCaMP(csuEx93).

We have made these corrections to the nomenclature.

(10) Figure S6 appears to come out of order. Also, it would be nice to have more of a legend for this figure. The format of the figure could also be improved for clarity.

We have corrected Figure S6 (now S8) and added more information to the legend.

(11) Methods section, Chemotaxis assays: "Most assays lasted ~3.5 hours at room temperature in line with the speed of P. pacificus without food..." It's not clear what this means. Does it take the worms 3.5 hours to crawl across the surface of the plate?

Correct, P. pacificus requires 3-4 hours to crawl across the surface of the plate, which is the standard time for chemotaxis assays for some odors and all salts. We have added this clarification to the Methods.

Author Response

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

eLife assessment

This study presents potentially valuable results on glutamine-rich motifs in relation to protein expression and alternative genetic codes. The author's interpretation of the results is so far only supported by incomplete evidence, due to a lack of acknowledgment of alternative explanations, missing controls and statistical analysis and writing unclear to non experts in the field. These shortcomings could be at least partially overcome by additional experiments, thorough rewriting, or both.

We thank both the Reviewing Editor and Senior Editor for handling this manuscript.

Based on your suggestions, we have provided controls, performed statistical analysis, and rewrote our manuscript. The revised manuscript is significantly improved and more accessible to non-experts in the field.

Reviewer #1 (Public Review):

Summary

This work contains 3 sections. The first section describes how protein domains with SQ motifs can increase the abundance of a lacZ reporter in yeast. The authors call this phenomenon autonomous protein expression-enhancing activity, and this finding is well supported. The authors show evidence that this increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance, and that this phenomenon is not affected by mutants in translational quality control. It was not completely clear whether the increased protein abundance is due to increased translation or to increased protein stability.

In section 2, the authors performed mutagenesis of three N-terminal domains to study how protein sequence changes protein stability and enzymatic activity of the fusions. These data are very interesting, but this section needs more interpretation. It is not clear if the effect is due to the number of S/T/Q/N amino acids or due to the number of phosphorylation sites.

In section 3, the authors undertake an extensive computational analysis of amino acid runs in 27 species. Many aspects of this section are fascinating to an expert reader. They identify regions with poly-X tracks. These data were not normalized correctly: I think that a null expectation for how often poly-X track occur should be built for each species based on the underlying prevalence of amino acids in that species. As a result, I believe that the claim is not well supported by the data.

Strengths

This work is about an interesting topic and contains stimulating bioinformatics analysis. The first two sections, where the authors investigate how S/T/Q/N abundance modulates protein expression level, is well supported by the data. The bioinformatics analysis of Q abundance in ciliate proteomes is fascinating. There are some ciliates that have repurposed stop codons to code for Q. The authors find that in these proteomes, Q-runs are greatly expanded. They offer interesting speculations on how this expansion might impact protein function.

Weakness

At this time, the manuscript is disorganized and difficult to read. An expert in the field, who will not be distracted by the disorganization, will find some very interesting results included. In particular, the order of the introduction does not match the rest of the paper.

In the first and second sections, where the authors investigate how S/T/Q/N abundance modulates protein expression levels, it is unclear if the effect is due to the number of phosphorylation sites or the number of S/T/Q/N residues.

There are three reasons why the number of phosphorylation sites in the Q-rich motifs is not relevant to their autonomous protein expression-enhancing (PEE) activities:

First, we have reported previously that phosphorylation-defective Rad51-NTD (Rad51-3SA) and wild-type Rad51-NTD exhibit similar autonomous PEE activity. Mec1/Tel1-dependent phosphorylation of Rad51-NTD antagonizes the proteasomal degradation pathway, increasing the half-life of Rad51 from ∼30 min to ≥180 min (1). (page 1, lines 11-14)

Second, in our preprint manuscript, we have already shown that phosphorylation-defective Rad53-SCD1 (Rad51-SCD1-5STA) also exhibits autonomous PEE activity similar to that of wild-type Rad53-SCD (Figure 2D, Figure 4A and Figure 4C). We have highlighted this point in our revised manuscript (page 9, lines 19-21).

Third, as revealed by the results of Figure 4, it is the percentages, and not the numbers, of S/T/Q/N residues that are correlated with the PEE activities of Q-rich motifs.

The authors also do not discuss if the N-end rule for protein stability applies to the lacZ reporter or the fusion proteins.

The autonomous PEE function of S/T/Q-rich NTDs is unlikely to be relevant to the N-end rule. The N-end rule links the in vivo half-life of a protein to the identity of its N-terminal residues. In S. cerevisiae, the N-end rule operates as part of the ubiquitin system and comprises two pathways. First, the Arg/N-end rule pathway, involving a single N-terminal amidohydrolase Nta1, mediates deamidation of N-terminal asparagine (N) and glutamine (Q) into aspartate (D) and glutamate (E), which in turn are arginylated by a single Ate1 R-transferase, generating the Arg/N degron. N-terminal R and other primary degrons are recognized by a single N-recognin Ubr1 in concert with ubiquitin-conjugating Ubc2/Rad6. Ubr1 can also recognize several other N-terminal residues, including lysine (K), histidine (H), phenylalanine (F), tryptophan (W), leucine (L) and isoleucine (I) (68-70). Second, the Ac/N-end rule pathway targets proteins containing N-terminally acetylated (Ac) residues. Prior to acetylation, the first amino acid methionine (M) is catalytically removed by Met-aminopeptidases (MetAPs), unless a residue at position 2 is non-permissive (too large) for MetAPs. If a retained N-terminal M or otherwise a valine (V), cysteine (C), alanine (A), serine (S) or threonine (T) residue is followed by residues that allow N-terminal acetylation, the proteins containing these AcN degrons are targeted for ubiquitylation and proteasome-mediated degradation by the Doa10 E3 ligase (71).

The PEE activities of these S/T/Q-rich domains are unlikely to arise from counteracting the N-end rule for two reasons. First, the first two amino acid residues of Rad51-NTD, Hop1-SCD, Rad53-SCD1, Sup35-PND, Rad51-ΔN, and LacZ-NVH are MS, ME, ME, MS, ME, and MI, respectively, where M is methionine, S is serine, E is glutamic acid and I is isoleucine. Second, Sml1-NTD behaves similarly to these N-terminal fusion tags, despite its methionine and glutamine (MQ) amino acid signature at the N-terminus. (Page 12, line 3 to page 13, line 2)

The most interesting part of the paper is an exploration of S/T/Q/N-rich regions and other repetitive AA runs in 27 proteomes, particularly ciliates. However, this analysis is missing a critical control that makes it nearly impossible to evaluate the importance of the findings. The authors find the abundance of different amino acid runs in various proteomes. They also report the background abundance of each amino acid. They do not use this background abundance to normalize the runs of amino acids to create a null expectation from each proteome. For example, it has been clear for some time (Ruff, 2017; Ruff et al., 2016) that Drosophila contains a very high background of Q's in the proteome and it is necessary to control for this background abundance when finding runs of Q's.

We apologize for not explaining sufficiently well the topic eliciting this reviewer’s concern in our preprint manuscript. In the second paragraph of page 14, we cite six references to highlight that SCDs are overrepresented in yeast and human proteins involved in several biological processes (5, 43) and that polyX prevalence differs among species (79-82).

We will cite a reference by Kiersten M. Ruff in our revised manuscript (38).

K. M. Ruff, J. B. Warner, A. Posey and P. S. Tan (2017) Polyglutamine length dependent structural properties and phase behavior of huntingtin exon1. Biophysical Journal 112, 511a.

The authors could easily address this problem with the data and analysis they have already collected. However, at this time, without this normalization, I am hesitant to trust the lists of proteins with long runs of amino acid and the ensuing GO enrichment analysis. Ruff KM. 2017. Washington University in St.

Ruff KM, Holehouse AS, Richardson MGO, Pappu RV. 2016. Proteomic and Biophysical Analysis of Polar Tracts. Biophys J 110:556a.

We thank Reviewer #1 for this helpful suggestion and now address this issue by means of a different approach described below.

Based on a previous study (43), we applied seven different thresholds to seek both short and long, as well as pure and impure, polyX strings in 20 different representative near-complete proteomes, including 4X (4/4), 5X (4/5-5/5), 6X (4/6-6/6), 7X (4/7-7/7), 8-10X (≥50%X), 11-10X (≥50%X) and ≥21X (≥50%X).

To normalize the runs of amino acids and create a null expectation from each proteome, we determined the ratios of the overall number of X residues for each of the seven polyX motifs relative to those in the entire proteome of each species, respectively. The results of four different polyX motifs are shown in our revised manuscript, i.e., polyQ (Figure 7), polyN (Figure 8), polyS (Figure 9) and polyT (Figure 10). Thus, polyX prevalence differs among species and the overall X contents of polyX motifs often but not always correlate with the X usage frequency in entire proteomes (43).

Most importantly, our results reveal that, compared to Stentor coeruleus or several non-ciliate eukaryotic organisms (e.g., Plasmodium falciparum, Caenorhabditis elegans, Danio rerio, Mus musculus and Homo sapiens), the five ciliates with reassigned TAAQ and TAGQ codons not only have higher Q usage frequencies, but also more polyQ motifs in their proteomes (Figure 7). In contrast, polyQ motifs prevail in Candida albicans, Candida tropicalis, Dictyostelium discoideum, Chlamydomonas reinhardtii, Drosophila melanogaster and Aedes aegypti, though the Q usage frequencies in their entire proteomes are not significantly higher than those of other eukaryotes (Figure 1). Due to their higher N usage frequencies, Dictyostelium discoideum, Plasmodium falciparum and Pseudocohnilembus persalinus have more polyN motifs than the other 23 eukaryotes we examined here (Figure 8). Generally speaking, all 26 eukaryotes we assessed have similar S usage frequencies and percentages of S contents in polyS motifs (Figure 9). Among these 26 eukaryotes, Dictyostelium discoideum possesses many more polyT motifs, though its T usage frequency is similar to that of the other 25 eukaryotes (Figure 10).

In conclusion, these new normalized results confirm that the reassignment of stop codons to Q indeed results in both higher Q usage frequencies and more polyQ motifs in ciliates.  

Reviewer #2 (Public Review):

Summary:

This study seeks to understand the connection between protein sequence and function in disordered regions enriched in polar amino acids (specifically Q, N, S and T). While the authors suggest that specific motifs facilitate protein-enhancing activities, their findings are correlative, and the evidence is incomplete. Similarly, the authors propose that the re-assignment of stop codons to glutamine-encoding codons underlies the greater user of glutamine in a subset of ciliates, but again, the conclusions here are, at best, correlative. The authors perform extensive bioinformatic analysis, with detailed (albeit somewhat ad hoc) discussion on a number of proteins. Overall, the results presented here are interesting, but are unable to exclude competing hypotheses.

Strengths:

Following up on previous work, the authors wish to uncover a mechanism associated with poly-Q and SCD motifs explaining proposed protein expression-enhancing activities. They note that these motifs often occur IDRs and hypothesize that structural plasticity could be capitalized upon as a mechanism of diversification in evolution. To investigate this further, they employ bioinformatics to investigate the sequence features of proteomes of 27 eukaryotes. They deepen their sequence space exploration uncovering sub-phylum-specific features associated with species in which a stop-codon substitution has occurred. The authors propose this stop-codon substitution underlies an expansion of ploy-Q repeats and increased glutamine distribution.

Weaknesses:

The preprint provides extensive, detailed, and entirely unnecessary background information throughout, hampering reading and making it difficult to understand the ideas being proposed.

The introduction provides a large amount of detailed background that appears entirely irrelevant for the paper. Many places detailed discussions on specific proteins that are likely of interest to the authors occur, yet without context, this does not enhance the paper for the reader.

The paper uses many unnecessary, new, or redefined acronyms which makes reading difficult. As examples:

1) Prion forming domains (PFDs). Do the authors mean prion-like domains (PLDs), an established term with an empirical definition from the PLAAC algorithm? If yes, they should say this. If not, they must define what a prion-forming domain is formally.

The N-terminal domain (1-123 amino acids) of S. cerevisiae Sup35 was already referred to as a “prion forming domain (PFD)” in 2006 (48). Since then, PFD has also been employed as an acronym in other yeast prion papers (Cox, B.S. et al. 2007; Toombs, T. et al. 2011).

B. S. Cox, L. Byrne, M. F., Tuite, Protein Stability. Prion 1, 170-178 (2007). J. A. Toombs, N. M. Liss, K. R. Cobble, Z. Ben-Musa, E. D. Ross, [PSI+] maintenance is dependent on the composition, not primary sequence, of the oligopeptide repeat domain. PLoS One 6, e21953 (2011).

2) SCD is already an acronym in the IDP field (meaning sequence charge decoration) - the authors should avoid this as their chosen acronym for Serine(S) / threonine (T)-glutamine (Q) cluster domains. Moreover, do we really need another acronym here (we do not).

SCD was first used in 2005 as an acronym for the Serine (S)/threonine (T)-glutamine (Q) cluster domain in the DNA damage checkpoint field (4). Almost a decade later, SCD became an acronym for “sequence charge decoration” (Sawle, L. et al. 2015; Firman, T. et al. 2018).

L. Sawle and K, Ghosh, A theoretical method to compute sequence dependent configurational properties in charged polymers and proteins. J. Chem Phys. 143, 085101(2015).

T. Firman and Ghosh, K. Sequence charge decoration dictates coil-globule transition in intrinsically disordered proteins. J. Chem Phys. 148, 123305 (2018).

3) Protein expression-enhancing (PEE) - just say expression-enhancing, there is no need for an acronym here.

Thank you. Since we have shown that the addition of Q-rich motifs to LacZ affects protein expression rather than transcription, we think it is better to use the “PEE” acronym.

The results suggest autonomous protein expression-enhancing activities of regions of multiple proteins containing Q-rich and SCD motifs. Their definition of expression-enhancing activities is vague and the evidence they provide to support the claim is weak. While their previous work may support their claim with more evidence, it should be explained in more detail. The assay they choose is a fusion reporter measuring beta-galactosidase activity and tracking expression levels. Given the presented data they have shown that they can drive the expression of their reporters and that beta gal remains active, in addition to the increase in expression of fusion reporter during the stress response. They have not detailed what their control and mock treatment is, which makes complete understanding of their experimental approach difficult. Furthermore, their nuclear localization signal on the tag could be influencing the degradation kinetics or sequestering the reporter, leading to its accumulation and the appearance of enhanced expression. Their evidence refuting ubiquitin-mediated degradation does not have a convincing control.

Although this reviewer’s concern regarding our use of a nuclear localization signal on the tag is understandable, we are confident that this signal does not bias our findings for two reasons. First, the negative control LacZ-NV also possesses the same nuclear localization signal (Figure 1A, lane 2). Second, another fusion target, Rad51-ΔN, does not harbor the NVH tag (Figure 1D, lanes 3-4). Compared to wild-type Rad51, Rad51-ΔN is highly labile. In our previous study, removal of the NTD from Rad51 reduced by ~97% the protein levels of corresponding Rad51-ΔN proteins relative to wild-type (1).

Based on the experimental results, the authors then go on to perform bioinformatic analysis of SCD proteins and polyX proteins. Unfortunately, there is no clear hypothesis for what is being tested; there is a vague sense of investigating polyX/SCD regions, but I did not find the connection between the first and section compelling (especially given polar-rich regions have been shown to engage in many different functions). As such, this bioinformatic analysis largely presents as many lists of percentages without any meaningful interpretation. The bioinformatics analysis lacks any kind of rigorous statistical tests, making it difficult to evaluate the conclusions drawn. The methods section is severely lacking. Specifically, many of the methods require the reader to read many other papers. While referencing prior work is of course, important, the authors should ensure the methods in this paper provide the details needed to allow a reader to evaluate the work being presented. As it stands, this is not the case.

Thank you. As described in detail below, we have now performed rigorous statistical testing using the GofuncR package (Figure 11, Figure 12 and DS7-DS32).

Overall, my major concern with this work is that the authors make two central claims in this paper (as per the Discussion). The authors claim that Q-rich motifs enhance protein expression. The implication here is that Q-rich motif IDRs are special, but this is not tested. As such, they cannot exclude the competing hypothesis ("N-terminal disordered regions enhance expression").

In fact, “N-terminal disordered regions enhance expression” exactly summarizes our hypothesis.

On pages 12-13 and Figure 4 of our preprint manuscript, we explained our hypothesis in the paragraph entitled “The relationship between PEE function, amino acid contents, and structural flexibility”.

The authors also do not explore the possibility that this effect is in part/entirely driven by mRNA-level effects (see Verma Na Comms 2019).

As pointed out by the first reviewer, we present evidence that the increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance (Figure 2), and that this phenomenon is not affected in translational quality control mutants (Figure 3).

As such, while these observations are interesting, they feel preliminary and, in my opinion, cannot be used to draw hard conclusions on how N-terminal IDR sequence features influence protein expression. This does not mean the authors are necessarily wrong, but from the data presented here, I do not believe strong conclusions can be drawn. That re-assignment of stop codons to Q increases proteome-wide Q usage. I was unable to understand what result led the authors to this conclusion.

My reading of the results is that a subset of ciliates has re-assigned UAA and UAG from the stop codon to Q. Those ciliates have more polyQ-containing proteins. However, they also have more polyN-containing proteins and proteins enriched in S/T-Q clusters. Surely if this were a stop-codon-dependent effect, we'd ONLY see an enhancement in Q-richness, not a corresponding enhancement in all polar-rich IDR frequencies? It seems the better working hypothesis is that free-floating climate proteomes are enriched in polar amino acids compared to sessile ciliates.

We thank this reviewer for raising this point, however her/his comments are not supported by the results in Figure 7.

Regardless, the absence of any kind of statistical analysis makes it hard to draw strong conclusions here.

We apologize for not explaining more clearly the results of Tables 5-7 in our preprint manuscript.

To address the concerns about our GO enrichment analysis by both reviewers, we have now performed rigorous statistical testing for SCD and polyQ protein overrepresentation using the GOfuncR package (https://bioconductor.org/packages/release/bioc/html/GOfuncR.html). GOfuncR is an R package program that conducts standard candidate vs. background enrichment analysis by means of the hypergeometric test. We then adjusted the raw p-values according to the Family-wise error rate (FWER). The same method had been applied to GO enrichment analysis of human genomes (89).

The results presented in Figure 11 and Figure 12 (DS7-DS32) support our hypothesis that Q-rich motifs prevail in proteins involved in specialized biological processes, including Saccharomyces cerevisiae RNA-mediated transposition, Candida albicans filamentous growth, peptidyl-glutamic acid modification in ciliates with reassigned stop codons (TAAQ and TAGQ), Tetrahymena thermophila xylan catabolism, Dictyostelium discoideum sexual reproduction, Plasmodium falciparum infection, as well as the nervous systems of Drosophila melanogaster, Mus musculus, and Homo sapiens (78). In contrast, peptidyl-glutamic acid modification and microtubule-based movement are not overrepresented with Q-rich proteins in Stentor coeruleus, a ciliate with standard stop codons.

Recommendations for the authors:

Please note that you control which revisions to undertake from the public reviews and recommendations for the authors.

Reviewer #1 (Recommendations For The Authors):

The order of paragraphs in the introduction was very difficult to follow. Each paragraph was clear and easy to understand, but the order of paragraphs did not make sense to this reader. The order of events in the abstract matches the order of events in the results section. However, the order of paragraphs in the introduction is completely different and this was very confusing. This disordered list of facts might make sense to an expert reader but makes it hard for a non-expert reader to understand.

Apologies. We endeavored to improve the flow of our revised manuscript to make it more readable.

The section beginning on pg 12 focused on figures 4 and 5 was very interesting and highly promising. However, it was initially hard for me to tell from the main text what the experiment was. Please add to the text an explanation of the experiment, because it is hard to figure out what was going on from the figures alone. Figure 4 is fantastic, but would be improved by adding error bars and scaling the x-axis to be the same in panels B,C,D.

Thank you for this recommendation. We have now scaled both the x-axis and y-axis equivalently in panels B, C and D of Figure 4. Error bars are too small to be included.

It is hard to tell if the key variable is the number of S/T/Q/N residues or the number of phosphosites. I think a good control would be to add a regression against the number of putative phosphosites. The sequences are well designed. I loved this part but as a reader, I need more interpretation about why it matters and how it explains the PEE.

As described above, we have shown that the number of phosphorylation sites in the Q-rich motifs is not relevant to their autonomous protein expression-enhancing (PEE) activities.

I believe that the prevalence of polyX runs is not meaningful without normalizing for the background abundance of each amino acid. The proteome-wide abundance and the assumption that amino acids occur independently can be used to form a baseline expectation for which runs are longer than expected by chance. I think Figures 6 and 7 should go into the supplement and be replaced in the main text with a figure where Figure 6 is normalized by Figure 7. For example in P. falciparum, there are many N-runs (Figure 6), but the proteome has the highest fraction of N’s (Figure 7).

Thank you for these suggestions. The three figures in our preprint manuscript (Figures 6-8) have been moved into the supplementary information (Figures S1-S3). For normalization, we have provided four new figures (Figures 7-10) in our revised manuscript.

The analysis of ciliate proteomes was fascinating. I am particularly interested in the GO enrichment for “peptidyl-glutamic acid modification” (pg 20) because these enzymes might be modifying some of Q’s in the Q-runs. I might be wrong about this idea or confused about the chemistry. Do these ciliates live in Q-rich environments? Or nitrogen rich environments?

Polymeric modifications (polymodifications) are a hallmark of C-terminal tubulin tails, whereas secondary peptide chains of glutamic acids (polyglutamylation) and glycines (polyglycylation) are catalyzed from the γ-carboxyl group of primary chain glutamic acids. It is not clear if these enzymes can modify some of the Q’s in the Q-runs.

To our knowledge, ciliates are abundant in almost every liquid water environment, i.e., oceans/seas, marine sediments, lakes, ponds, and rivers, and even soils.

I think you should include more discussion about how the codons that code for Q’s are prone to slippage during DNA replication, and thus many Q-runs are unstable and expand (e.g. Huntington’s Disease). The end of pg 24 or pg 25 would be good places.

We thank the reviewer for these comments.

PolyQ motifs have a particular length-dependent codon usage that relates to strand slippage in CAG/CTG trinucleotide repeat regions during DNA replication. In most organisms having standard genetic codons, Q is encoded by CAGQ and CAAQ. Here, we have determined and compared proteome-wide Q contents, as well as the CAGQ usage frequencies (i.e., the ratio between CAGQ and the sum of CAGQ, CAGQ, TAAQ, and TAGQ).

Our results reveal that the likelihood of forming long CAG/CTG trinucleotide repeats are higher in five eukaryotes due to their higher CAGQ usage frequencies, including Drosophila melanogaster (86.6% Q), Danio rerio (74.0% Q), Mus musculus (74.0% Q), Homo sapiens (73.5% Q), and Chlamydomonas reinhardtii (87.3% Q) (orange background, Table 2). In contrast, another five eukaryotes that possess high numbers of polyQ motifs (i.e., Dictyostelium discoideum, Candida albicans, Candida tropicalis, Plasmodium falciparum and Stentor coeruleus) (Figure 1) utilize more CAAQ (96.2%, 84.6%, 84.5%, 86.7% and 75.7%) than CAAQ (3.8%, 15.4%, 15.5%, 13.3% and 24.3%), respectively, to avoid the formation of long CAG/CTG trinucleotide repeats (green background, Table 2). Similarly, all five ciliates with reassigned stop codons (TAAQ and TAGQ) have low CAGQ usage frequencies (i.e., from 3.8% Q in Pseudocohnilembus persalinus to 12.6% Q in Oxytricha trifallax) (red font, Table 2). Accordingly, the CAG-slippage mechanism might operate more frequently in Chlamydomonas reinhardtii, Drosophila melanogaster, Danio rerio, Mus musculus and Homo sapiens than in Dictyostelium discoideum, Candida albicans, Candida tropicalis, Plasmodium falciparum, Stentor coeruleus and the five ciliates with reassigned stop codons (TAAQ and TAGQ).

Author response table 1.

Usage frequencies of TAA, TAG, TAAQ, TAGQ, CAAQ and CAGQ codons in the entire proteomes of 20 different organisms.

Pg 7, paragraph 2 has no direction. Please add the conclusion of the paragraph to the first sentence.

This paragraph has been moved to the “Introduction” section” of the revised manuscript.

Pg 8, I suggest only mentioning the PFDs used in the experiments. The rest are distracting.

We have addressed this concern above.

Pg 12. Please revise the "The relationship...." text to explain the experiment.

We apologize for not explaining this topic sufficiently well in our preprint manuscript.

SCDs are often structurally flexible sequences (4) or even IDRs. Using IUPred2A (https://iupred2a.elte.hu/plot_new), a web-server for identifying disordered protein regions (88), we found that Rad51-NTD (1-66 a.a.) (1), Rad53-SCD1 (1-29 a.a.) and Sup35-NPD (1-39 a.a.) are highly structurally flexible. Since a high content of serine (S), threonine (T), glutamine (Q), asparanine (N) is a common feature of IDRs (17-20), we applied alanine scanning mutagenesis approach to reduce the percentages of S, T, Q or N in Rad51-NTD, Rad53-SCD1 or Sup35-NPD, respectively. As shown in Figure 4 and Figure 5, there is a very strong positive relationship between STQ and STQN amino acid percentages and β-galactosidase activities. (Page 13, lines 5-10)

Pg 13, first full paragraph, "Futionally, IDRs..." I think this paragraph belongs in the Discussion.

This paragraph is now in the “Introduction” section (Page 5, Lines 11-15).

Pg. 15, I think the order of paragraphs should be swapped.

These paragraphs have been removed or rewritten in the “Introduction section” of our revised manuscript.

Pg 17 (and other parts) I found the lists of numbers and percentages hard to read and I think you should refer readers to the tables.

Thank you. In the revised manuscript, we have avoided using lists of numbers and percentages, unless we feel they are absolutely essential.

Pg. 19 please add more interpretation to the last paragraph. It is very cool but I need help understanding the result. Are these proteins diverging rapidly? Perhaps this is a place to include the idea of codon slippage during DNA replication.

Thank you. The new results in Table 2 indicate that the CAG-slippage mechanism is unlikely to operate in ciliates with reassigned stop codons (TAAQ and TAGQ).

Pg 24. "Based on our findings from this study, we suggest that Q-rich motifs are useful toolkits for generating novel diversity during protein evolution, including by enabling greater protein expression, protein-protein interactions, posttranslational modifications, increased solubility, and tunable stability, among other important traits." This idea needs to be cited. Keith Dunker has written extensively about this idea as have others. Perhaps also discuss why Poly Q rich regions are different from other IDRs and different from other IDRs that phase-separate.

Agreed, we have cited two of Keith Dunker’s papers in our revised manuscript (73, 74).

Minor notes:

Please define Borg genomes (pg 25).

Borgs are long extrachromosomal DNA sequences in methane-oxidizing Methanoperedens archaea, which display the potential to augment methane oxidation (101). They are now described in our revised manuscript. (Page 15, lines 12-14)

Reviewer #2 (Recommendations For The Authors):

The authors dance around disorder but never really quantify or show data. This seems like a strange blindspot.

We apologize for not explaining this topic sufficiently well in our preprint manuscript. We have endeavored to do so in our revised manuscript.

The authors claim the expression enhancement is "autonomous," but they have not ruled things out that would make it not autonomous.

Evidence of the “autonomous” nature of expression enhancement is presented in Figure 1, Figure 4, and Figure 5 of the preprint manuscript.

Recommendations for improving the writing and presentation.

The title does not recapitulate the entire body of work. The first 5 figures are not represented by the title in any way, and indeed, I have serious misgivings as to whether the conclusion stated in the title is supported by the work. I would strongly suggest the authors change the title.

Figure 2 could be supplemental.

Thank you. We think it is important to keep Figure 2 in the text.

Figures 4 and 5 are not discussed much or particularly well.

This reviewer’s opinion of Figure 4 and Figure 5 is in stark contrast to those of the first reviewer.

The introduction, while very thorough, takes away from the main findings of the paper. It is more suited to a review and not a tailored set of minimal information necessary to set up the question and findings of the paper. The question that the authors are after is also not very clear.

Thank you. The entire “Introduction” section has been extensively rewritten in the revised manuscript.

Schematics of their fusion constructs and changes to the sequence would be nice, even if supplemental.

Schematics of the fusion constructs are provided in Figure 1A.

The methods section should be substantially expanded.

The method section in the revised manuscript has been rewritten and expanded. The six Javascript programs used in this work are listed in Table S4.

The text is not always suited to the general audience and readership of eLife.

We have now rewritten parts of our manuscript to make it more accessible to the broad readership of eLife.

In some cases, section headers really don't match what is presented, or there is no evidence to back the claim.

The section headers in the revised manuscript have been corrected.

A lot of the listed results in the back half of the paper could be a supplemental table, listing %s in a paragraph (several of them in a row) is never nice

Acknowledged. In the revised manuscript, we have removed almost all sentences listing %s.

Minor corrections to the text and figures.

There is a reference to table 1 multiple times, and it seems that there is a missing table. The current table 1 does not seem to be the same table referred to in some places throughout the text.

Apologies for this mistake, which we have now corrected in our revised manuscript.

In some places its not clear where new work is and where previous work is mentioned. It would help if the authors clearly stated "In previous work...."

Acknowledged. We have corrected this oversight in our revised manuscript.

Not all strains are listed in the strain table (KO's in figure 3 are not included)

Apologies, we have now corrected Table S2, as suggested by this reviewer.

Author response table 2.

S. cerevisiae strains used in this study

Author Response

eLife assessment

This study presents potentially valuable results on glutamine-rich motifs in relation to protein expression and alternative genetic codes. The author's interpretation of the results is so far only supported by incomplete evidence, due to a lack of acknowledgment of alternative explanations, missing controls and statistical analysis and writing unclear to non experts in the field. These shortcomings could be at least partially overcome by additional experiments, thorough rewriting, or both.

We thank both the Reviewing Editor and Senior Editor for handling this manuscript and will submit our revised manuscript after the reviewed preprint is published by eLife.  

Reviewer #1 (Public Review):

Summary

This work contains 3 sections. The first section describes how protein domains with SQ motifs can increase the abundance of a lacZ reporter in yeast. The authors call this phenomenon autonomous protein expression-enhancing activity, and this finding is well supported. The authors show evidence that this increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance, and that this phenomenon is not affected by mutants in translational quality control. It was not completely clear whether the increased protein abundance is due to increased translation or to increased protein stability.

In section 2, the authors performed mutagenesis of three N-terminal domains to study how protein sequence changes protein stability and enzymatic activity of the fusions. These data are very interesting, but this section needs more interpretation. It is not clear if the effect is due to the number of S/T/Q/N amino acids or due to the number of phosphorylation sites.

In section 3, the authors undertake an extensive computational analysis of amino acid runs in 27 species. Many aspects of this section are fascinating to an expert reader. They identify regions with poly-X tracks. These data were not normalized correctly: I think that a null expectation for how often poly-X track occur should be built for each species based on the underlying prevalence of amino acids in that species. As a result, I believe that the claim is not well supported by the data.

Strengths

This work is about an interesting topic and contains stimulating bioinformatics analysis. The first two sections, where the authors investigate how S/T/Q/N abundance modulates protein expression level, is well supported by the data. The bioinformatics analysis of Q abundance in ciliate proteomes is fascinating. There are some ciliates that have repurposed stop codons to code for Q. The authors find that in these proteomes, Q-runs are greatly expanded. They offer interesting speculations on how this expansion might impact protein function.

Weakness

At this time, the manuscript is disorganized and difficult to read. An expert in the field, who will not be distracted by the disorganization, will find some very interesting results included. In particular, the order of the introduction does not match the rest of the paper.

In the first and second sections, where the authors investigate how S/T/Q/N abundance modulates protein expression levels, it is unclear if the effect is due to the number of phosphorylation sites or the number of S/T/Q/N residues.

There are three reasons why the number of phosphorylation sites in the Q-rich motifs is not relevant to their autonomous protein expression-enhancing (PEE) activities:

First, we have reported previously that phosphorylation-defective Rad51-NTD (Rad51-3SA) and wild-type Rad51-NTD exhibit similar autonomous PEE activity. Mec1/Tel1-dependent phosphorylation of Rad51-NTD antagonizes the proteasomal degradation pathway, increasing the half-life of Rad51 from ∼30 min to ≥180 min (Ref 27; Woo, T. T. et al. 2020).

1. T. T. Woo, C. N. Chuang, M. Higashide, A. Shinohara, T. F. Wang, Dual roles of yeast Rad51 N-terminal domain in repairing DNA double-strand breaks. Nucleic Acids Res 48, 8474-8489 (2020).

Second, in our preprint manuscript, we have also shown that phosphorylation-defective Rad53-SCD1 (Rad51-SCD1-5STA) also exhibits autonomous PEE activity similar to that of wild-type Rad53-SCD (Figure 2D, Figure 4A and Figure 4C).

Third, as revealed by the results of our preprint manuscript (Figure 4), it is the percentages, and not the numbers, of S/T/Q/N residues that are correlated with the PEE activities of Q-rich motifs.

The authors also do not discuss if the N-end rule for protein stability applies to the lacZ reporter or the fusion proteins.

The autonomous PEE function of S/T/Q-rich NTDs is unlikely to be relevant to the N-end rule. The N-end rule links the in vivo half-life of a protein to the identity of its N-terminal residues. In S. cerevisiae, the N-end rule operates as part of the ubiquitin system and comprises two pathways. First, the Arg/N-end rule pathway, involving a single N-terminal amidohydrolase Nta1, mediates deamidation of N-terminal asparagine (N) and glutamine (Q) into aspartate (D) and glutamate (E), which in turn are arginylated by a single Ate1 R-transferase, generating the Arg/N degron. N-terminal R and other primary degrons are recognized by a single N-recognin Ubr1 in concert with ubiquitin-conjugating Ubc2/Rad6. Ubr1 can also recognize several other N-terminal residues, including lysine (K), histidine (H), phenylalanine (F), tryptophan (W), leucine (L) and isoleucine (I) (Bachmair, A. et al. 1986; Tasaki, T. et al. 2012; Varshavshy, A. et al. 2019). Second, the Ac/N-end rule pathway targets proteins containing N-terminally acetylated (Ac) residues. Prior to acetylation, the first amino acid methionine (M) is catalytically removed by Met-aminopeptides, unless a residue at position 2 is non-permissive (too large) for MetAPs. If a retained N-terminal M or otherwise a valine (V), cysteine (C), alanine (A), serine (S) or threonine (T) residue is followed by residues that allow N-terminal acetylation, the proteins containing these AcN degrons are targeted for ubiquitylation and proteasome-mediated degradation by the Doa10 E3 ligase (Hwang, C. S., 2019).

A. Bachmair, D. Finley, A. Varshavsky, In vivo half-life of a protein is a function of its amino-terminal residue. Science 234, 179-186 (1986).

T. Tasaki, S. M. Sriram, K. S. Park, Y. T. Kwon, The N-end rule pathway. Annu Rev Biochem 81, 261-289 (2012).

A. Varshavsky, N-degron and C-degron pathways of protein degradation. Proc Natl Acad Sci 116, 358-366 (2019).

C. S. Hwang, A. Shemorry, D. Auerbach, A. Varshavsky, The N-end rule pathway is mediated by a complex of the RING-type Ubr1 and HECT-type Ufd4 ubiquitin ligases. Nat Cell Biol 12, 1177-1185 (2010).

The PEE activities of these S/T/Q-rich domains are unlikely to arise from counteracting the N-end rule for two reasons. First, the first two amino acid residues of Rad51-NTD, Hop1-SCD, Rad53-SCD1, Sup35-PND, Rad51-ΔN, and LacZ-NVH are MS, ME, ME, MS, ME, and MI, respectively, where M is methionine, S is serine, E is glutamic acid and I is isoleucine. Second, Sml1-NTD behaves similarly to these N-terminal fusion tags, despite its methionine and glutamine (MQ) amino acid signature at the N-terminus.

The most interesting part of the paper is an exploration of S/T/Q/N-rich regions and other repetitive AA runs in 27 proteomes, particularly ciliates. However, this analysis is missing a critical control that makes it nearly impossible to evaluate the importance of the findings. The authors find the abundance of different amino acid runs in various proteomes. They also report the background abundance of each amino acid. They do not use this background abundance to normalize the runs of amino acids to create a null expectation from each proteome. For example, it has been clear for some time (Ruff, 2017; Ruff et al., 2016) that Drosophila contains a very high background of Q's in the proteome and it is necessary to control for this background abundance when finding runs of Q's.

We apologize for not explaining sufficiently well the topic eliciting this reviewer’s concern in our preprint manuscript. In the second paragraph of page 14, we cite six references to highlight that SCDs are overrepresented in yeast and human proteins involved in several biological processes (32, 74), and that polyX prevalence differs among species (43, 75-77).

1. Cheung HC, San Lucas FA, Hicks S, Chang K, Bertuch AA, Ribes-Zamora A. An S/T-Q cluster domain census unveils new putative targets under Tel1/Mec1 control. BMC Genomics. 2012;13:664.

2. Mier P, Elena-Real C, Urbanek A, Bernado P, Andrade-Navarro MA. The importance of definitions in the study of polyQ regions: A tale of thresholds, impurities and sequence context. Comput Struct Biotechnol J. 2020;18:306-13.

3. Cara L, Baitemirova M, Follis J, Larios-Sanz M, Ribes-Zamora A. The ATM- and ATR-related SCD domain is over-represented in proteins involved in nervous system development. Sci Rep. 2016;6:19050.

4. Kuspa A, Loomis WF. The genome of Dictyostelium discoideum. Methods Mol Biol. 2006;346:15-30.

5. Davies HM, Nofal SD, McLaughlin EJ, Osborne AR. Repetitive sequences in malaria parasite proteins. FEMS Microbiol Rev. 2017;41(6):923-40.

6. Mier P, Alanis-Lobato G, Andrade-Navarro MA. Context characterization of amino acid homorepeats using evolution, position, and order. Proteins. 2017;85(4):709-19.

We will cite the two references by Kiersten M. Ruff in our revised manuscript.

K. M. Ruff and R. V. Pappu, (2015) Multiscale simulation provides mechanistic insights into the effects of sequence contexts of early-stage polyglutamine-mediated aggregation. Biophysical Journal 108, 495a.

K. M. Ruff, J. B. Warner, A. Posey and P. S. Tan (2017) Polyglutamine length dependent structural properties and phase behavior of huntingtin exon1. Biophysical Journal 112, 511a.

The authors could easily address this problem with the data and analysis they have already collected. However, at this time, without this normalization, I am hesitant to trust the lists of proteins with long runs of amino acid and the ensuing GO enrichment analysis.

Ruff KM. 2017. Washington University in St.

Ruff KM, Holehouse AS, Richardson MGO, Pappu RV. 2016. Proteomic and Biophysical Analysis of Polar Tracts. Biophys J 110:556a.

We thank Reviewer #1 for this helpful suggestion and now address this issue by means of a different approach described below.

Based on a previous study (43; Palo Mier et al. 2020), we applied seven different thresholds to seek both short and long, as well as pure and impure, polyX strings in 20 different representative near-complete proteomes, including 4X (4/4), 5X (4/5-5/5), 6X (4/6-6/6), 7X (4/7-7/7), 8-10X (≥50%X), 11-10X (≥50%X) and ≥21X (≥50%X).

To normalize the runs of amino acids and create a null expectation from each proteome, we determined the ratios of the overall number of X residues for each of the seven polyX motifs relative to those in the entire proteome of each species, respectively. The results of four different polyX motifs are shown below, i.e., polyQ (Author response image 1), polyN (Author response image 2), polyS (Author response image 3) and polyT (Author response image 4).

Author response image 1.

Q contents in 7 different types of polyQ motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.  

Author response image 2.

N contents in 7 different types of polyN motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author response image 3.

S contents in 7 different types of polyS motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.  

Author response image 4.

T contents in 7 different types of polyT motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

The results summarized in these four new figures support that polyX prevalence differs among species and that the overall X contents of polyX motifs often but not always correlate with the X usage frequency in entire proteomes (43; Palo Mier et al. 2020).

Most importantly, our results reveal that, compared to Stentor coeruleus or several non-ciliate eukaryotic organisms (e.g., Plasmodium falciparum, Caenorhabditis elegans, Danio rerio, Mus musculus and Homo sapiens), the five ciliates with reassigned TAAQ and TAGQ codons not only have higher Q usage frequencies, but also more polyQ motifs in their proteomes (Figure 1). In contrast, polyQ motifs prevail in Candida albicans, Candida tropicalis, Dictyostelium discoideum, Chlamydomonas reinhardtii, Drosophila melanogaster and Aedes aegypti, though the Q usage frequencies in their entire proteomes are not significantly higher than those of other eukaryotes (Figure 1). Due to their higher N usage frequencies, Dictyostelium discoideum, Plasmodium falciparum and Pseudocohnilembus persalinus have more polyN motifs than the other 23 eukaryotes we examined here (Figure 2). Generally speaking, all 26 eukaryotes we assessed have similar S usage frequencies and percentages of S contents in polyS motifs (Figure 3). Among these 26 eukaryotes, Dictyostelium discoideum possesses many more polyT motifs, though its T usage frequency is similar to that of the other 25 eukaryotes (Figure 4).

In conclusion, these new normalized results confirm that the reassignment of stop codons to Q indeed results in both higher Q usage frequencies and more polyQ motifs in ciliates.  

Reviewer #2 (Public Review):

Summary:

This study seeks to understand the connection between protein sequence and function in disordered regions enriched in polar amino acids (specifically Q, N, S and T). While the authors suggest that specific motifs facilitate protein-enhancing activities, their findings are correlative, and the evidence is incomplete. Similarly, the authors propose that the re-assignment of stop codons to glutamine-encoding codons underlies the greater user of glutamine in a subset of ciliates, but again, the conclusions here are, at best, correlative. The authors perform extensive bioinformatic analysis, with detailed (albeit somewhat ad hoc) discussion on a number of proteins. Overall, the results presented here are interesting, but are unable to exclude competing hypotheses.

Strengths:

Following up on previous work, the authors wish to uncover a mechanism associated with poly-Q and SCD motifs explaining proposed protein expression-enhancing activities. They note that these motifs often occur IDRs and hypothesize that structural plasticity could be capitalized upon as a mechanism of diversification in evolution. To investigate this further, they employ bioinformatics to investigate the sequence features of proteomes of 27 eukaryotes. They deepen their sequence space exploration uncovering sub-phylum-specific features associated with species in which a stop-codon substitution has occurred. The authors propose this stop-codon substitution underlies an expansion of ploy-Q repeats and increased glutamine distribution.

Weaknesses:

The preprint provides extensive, detailed, and entirely unnecessary background information throughout, hampering reading and making it difficult to understand the ideas being proposed. The introduction provides a large amount of detailed background that appears entirely irrelevant for the paper. Many places detailed discussions on specific proteins that are likely of interest to the authors occur, yet without context, this does not enhance the paper for the reader.

The paper uses many unnecessary, new, or redefined acronyms which makes reading difficult. As examples:

(1) Prion forming domains (PFDs). Do the authors mean prion-like domains (PLDs), an established term with an empirical definition from the PLAAC algorithm? If yes, they should say this. If not, they must define what a prion-forming domain is formally.

The N-terminal domain (1-123 amino acids) of S. cerevisiae Sup35 was already referred to as a “prion forming domain (PFD)” in 2006 (Tuite, M. F. 2006). Since then, PFD has also been employed as an acronym in other yeast prion papers (Cox, B.S. et al. 2007; Toombs, T. et al. 2011).

M. F., Tuite, Yeast prions and their prion forming domain. Cell 27, 397-407 (2005).

B. S. Cox, L. Byrne, M. F., Tuite, Protein Stability. Prion 1, 170-178 (2007).

J. A. Toombs, N. M. Liss, K. R. Cobble, Z. Ben-Musa, E. D. Ross, [PSI+] maintenance is dependent on the composition, not primary sequence, of the oligopeptide repeat domain. PLoS One 6, e21953 (2011).

(2) SCD is already an acronym in the IDP field (meaning sequence charge decoration) - the authors should avoid this as their chosen acronym for Serine(S) / threonine (T)-glutamine (Q) cluster domains. Moreover, do we really need another acronym here (we do not).

SCD was first used in 2005 as an acronym for the Serine (S)/threonine (T)-glutamine (Q) cluster domain in the DNA damage checkpoint field (Traven, A. and Heierhorst, J. 2005). Almost a decade later, SCD became an acronym for “sequence charge decoration” (Sawle, L. et al. 2015; Firman, T. et al. 2018).

A. Traven and J, Heierhorst, SQ/TQ cluster domains: concentrated ATM/ATR kinase phosphorylation site regions in DNA-damage-response proteins. Bioessays. 27, 397-407 (2005).

L. Sawle and K, Ghosh, A theoretical method to compute sequence dependent configurational properties in charged polymers and proteins. J. Chem Phys. 143, 085101(2015).

T. Firman and Ghosh, K. Sequence charge decoration dictates coil-globule transition in intrinsically disordered proteins. J. Chem Phys. 148, 123305 (2018).

(3) Protein expression-enhancing (PEE) - just say expression-enhancing, there is no need for an acronym here.

Thank you. Since we have shown that addition of Q-rich motifs to LacZ affects protein expression rather than transcription, we think it is better to use the “PEE” acronym.

The results suggest autonomous protein expression-enhancing activities of regions of multiple proteins containing Q-rich and SCD motifs. Their definition of expression-enhancing activities is vague and the evidence they provide to support the claim is weak. While their previous work may support their claim with more evidence, it should be explained in more detail. The assay they choose is a fusion reporter measuring beta-galactosidase activity and tracking expression levels. Given the presented data they have shown that they can drive the expression of their reporters and that beta gal remains active, in addition to the increase in expression of fusion reporter during the stress response. They have not detailed what their control and mock treatment is, which makes complete understanding of their experimental approach difficult. Furthermore, their nuclear localization signal on the tag could be influencing the degradation kinetics or sequestering the reporter, leading to its accumulation and the appearance of enhanced expression. Their evidence refuting ubiquitin-mediated degradation does not have a convincing control.

Based on the experimental results, the authors then go on to perform bioinformatic analysis of SCD proteins and polyX proteins. Unfortunately, there is no clear hypothesis for what is being tested; there is a vague sense of investigating polyX/SCD regions, but I did not find the connection between the first and section compelling (especially given polar-rich regions have been shown to engage in many different functions). As such, this bioinformatic analysis largely presents as many lists of percentages without any meaningful interpretation. The bioinformatics analysis lacks any kind of rigorous statistical tests, making it difficult to evaluate the conclusions drawn. The methods section is severely lacking. Specifically, many of the methods require the reader to read many other papers. While referencing prior work is of course, important, the authors should ensure the methods in this paper provide the details needed to allow a reader to evaluate the work being presented. As it stands, this is not the case.

Thank you. As described in detail below, we have now performed rigorous statistical testing using the GofuncR package.

Overall, my major concern with this work is that the authors make two central claims in this paper (as per the Discussion). The authors claim that Q-rich motifs enhance protein expression. The implication here is that Q-rich motif IDRs are special, but this is not tested. As such, they cannot exclude the competing hypothesis ("N-terminal disordered regions enhance expression").

In fact, “N-terminal disordered regions enhance expression” exactly summarizes our hypothesis.

On pages 12-13 and Figure 4 of our preprint manuscript, we explained our hypothesis in the paragraph entitled “The relationship between PEE function, amino acid contents, and structural flexibility”.

The authors also do not explore the possibility that this effect is in part/entirely driven by mRNA-level effects (see Verma Na Comms 2019).

As pointed out by the first reviewer, we show evidence that the increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance (Figure 2), and that this phenomenon is not affected by translational quality control mutants (Figure 3).

As such, while these observations are interesting, they feel preliminary and, in my opinion, cannot be used to draw hard conclusions on how N-terminal IDR sequence features influence protein expression. This does not mean the authors are necessarily wrong, but from the data presented here, I do not believe strong conclusions can be drawn. That re-assignment of stop codons to Q increases proteome-wide Q usage. I was unable to understand what result led the authors to this conclusion.

My reading of the results is that a subset of ciliates has re-assigned UAA and UAG from the stop codon to Q. Those ciliates have more polyQ-containing proteins. However, they also have more polyN-containing proteins and proteins enriched in S/T-Q clusters. Surely if this were a stop-codon-dependent effect, we'd ONLY see an enhancement in Q-richness, not a corresponding enhancement in all polar-rich IDR frequencies? It seems the better working hypothesis is that free-floating climate proteomes are enriched in polar amino acids compared to sessile ciliates.

Thank you. These comments are not supported by the results in Figure 1.

Regardless, the absence of any kind of statistical analysis makes it hard to draw strong conclusions here.

We apologize for not explaining more clearly the results of Tables 5-7 in our preprint manuscript.

To address the concerns about our GO enrichment analysis by both reviewers, we have now performed rigorous statistical testing for SCD and polyQ protein overrepresentation using the GOfuncR package (https://bioconductor.org/packages/release/bioc/html/GOfuncR.html). GOfuncR is an R package program that conducts standard candidate vs. background enrichment analysis by means of the hypergeometric test. We then adjusted the raw p-values according to the Family-wise error rate (FWER). The same method had been applied to GO enrichment analysis of human genomes (Huttenhower, C., et al. 2009).

Curtis Huttenhower, C., Haley, E. M., Hibbs, M., A., Dumeaux, V., Barrett, D. R., Hilary A. Coller, H. A., and Olga G. Troyanskaya, O., G. Exploring the human genome with functional maps, Genome Research 19, 1093-1106 (2009).

The results presented in Author response image 5 and Author response image 6 support our hypothesis that Q-rich motifs prevail in proteins involved in specialized biological processes, including Saccharomyces cerevisiae RNA-mediated transposition, Candida albicans filamentous growth, peptidyl-glutamic acid modification in ciliates with reassigned stop codons (TAAQ and TAGQ), Tetrahymena thermophila xylan catabolism, Dictyostelium discoideum sexual reproduction, Plasmodium falciparum infection, as well as the nervous systems of Drosophila melanogaster, Mus musculus, and Homo sapiens (74). In contrast, peptidyl-glutamic acid modification and microtubule-based movement are not overrepresented with Q-rich proteins in Stentor coeruleus, a ciliate with standard stop codons.

1. Cara L, Baitemirova M, Follis J, Larios-Sanz M, Ribes-Zamora A. The ATM- and ATR-related SCD domain is over-represented in proteins involved in nervous system development. Sci Rep. 2016;6:19050.

Author response image 5.

Selection of biological processes with overrepresented SCD-containing proteins in different eukaryotes. The percentages and number of SCD-containing proteins in our search that belong to each indicated Gene Ontology (GO) group are shown. GOfuncR (Huttenhower, C., et al. 2009) was applied for GO enrichment and statistical analysis. The p values adjusted according to the Family-wise error rate (FWER) are shown. The five ciliates with reassigned stop codons (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author response image 6.

Selection of biological processes with overrepresented polyQ-containing proteins in different eukaryotes. The percentages and numbers of polyQ-containing proteins in our search that belong to each indicated Gene Ontology (GO) group are shown. GOfuncR (Huttenhower, C., et al. 2009) was applied for GO enrichment and statistical analysis. The p values adjusted according to the Family-wise error rate (FWER) are shown. The five ciliates with reassigned stops codons (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors set out to explore the role of upstream open reading frames (uORFs) in stabilizing protein levels during Drosophila development and evolution. By utilizing a modified ICIER model for ribosome translation simulations and conducting experimental validations in Drosophila species, the study investigates how uORFs buffer translational variability of downstream coding sequences. The findings reveal that uORFs significantly reduce translational variability, which contributes to gene expression stability across different biological contexts and evolutionary timeframes.

We thank the reviewer for carefully reading our manuscript and providing thoughtful and constructive feedback. We believe the manuscript has been significantly improved by incorporating your suggestions. Please find our detailed responses and corresponding revisions below.

Strengths:

(1) The study introduces a sophisticated adaptation of the ICIER model, enabling detailed simulation of ribosomal traffic and its implications for translation efficiency.

(2) The integration of computational predictions with empirical data through knockout experiments and translatome analysis in Drosophila provides a compelling validation of the model's predictions.

(3) By demonstrating the evolutionary conservation of uORFs' buffering effects, the study provides insights that are likely applicable to a wide range of eukaryotes.

We appreciate your positive feedback and thoughtful summary of the strengths of our study.

Weaknesses:

(1) Although the study is technically sound, it does not clearly articulate the mechanisms through which uORFs buffer translational variability. A clearer hypothesis detailing the potential molecular interactions or regulatory pathways by which uORFs influence translational stability would enhance the comprehension and impact of the findings.

Thanks for your constructive comments. In the Discussion section of our previous submission (Original Lines 470-489), we proposed that uORFs function as “molecular dams” to smooth out fluctuations in ribosomal flow toward downstream CDS regions, primarily via mechanisms involving ribosome collision and dissociation. To further address your concern, we have expanded the Discussion and included a new model figure (Fig. 9) to more clearly articulate the potential biological and mechanistic basis by which translating 80S ribosomes may induce the dissociation of 40S ribosomes. The revised section (Lines 540–557) now reads:

“Ribosome slowdown or stalling on mRNA due to rare codons [56,96-98] or nascent blocking peptides [99-102] frequently triggers ribosome collisions genome-wide [103-105]. Such collisions, especially among elongating 80S ribosomes, often activate ribosome quality control (RQC) pathways that recognize collision interfaces on the 40S subunit, leading to ribosomal subunit dissociation and degradation [106-108]. In mammals, ZNF598 specifically identifies collided ribosomes to initiate ubiquitin-dependent protein and mRNA quality control pathways [109-113]. Analogously, yeast employs Hel2-mediated ubiquitination of uS10, initiating dissociation via the RQC-trigger complex (RQT) [114]. Furthermore, the human RQT (hRQT) complex recognizes ubiquitinated ribosomes and induces subunit dissociation similarly to yeast RQT [115]. However, transient ribosome collisions can evade RQC by promoting resumed elongation through mechanical force provided by trailing ribosomes, thereby mitigating stalling [116]. Beyond 80S collisions, evidence increasingly highlights a distinct collision type involving scanning 40S subunits or pre-initiation (43S) complexes. Recently, an initiation RQC pathway (iRQC) targeting the small ribosomal subunit (40S) has been described, particularly involving collisions between scanning 43S complexes or between stalled 43S and elongating 80S ribosomes (Figure 9B) [117,118]. During iRQC, E3 ubiquitin ligase RNF10 ubiquitinates uS3 and uS5 proteins, resulting in 40S degradation [118]. This mechanism aligns closely with our ICIER model, proposing collision-driven 43S dissociation in the 5' UTRs. Future studies exploring these mechanisms in greater detail will clarify how uORFs modulate translational regulation through buffering effects.”

(2) The study could be further improved by a discussion regarding the evolutionary selection of uORFs. Specifically, it would be beneficial to explore whether uORFs are favored evolutionarily primarily for their role in reducing translation efficiency or for their capability to stabilize translation variability. Such a discussion would provide deeper insights into the evolutionary dynamics and functional significance of uORFs in genetic regulation.

Thank you for this insightful suggestion. We agree that understanding whether uORFs are evolutionarily favored for their role in translational repression or for their capacity to buffer translational variability is a compelling and unresolved question. Our study suggests that translational buffering, rather than translational repression alone, can also drive evolutionary selection favoring uORFs, although it remains challenging to empirically disentangle these functions due to their inherent linkage. We have expanded the discussion in the revised manuscript to address this point in more detail (Lines 494-513), which is reproduced as follows:

“Previous studies have shown that a significant fraction of fixed uORFs in the populations of D. melanogaster and humans were driven by positive Darwinian selection 63,67, suggesting active maintenance through adaptive evolution rather than purely neutral or deleterious processes. While uORFs have traditionally been recognized for their capacity to attenuate translation of downstream CDSs, accumulating evidence now underscores their critical role in stabilizing gene expression under fluctuating cellular and environmental conditions [43,55,56]. Whether the favored evolutionary selection of uORFs acts primarily through their role in translational repression or translational buffering remains a compelling yet unresolved question, as these two functions are inherently linked. Indeed, highly conserved uORFs tend to be translated at higher levels, resulting not only in stronger inhibition of CDS translation [34,45,67] but also in a more pronounced buffering effect, as demonstrated in this study. This buffering capacity of uORFs potentially provides selective advantages by reducing fluctuations in protein synthesis, thus minimizing gene-expression noise and enhancing cellular homeostasis. This suggests that selection may favor uORFs that contribute to translational robustness, a hypothesis supported by findings in yeast and mammals showing that uORFs are significantly enriched in stressresponse genes and control the translation of certain master regulators of stress responses [41,42,94,95]. Our study suggests that translational buffering, rather than translational repression alone, can also drive evolutionary selection favoring uORFs, although it remains challenging to empirically disentangle these functions. Future comparative genomic analyses, coupled with experimental approaches such as ribosome profiling and functional mutagenesis, will be crucial in elucidating the precise evolutionary forces driving uORF conservation and adaptation.”

Reviewer #2 (Public review):

uORFs, short open reading frames located in the 5' UTR, are pervasive in genomes. However, their roles in maintaining protein abundance are not clear. In this study, the authors propose that uORFs act as "molecular dam", limiting the fluctuation of the translation of downstream coding sequences. First, they performed in silico simulations using an improved ICIER model, and demonstrated that uORF translation reduces CDS translational variability, with buffering capacity increasing in proportion to uORF efficiency, length, and number. Next, they analzed the translatome between two related Drosophila species, revealing that genes with uORFs exhibit smaller fluctuations in translation between the two species and across different developmental stages within the same specify. Moreover, they identified that bicoid, a critical gene for Drosophila development, contains a uORF with substantial changes in translation efficiency. Deleting this uORF in Drosophila melanogaster significantly affected its gene expression, hatching rates, and survival under stress condition. Lastly, by leveraging public Ribo-seq data, the authors showed that the buffering effect of uORFs is also evident between primates and within human populations. Collectively, the study advances our understanding of how uORFs regulate the translation of downstream coding sequences at the genome-wide scale, as well as during development and evolution.

The conclusions of this paper are mostly well supported by data, but some definitions and data analysis need to be clarified and extended.

We thank the reviewer for the thoughtful and constructive review. Your summary accurately captures the key findings of our study. We have carefully addressed all your concerns in the revised manuscript, and we believe it has been significantly improved based on your valuable input.

(1) There are two definitions of translation efficiency (TE) in the manuscript: one refers to the number of 80S ribosomes that complete translation at the stop codon of a CDS within a given time interval, while the other is calculated based on Ribo-seq and mRNA-seq data (as described on Page 7, line 209). To avoid potential misunderstandings, please use distinct terms to differentiate these two definitions.

Thank you for highlighting this important point, and we apologize for the confusion. The two definitions of translation efficiency (TE) in our manuscript arise from methodological differences between simulation and experimental analyses. To clarify, in the revised manuscript, we use “translation rate” in the context of simulations to describe the number of 80S ribosomes completing translation at the CDS stop codon per unit time. We retain the conventional “translation efficiency (TE)” for Ribo-seq–based measurements. 

In this revised manuscript, we have added a more detailed explanation of TE in the revised manuscript (Lines 202–206), which now reads:

“For each sample, we followed established procedures [62-66] to calculate the translational efficiency (TE) for each feature (CDS or uORF). TE serves as a proxy for the translation rate at which ribosomes translate mRNA into proteins, typically quantified by comparing the density of ribosome-protected mRNA fragment (RPF) to the mRNA abundance for that feature (see Materials and Methods).”

(2) Page 7, line 209: "The translational efficiencies (TEs) of the conserved uORFs were highly correlated between the two species across all developmental stages and tissues examined, with Spearman correlation coefficients ranging from 0.478 to 0.573 (Fig. 2A)." However, the authors did not analyze the correlation of translation efficiency of conserved CDSs between the two species, and compare this correlation to the correlation between the TEs of CDSs. These analyzes will further support the authors conclusion regarding the role of conserved uORFs in translation regulation.

In the revised manuscript, we have incorporated a comparison of translational efficiency (TE) correlations for conserved CDSs between the two species. We found that CDSs exhibit significantly higher interspecific TE correlations than uORFs, with Spearman’s rho ranging from 0.588 to 0.806. This suggests that uORFs tend to show greater variability in TE than CDSs, consistent with our model in which uORFs buffer fluctuations in downstream CDS translation. The updated results were included in the revised manuscript (Lines 223-227) as follows:

“In contrast, TE of CDSs exhibited a significantly higher correlation between the two species in the corresponding samples compared to that of uORFs, with Spearman’s rho ranging from 0.588 to 0.806 (P = 0.002, Wilcoxon signed-rank test; Figure 2A). This observation is consistent with our simulation results, which indicate that uORFs experience greater translational fluctuations than their downstream CDSs.”

(3) Page 8, line 217: "Among genes with multiple uORFs, one uORF generally emerged as dominant, displaying a higher TE than the others within the same gene (Fig. 2C)." The basis for determining dominance among uORFs is not explained and this lack of clarification undermines the interpretation of these findings.

Thank you for pointing this out. We apologize for the confusion. In our study, a “dominant” uORF is defined as the one with the highest translation efficiency (TE) among all uORFs within the same gene. This designation is based solely on TE, which we consider a key metric for uORF activity, as it directly reflects translational output and potential regulatory impact. We have revised the manuscript to clarify this definition (Lines 232–244), now stating:

“Among genes with multiple uORFs, we defined the uORF with the highest TE as the dominant uORF for that gene, as TE is one of the most relevant metrics for assessing uORF function 45,67…… These results suggest that genes with multiple uORFs tend to retain the same dominant uORF across developmental stages, indicating that the dominant uORFs may serve as the key translational regulator of the downstream CDS.”

(4) According to the simulation, the translation of uORFs should exhibit greater variability than that of CDSs. However, the authors observed significantly fewer uORFs with significant TE changes compared to CDSs. This discrepancy may be due to lower sequencing depth resulting in fewer reads mapped to uORFs. Therefore, the authors may compare this variability specifically among highly expressed genes.

Thank you for this thoughtful observation. We agree that the lower proportion of uORFs showing significant TE changes compared to CDSs, as reported in Table 1, appears inconsistent with our conclusion that uORFs exhibit greater translational variability. However, this discrepancy is largely attributable to differences in sequencing depth and feature length—uORFs are generally much shorter and more weakly expressed than CDSs, resulting in fewer mapped reads and reduced statistical power (Figure S18A).

To address this issue, we first followed your suggestion and restricted our analysis to genes with both mRNA and RPF RPKM values above the 50th percentile in D. melanogaster and D. simulans. While this filtering increased the total proportion of features with significant TE changes (due to improved read coverage), the proportion of significant uORFs still remained lower than that of CDSs (Table R1). This suggests that even among highly expressed genes, the disparity in read counts between uORFs and CDSs persists (Figure S18B), and thus the issue is not fully resolved.

To better capture biological relevance, we compared the absolute values of log2(TE changes) between D. melanogaster and D. simulans for uORFs and their corresponding CDSs. Across all samples, uORFs consistently exhibit larger TE shifts than their downstream CDSs, supporting our model that uORFs act as translational buffers (Figure 3B).

We have made relevant changes to report the new analysis in this revised manuscript. Specifically, in our original submission, we stated this observation with the sentence “The smaller number of uORFs showing significant TE changes compared to CDSs between D. melanogaster and D. simulans likely reflects their shorter length and reduced statistical power, rather than indicating that uORFs are less variable in translation than CDSs.” To make this point clearer, in the revised version (Lines 275-284), we rephrased this sentence which read as follows: 

“Note that due to their shorter length and generally lower TE, uORFs had considerably lower read counts than CDSs, limiting the statistical power to detect significant interspecific TE differences for uORFs. This trend consistently holds whether analyzing all expressed uORFs (Figure S18A) or only highly expressed genes (Figure S18B). Thus, the fewer uORFs showing significant TE divergence likely reflects lower read counts and statistical sensitivity rather than reduced translational variability relative to CDSs. In fact, the absolute values of log2(fold change) of TE for uORFs between D. melanogaster and D. simulans were significantly greater than those observed for corresponding CDSs across all samples (P < 0.001, Wilcoxon signed-rank test; Figure 3B), suggesting that the magnitude of

TE changes in CDSs is generally smaller than that in uORFs, due to the buffering effect of uORF.”

Author response table 1.

Proportion of uORFs and CDSs with significant TE changes before and after selecting HEGs

(5) If possible, the author may need to use antibodies against bicoid to test the effect of ATG deletion on bicoid expression, particularly under different developmental stages or growth conditions.

According to the authors' conclusions, the deletion mutant should exhibit greater variability in bicoid protein abundance. This experiment could provide strong support for the proposed mechanisms.

Thank you for this excellent suggestion. We fully agree that testing Bcd protein levels across developmental stages or stress conditions using antibodies would be a strong validation of our model, which predicts greater variability in Bcd protein abundance upon uORF deletion.

In fact, we attempted such experiments in both wild-type and mutant backgrounds. However, we encountered substantial difficulties in obtaining a reliable anti-Bcd antibody. Some Bcd antibodies referenced in the published literature were homemade and often shared among research groups as gifts [1-3] and some commercially available antibodies cited in previous studies are no longer supplied by vendors [4-6]. We managed to obtain a custom-made antibody from Professor Feng Liu, but unfortunately, it produced inconsistent and unsatisfactory results. Despite considerable effort—including during the COVID-19 pandemic—we were unable to identify a reagent suitable for robust and reproducible detection of Bcd protein.

As an alternative, we used sucrose gradient fractionation followed by qPCR to directly measure the translation efficiency of bicoid in vivo. We believe this approach offers a clear and quantitative readout of translational activity, and it avoids potential confounding from protein degradation, which may vary across conditions and developmental stages. Nonetheless, we recognize the value of antibody-based validation and will pursue this direction in future work if reliable antibodies become available. We have added this limitation to the revised Discussion section (Lines 563–568) as follows:

“We demonstrated that the bcd uORF represses CDS translation using sucrose gradient fractionation followed by qPCR—an approach that directly measures translation efficiency while minimizing confounding from RNA/protein degradation. However, detecting Bcd protein levels with antibodies across developmental stages or conditions in the mutants and wild-type controls would provide an even stronger validation of our model and should be explored in future studies.”

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors):

(1) The authors should provide a more detailed explanation for the modifications made to the ICIER model. Specifically, an explanation of the biological or mechanistic rationale behind the ability of the 80S ribosome to cause upstream 40S ribosomes to dissociate from mRNA would help clarify this aspect of the model.

Thank you for this suggestion. In the original submission, we described our modifications to the ICIER model in the section titled “An extended ICIER model for quantifying uORF buffering in CDS translation” (Lines 88-124 of the revised manuscript). 

To further clarify the biological rationale behind this mechanism, we have now included a conceptual model figure (Figure 9) illustrating mechanistically how uORF translation can buffer downstream translation within a single mRNA molecule. Additionally, we expanded the Discussion to summarize the current understanding of how collisions between translating 80S ribosomes and scanning 40S subunits may lead to dissociation, referencing known initial ribosome quality control (iRQC) pathways. These revisions provide a clearer mechanistic framework for interpreting the buffering effects modeled in our simulations. The relevant part is reproduced from Discussion (Lines 540-557) which reads as follows:

“Ribosome slowdown or stalling on mRNA due to rare codons [56,96-98] or nascent blocking peptides [99-102] frequently triggers ribosome collisions genome-wide [103-105]. Such collisions, especially among elongating 80S ribosomes, often activate ribosome quality control (RQC) pathways that recognize collision interfaces on the 40S subunit, leading to ribosomal subunit dissociation and degradation [106-108]. In mammals, ZNF598 specifically identifies collided ribosomes to initiate ubiquitin-dependent protein and mRNA quality control pathways [109-113]. Analogously, yeast employs Hel2-mediated ubiquitination of uS10, initiating dissociation via the RQC-trigger complex (RQT) [114]. Furthermore, the human RQT (hRQT) complex recognizes ubiquitinated ribosomes and induces subunit dissociation similarly to yeast RQT [115]. However, transient ribosome collisions can evade RQC by promoting resumed elongation through mechanical force provided by trailing ribosomes, thereby mitigating stalling [116]. Beyond 80S collisions, evidence increasingly highlights a distinct collision type involving scanning 40S subunits or pre-initiation (43S) complexes. Recently, an initiation RQC pathway (iRQC) targeting the small ribosomal subunit (40S) has been described, particularly involving collisions between scanning 43S complexes or between stalled 43S and elongating 80S ribosomes (Figure 9B) [117,118]. During iRQC, E3 ubiquitin ligase RNF10 ubiquitinates uS3 and uS5 proteins, resulting in 40S degradation [118]. This mechanism aligns closely with our ICIER model, proposing collision-driven 43S dissociation in the 5' UTRs. Future studies exploring these mechanisms in greater detail will clarify how uORFs modulate translational regulation through buffering effects.”

(2) The figure legend references Figure 5C; however, this figure appears to be missing from the document.

We apologize for the oversight. The missing panel previously referred to as Figure 5C has now been incorporated into the revised Figure 6A. The figure and its corresponding legend have been corrected accordingly in the updated manuscript.

Reviewer #2 (Recommendations for the authors):

This is an important study that enhances our understanding of the roles of uORFs in translational regulation. In addition to the suggestions provided in the public review, the following minor points should be addressed before publication in eLife:

(1) Page 7, line 207: "We identified 18,412 canonical uORFs shared between the two species (referred to as conserved uORFs hereafter)." The term "canonical uORFs" requires clarification. Does this refer to uORFs with specific sequence features, conservation, or another defining characteristic?

Thank you for pointing this out. We apologize for the lack of clarity. In our study, a canonical uORF is defined as an open reading frame (ORF) that initiates with a canonical AUG start codon located in the 5′ untranslated region (UTR) and terminates with a stop codon (UAA, UAG, or UGA) within the same mRNA. Conservation of uORFs is defined solely based on the presence of AUG start codons at orthologous positions in the 5′ UTR across species, regardless of differences in the stop codon.

To clarify this definition, we have revised the sentence as follows (Lines 213-219): “We focused on canonical uORFs that initiate with an ATG start codon in the 5′ UTR and terminate with a stop codon (TAA, TAG, or TGA). Because the ATG start codon is the defining feature of a canonical uORF and tends to be more conserved than its downstream sequence [67], we defined uORF conservation based on the presence of the ATG start codon in the 5′ UTR of D. melanogaster and its orthologous positions in D. simulans, regardless of differences in the stop codon. Using this criterion, we identified 18,412 canonical uORFs with conserved start codons between the two species.”

(2) Page 8, line 227: "Furthermore, the dominant uORFs showed a higher proportion of conserved uATGs than the other translated uORFs." There appears to be a typographical error. Should "other uATGs" instead read "other uORFs"?

Thank you for pointing this out. As we addressed in response to your previous concern, in this study, we defined uORF conservation primarily based on the presence of their start codon (uATG) both in D. melanogaster and the orthologous sites of D. simulans, as the start codon is the defining feature of a uORF and tends to be more conserved than the remaining sequence, as demonstrated in our previous study [7]. We used the term “conserved uATGs” to reflect this definition and believe it accurately conveys the intended meaning in this context.

(3) Page 8, line 240: "uORFs exhibited a significant positive correlation with the TE of their downstream CDSs in all samples analyzed (P < 0.001, Spearman's correlation)." A Spearman's rho of 0.11 or 0.21 may not practically represent a "significant" positive correlation. Consider rephrasing this as "a positive correlation."

Thank you for the suggestion. We have revised the sentence in the manuscript to read (Lines 257-259): “uORFs exhibited a modest, yet statistically significant, positive correlation with the TE of their downstream CDSs across all samples analyzed (P < 0.001, Spearman’s correlation).”

(4) Page 9, line 269: The analysis of interspecific TE changes between uORFs and their corresponding CDSs is a crucial piece of evidence supporting the authors' conclusions. Presenting this analysis as part of the figures, rather than in "Table 1," would improve clarity and accessibility.

Thank you for this suggestion. In Table 1, we originally presented the number of uORFs and CDSs that showed significant differences in TE between D. melanogaster and D. simulans during various developmental stages. One key point we aimed to emphasize was that, although TE changes in uORFs and their downstream CDSs are positively correlated, there is a notable difference in the magnitude of these changes. To better convey this, we have summarized the core findings of Table 1 in graphical form.

In Figure 3B of the revised version, we compared the absolute values of interspecific TE changes between CDS and uORF, showing that CDSs consistently exhibit smaller shifts than their upstream uORFs. This result further supports the translational buffering effect of uORFs on downstream CDS expression. We have included the updated results in the revised manuscript (Lines 281-284) as follows:

“In fact, the absolute values of log2(fold change) of TE for uORFs between D. melanogaster and D. simulans was significantly greater than that observed for corresponding CDSs across all samples (P < 0.001, Wilcoxon signed-rank test; Figure 3B), suggesting that the magnitude of TE changes in CDSs is generally smaller than that in uORFs, due to the buffering effect of uORF.”

(5) Page 9, line 279: The phrase "dominantly translated" needs clarification. Does it refer to Figure 2C, where one uORF is dominantly translated within a gene, or does it mean that the uORF's translation is higher than that of its corresponding CDS?

We apologize for the obscurity. The phrase "dominantly translated" means one uORF with the highest TE compared to other uORFs within a gene. We have rephrased the relevant sentence in the revised version (Lines 299-304), which now reads:

“To investigate how the conservation level and translation patterns of uORFs influence their buffering capacity on CDS translation, we categorized genes expressed in each pair of samples into three classes:

Class I, genes with conserved uORFs that are dominantly translated (i.e., exhibiting the highest TE among all uORFs within the same gene) in both Drosophila species; Class II, genes with conserved uORFs that are translated in both species but not dominantly translated in at least one; and Class III, the remaining expressed genes.”

(6) The sequencing data and analysis code should be made publicly available before publication to ensure transparency and reproducibility.

Thank you for this suggestion. As described in the Data availability section, all deepsequencing data generated in this study, including single-ended mRNA-Seq and Ribo-Seq data of 10 developmental stages and tissues of Drosophila simulans and paired-end mRNA-Seq data of 0-2 h, 26 h, 6-12 h, and 12-24 h Drosophila melanogaster embryos, were deposited in the China National Genomics Data Center Genome Sequence Archive (GSA) under accession numbers CRA003198, CRA007425, and CRA007426. The mRNA-Seq and Ribo-Seq data for the different developmental stages and tissues of Drosophila melanogaster were published in our previous paper [8] and were deposited in the Sequence Read Archive (SRA) under accession number SRP067542.

All original code has been deposited on GitHub: https://github.com/lujlab/uORF_buffer; https://github.com/lujlab/Buffer_eLife2025.

Response reference

(1) Li, X.Y., MacArthur, S., Bourgon, R., Nix, D., Pollard, D.A., Iyer, V.N., Hechmer, A., Simirenko, L., Stapleton, M., Luengo Hendriks, C.L., et al. (2008). Transcription factors bind thousands of active and inactive regions in the Drosophila blastoderm. PLoS Biol 6, e27. 10.1371/journal.pbio.0060027.

(2) Horner, V.L., Czank, A., Jang, J.K., Singh, N., Williams, B.C., Puro, J., Kubli, E., Hanes, S.D., McKim, K.S., Wolfner, M.F., and Goldberg, M.L. (2006). The Drosophila calcipressin sarah is required for several aspects of egg activation. Curr Biol 16, 1441-1446. 10.1016/j.cub.2006.06.024.

(3) Lee, K.M., Linskens, A.M., and Doe, C.Q. (2022). Hunchback activates Bicoid in Pair1 neurons to regulate synapse number and locomotor circuit function. Curr Biol 32, 2430-2441 e2433. 10.1016/j.cub.2022.04.025.

(4) Wharton, T.H., Nomie, K.J., and Wharton, R.P. (2018). No significant regulation of bicoid mRNA by Pumilio or Nanos in the early Drosophila embryo. PLoS One 13, e0194865. 10.1371/journal.pone.0194865.

(5) Wang, J., Zhang, S., Lu, H., and Xu, H. (2022). Differential regulation of alternative promoters emerges from unified kinetics of enhancer-promoter interaction. Nat Commun 13, 2714. 10.1038/s41467-022-30315-6.

(6) Xu, H., Sepulveda, L.A., Figard, L., Sokac, A.M., and Golding, I. (2015). Combining protein and mRNA quantification to decipher transcriptional regulation. Nat Methods 12, 739-742. 10.1038/nmeth.3446.

(7) Zhang, H., Wang, Y., Wu, X., Tang, X., Wu, C., and Lu, J. (2021). Determinants of genomewide distribution and evolution of uORFs in eukaryotes. Nat Commun 12, 1076. 10.1038/s41467-021-21394-y.

(8) Zhang, H., Dou, S., He, F., Luo, J., Wei, L., and Lu, J. (2018). Genome-wide maps of ribosomal occupancy provide insights into adaptive evolution and regulatory roles of uORFs during Drosophila development. PLoS Biol 16, e2003903. 10.1371/journal.pbio.2003903.

Author response:

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

Reviewer #1 (Public Review):

In this study, the authors examined the role of IBTK, a substrate-binding adaptor of the CRL3 ubiquitin ligase complex, in modulating the activity of the eiF4F translation initiation complex. They find that IBTK mediates the non-degradative ubiquitination of eiF4A1, promotes cap-dependent translational initiation, nascent protein synthesis, oncogene expression, and tumor cell growth. Correspondingly, phosphorylation of IBTK by mTORC1/ S6K1 increases eIF4A1 ubiquitination and sustains oncogenic translation.

Strengths:

This study utilizes multiple biochemical, proteomic, functional, and cell biology assays to substantiate their results. Importantly, the work nominates IBTK as a unique substrate of mTORC1, and further validates eiF4A1 (a crucial subunit of the ei44F complex) as a promising therapeutic target in cancer. Since IBTK interacts broadly with multiple members of the translational initial complex - it will be interesting to examine its role in eiF2alpha-mediated ER stress as well as eiF3-mediated translation. Additionally, since IBTK exerts pro-survival effects in multiple cell types, it will be of relevance to characterize the role of IBTK in mediating increased mTORC1 mediated translation in other tumor types, thus potentially impacting their treatment with eiF4F inhibitors.

Limitations/Weaknesses:

The findings are mostly well supported by data, but some areas need clarification and could potentially be enhanced with further experiments:

(1) Since eiF4A1 appears to function downstream of IBTK1, can the effects of IBTK1 KO/KD in reducing puromycin incorporation (in Fig 3A), cap-dependent luciferase reporter activity (Fig 3G), reduced oncogene expression (Fig 4A) or 2D growth/ invasion assays (Fig 4) be overcome or bypassed by overexpressing eiF4A1? These could potentially be tested in future studies.

We appreciate the reviewer for bringing up this crucial point. As per the reviewer's suggestion, we conducted experiments where we overexpressed Myc-eIF4A1 in IBTK-KO SiHa cells. Our findings indicate that increasing levels of eIF4A1 through ectopic overexpression is unable to reverse the decrease in puromycin incorporation (Fig. S3C) and protein expression of eIF4A1 targets caused by IBTK ablation (Fig. S4E). These results clearly demonstrate that IBTK ablation-induced eIF4A1 dysfunctions cannot be rescued by simply elevating eIF4A1 protein levels. Given the above results are negative, the impacts of eIF4A1 overexpression on the 2D growth/invasion capacities of IBTK-KO cells were not further examined. We sincerely appreciate the reviewer's understanding regarding this matter.

(2) The decrease in nascent protein synthesis in puromycin incorporation assays in Figure 3A suggest that the effects of IBTK KO are comparable to and additive with silvesterol. It would be of interest to examine whether silvesterol decreases nascent protein synthesis or increases stress granules in the IBTK KO cells stably expressing IBTK as well.

We appreciate the reviewer for bringing up this crucial point. We have showed that silvestrol treatment still decreased nascent protein synthesis in IBTK-KO cells overexpressing FLAG-IBTK as well (Fig. S3B).

(3) The data presented in Figure 5 regarding the role of mTORC1 in IBTK- mediated eiF4A1 ubiquitination needs further clarification on several points:

• It is not clear if the experiments in Figure 5F with Phos-tag gels are using the FLAG-IBTK deletion mutant or the peptide containing the mTOR sites as it is mentioned on line 517, page 19 "To do so, we generated an IBTK deletion mutant (900-1150 aa) spanning the potential mTORC1-regulated phosphorylation sites" This needs further clarification.

We appreciate the reviewer for bringing up this crucial point. The IBTK deletion mutant used in Fig. 5F is FLAG-IBTK900-1150aa. We have annotated it with smaller font size in the panel (red box) in Author response image 1.

Author response image 1.

• It may be of benefit to repeat the Phos tag experiments with full-length FLAG- IBTK and/or endogenous IBTK with molecular weight markers indicating the size of migrated bands.

We appreciate the reviewer for bringing up this crucial point. We attempted to perform Phos-tag assays to detect the overexpressed full-length FLAG-IBTK or endogenous IBTK. However, we encountered difficulties in successfully transferring the full-length FLAG-IBTK or endogenous IBTK onto the nitrocellulose membrane during Phos-tag WB analysis. This is likely due to the limitations of this technique. Based on our experience, phos-tag gel is less efficient in detecting protein motility shifts with large molecular weights. As the molecular weight of IBTK protein is approximately 160 kDa, it falls within this category. Considering these technical constraints, we did not include Phos-tag assay results for full-length IBTK in our study. We sincerely appreciate the reviewer's understanding regarding this matter.

The binding of Phos-tag to phosphorylated proteins induces a mobility shift during gel electrophoresis or protein separation techniques. This shift allows for the visualization and quantification of phosphorylated proteins separately from non-phosphorylated proteins. It's important to note that these mobility shifts indicate phosphorylation status, rather than actual molecular weights. pre- stained protein markers are typically used as a reference to assess the efficiency of protein transfer onto the membrane [Ref: 1]. Considering the aforementioned reasons, we did not add molecular weights to the WB images.

Reference [1]. FUJIFILM Wako Pure Chemical Corporation, https://www.wako- chemicals.de/media/pdf/c7/5e/20/FUJIFILM-Wako_Phos-tag-R.pdf

• Additionally, torin or Lambda phosphatase treatment may be used to confirm the specificity of the band in separate experiments.

We appreciate the reviewer for bringing up this crucial point. Torin1 is a synthetic mTOR inhibitor by preventing the binding of ATP to mTOR, leading to the inactivation of both mTORC1 and mTORC2, whereas rapamycin primarily targets mTORC1 activity and may inhibit mTORC2 in certain cell types after a prolonged treatment. We have identified that the predominant mediator of IBTK phosphorylation is the mTORC1/S6K1 complex. Therefore, in this context, we think that rapamycin is sufficient to inactivate the mTORC1/S6K1 pathway. As shown in Fig. 5F, the phosphorylated IBTK900-1150aa was markedly decreased while the non-phosphorylated form was simultaneously increased in rapamycin- treated cells. As per the reviewer's suggestion, we treated FLAG-IBTK900-1150aa overexpressed cells with lambda phosphatase. As shown in Fig. 5G, lambda phosphatase treatment completely abolished the mobility shifts of phosphorylated FLAG-IBTK900-1150aa. Additionally, the lowest band displayed an abundant accumulation of the non-phosphorylated form of FLAG-IBTK900-1150aa. These findings confirm that the mobility shifts observed in WB analysis correspond to the phosphorylated forms of FLAG-IBTK900-1150aa.

• Phos-tag gels with the IBTK CRISPR KO line would also help confirm that the non-phosphorylated band is indeed IBTK.

We appreciate the reviewer for bringing up this crucial point. As we state above, we performed Phos-tag assays to detect the mobility shifts of phosphorylated FLAG-IBTK900-1150aa. Anti-FLAG antibody, but not the anti-IBTK antibody was used for WB detection. This antibody does not exhibit cross-reactivity with endogenous IBTK.

• It is unclear why the lower, phosphorylated bands seem to be increasing (rather than decreasing) with AA starvation/ Rapa in Fig 5H.

We appreciate the reviewer for bringing up this crucial point. We think the panel the reviewer mentioned is Fig. 5F. According to the principle of Phos-tag assays, proteins with higher phosphorylation levels have slower migration rates on SDS-PAGE, while proteins with lower phosphorylation levels have faster migration rates.

As shown in Author response image 2, the green box indicates the most phosphorylated forms of FLAG-IBTK900-1150aa, the red box indicates the moderately phosphorylated forms of FLAG-IBTK900-1150aa, and the yellow box indicates the non-phosphorylated forms of FLAG-IBTK900-1150aa. AA starvation or Rapamycin treatment reduced the hyperphosphorylated forms of FLAG-IBTK900-1150aa (green box), while simultaneously increasing the hypophosphorylated (red box) and non- phosphorylated (yellow box) forms of FLAG-IBTK900-1150aa. Thus, we conclude that AA starvation or Rapamycin treatment leads to a marked decrease in the phosphorylation levels of FLAG-IBTK900-1150aa.

Author response image 2.

Reviewer #2 (Public Review):

Summary:

This study by Sun et al. identifies a novel role for IBTK in promoting cancer protein translation, through regulation of the translational helicase eIF4A1. Using a multifaceted approach, the authors demonstrate that IBTK interacts with and ubiquitinates eIF4A1 in a non-degradative manner, enhancing its activation downstream of mTORC1/S6K1 signaling. This represents a significant advance in elucidating the complex layers of dysregulated translational control in cancer.

Strengths:

A major strength of this work is the convincing biochemical evidence for a direct regulatory relationship between IBTK and eIF4A1. The authors utilize affinity purification and proximity labeling methods to comprehensively map the IBTK interactome, identifying eIF4A1 as a top hit. Importantly, they validate this interaction and the specificity for eIF4A1 over other eIF4 isoforms by co- immunoprecipitation in multiple cell lines. Building on this, they demonstrate that IBTK catalyzes non-degradative ubiquitination of eIF4A1 both in cells and in vitro through the E3 ligase activity of the CRL3-IBTK complex. Mapping IBTK phosphorylation sites and showing mTORC1/S6K1-dependent regulation provides mechanistic insight. The reduction in global translation and eIF4A1- dependent oncoproteins upon IBTK loss, along with clinical data linking IBTK to poor prognosis, support the functional importance.

Weaknesses:

While these data compellingly establish IBTK as a binding partner and modifier of eIF4A1, a remaining weakness is the lack of direct measurements showing IBTK regulates eIF4A1 helicase activity and translation of target mRNAs. While the effects of IBTK knockout/overexpression on bulk protein synthesis are shown, the expression of multiple eIF4A1 target oncogenes remains unchanged.

Summary:

Overall, this study significantly advances our understanding of how aberrant mTORC1/S6K1 signaling promotes cancer pathogenic translation via IBTK and eIF4A1. The proteomic, biochemical, and phosphorylation mapping approaches established here provide a blueprint for interrogating IBTK function. These data should galvanize future efforts to target the mTORC1/S6K1-IBTK-eIF4A1 axis as an avenue for cancer therapy, particularly in combination with eIF4A inhibitors.

Reviewer #1 (Recommendations For The Authors):

(1) Certain references should be provided for clarity. For e.g.,: Page 15, line 418 " The C-terminal glycine glycine (GG) amino acid residues are essential for Ub conjugation to targeted proteins".

We appreciate the reviewer for bringing up this crucial point. We have taken two fundamental review papers (PMID: 22524316, 9759494) on the ubiquitin system as references in this sentence.

(2) Please describe the properties of the ΔBTB mutant on page 15 when first describing it. What motifs does it lack and has it been described before in functional studies?

We appreciate the reviewer for bringing up this crucial point. We added a sentence to describe the properties of the ΔBTB mutant. This mutant lacks the BTB1 and BTB2 domains (deletion of aa 554–871), which have been previously demonstrated to be essential for binding to CUL3. The original reference has been added to the revised manuscript.

(3) In Figure 2G how do the authors explain the fact that co-expression of the Ub K-ALLR mutant, which is unable to form polyubiquitin chains, formed only a moderate reduction in IBTK-mediated eIF4A1 ubiquitination?

We appreciate the reviewer for bringing up this crucial point. The Ub K-ALLR mutant can indeed conjugate to substrate proteins, but it cannot form chains due to its absence of lysine residues, resulting in mono-ubiquitination. Multi- mono-ubiquitination refers to the attachment of single ubiquitin molecules to multiple lysine residues on a substrate protein. It's worth noting that a poly- ubiquitinated protein and a multi-mono-ubiquitinated protein appear strikingly similar in Western blot. Our findings demonstrated that the co-expression of the Ub K-ALL-R mutant resulted in only a modest reduction in IBTK-mediated eIF4A1 ubiquitination (Fig. 2G), and that eIF4A1 was ubiquitinated at twelve lysine residues when co-expressed with IBTK (Fig. S2F). As such, we conclude that the CRL3IBTK complex primarily catalyzes multi-mono-ubiquitination on eIF4A1. .

(4) In Figure 5, The identity of the seven sites in the IBTK 7ST A mutants should be specified.

We appreciate the reviewer for bringing up this crucial point. We have specified the seven mutation sites in the IBTK-7ST A mutant (Fig. 6A).

(5) In Figure 5, the rationale for generating antibodies only to S990/992/993, as opposed to the other mTORC1/S6K motifs should be specified.

We appreciate the reviewer for bringing up this crucial point. Upon demonstrating that IBTK can be phosphorylated—with evidence from positive Phos-tag and in vitro phosphorylation assays—we sought to directly detect changes in the phosphorylation levels using an antibody specific to IBTK phosphorylation. However, the expense of generating seven phosphorylation- specific antibodies for each site is significant. Recognizing that S990/992/993 are three adjacent sites, we deemed it appropriate to generate a single antibody to recognize the phospho-S990/992/993 epitope. Moreover, out of the seven phosphorylation sites, S992 perfectly matches the consensus motif for S6K1 phosphorylation (RXRXXS). Utilizing this antibody allowed us to observe a substantial decrease in the phosphorylation levels of these three adjacent Ser residues in IBTK following either AA deprivation or Rapamycin treatment (Fig. 5L). We have specified these points in the manuscript.

Reviewer #2 (Recommendations For The Authors):

The following suggestions would strengthen the study:

(1) Directly examine the effects of IBTK modulation (knockdown/knockout/ overexpression) on eIF4A1 helicase activity.

We appreciate the reviewer for bringing up this crucial point. We agree with the reviewer's suggestion that evaluating IBTK's influence on eIF4A1 helicase activity directly would enhance the strength of our conclusion. However, the current eIF4A1 helicase assays, as described in previous publications [Ref: 1, 2], can only be conducted using in vitro purified recombinant proteins. For instance, it is feasible to assess the varying levels of helicase activity exhibited by recombinant wild-type or mutant EIF4A1 proteins [Ref: 2]. Importantly, there is currently no reported methodology for evaluating the helicase activity of EIF4A1 in vivo, as mentioned by the reviewer in gene knockdown, knockout, or overexpression cellular contexts. Therefore, we have not performed these assays and we sincerely appreciate the reviewer's understanding in this regard. We sincerely appreciate the reviewer's understanding regarding this matter.

Reference:

[1] Chu J, Galicia-Vázquez G, Cencic R, Mills JR, Katigbak A, Porco JA, Pelletier J. CRISPR-mediated drug-target validation reveals selective pharmacological inhibition of the RNA helicase, eIF4A. Cell reports. 2016 Jun 14;15(11):2340-7.

[2] Chu J, Galicia-Vázquez G, Cencic R, Mills JR, Katigbak A, Porco JA, Pelletier J. CRISPR-mediated drug-target validation reveals selective pharmacological inhibition of the RNA helicase, eIF4A. Cell reports. 2016 Jun 14;15(11):2340-7.

(2) Justify why the expression of some but not all eIF4A1 target oncogenes is affected in IBTK-depleted/overexpressing cells. This is important if IBTK should be considered as a therapeutic target. The authors should consider which of the eIF4A1 targets are most impacted by IBTK KO. This would provide a more focused therapeutic approach in the future.

We appreciate the reviewer for bringing up this crucial point. As the reviewer has pointed out, we assessed the protein levels of ten reported eIF4A1 target genes across three cancer cell lines (Fig.4, Fig. S4A, C）. We observed that IBTK depletion led to a substantial reduction in the protein levels of most eIF4A1- regulated oncogenes upon IBTK depletion, although there were some exceptions. For instance, IBTK KO in H1299 cells exerted minimal influence on the protein levels of ROCK1 (Fig. S4A). Several possible explanations might account for this observation: firstly, given that our list of eIF4A1 target genes collected from previous studies conducted using distinct cell lines, it is not unexpected for different lines to exhibit subtle differences in regulation of eIF4A1 target genes. Secondly, as a CRL3 adaptor, IBTK potentially performs other biological functions via ubiquitination of specific substrates; dysregulation of these could buffer the impact of IBTK KO on the protein expression of some eIF4A1 target genes. We added these comments to the Discussion section of the revised manuscript.

(3) Expand mTOR manipulation experiments (inhibition, Raptor knockout, activation) and evaluate impacts on IBTK phosphorylation, eIF4A1 ubiquitination, and translation.

The mTORC1 signaling pathway is constitutively active under normal culture conditions. In order to inhibit mTORC1 activation, we employed several approaches including AA starvation, Rapamycin treatment, or Raptor knockout. Our results have demonstrated that both AA starvation and rapamycin treatment led to a reduction in eIF4A1 ubiquitination (Fig. 5M). Moreover, we have included new findings in the revised manuscript, which highlight that Raptor knockout specifically decreases eIF4A1 ubiquitination (Fig. 5N). It is worth mentioning that the impacts of mTOR inhibition or activation on protein translation have been extensively investigated and documented in numerous studies. Therefore, in our study, we did not feel it necessary to examine these treatments further.

(4) Although not absolutely necessary, it would be nice to see if some of these findings are true in other cancer cell types.

We appreciate the reviewer for bringing up this crucial point. We concur with the reviewer's suggestion that including data from other cancer cell types would enhance the strength of our conclusion. While the majority of our data is derived from two cervical cancer cell lines, we have corroborated certain key findings— such as the impact of IBTK on eIF4A1 and its target gene expression—in H1299 cells (human lung cancer) (Fig. 2C, Fig. S4A, B) and in CT26 cells (murine colon adenocarcinoma) (Fig. S4C, D). Additionally, we demonstrated that IBTK promotes IFN-γ-induced PD-L1 expression and tumor immune escape in both the H1299 and CT26 cells (Fig. S6A-K).

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review):

In the article by Dearlove et al., the authors present evidence in strong support of nucleotide ubiquitylation by DTX3L, suggesting it is a promiscuous E3 ligase with capacity to ubiquitylate ADP ribose and nucleotides. The authors include data to identify the likely site of attachment and the requirements for nucleotide modification. 

While this discovery potentially reveals a whole new mechanism by which nucleotide function can be regulated in cells, there are some weaknesses that should be considered. Is there any evidence of nucleotide ubiquitylation occurring cells? It seems possible, but evidence in support of this would strengthen the manuscript. The NMR data could also be strengthened as the binding interface is not reported or mapped onto the structure/model, this seems of considerable interest given that highly related proteins do have the same activity. 

The paper is for the most part well well-written and is potentially highly significant 

Comments on revised version: 

The revised manuscript has addressed many of the concerns raised and clarified a number of points. As a result the manuscript is improved. 

The primary concern that remains is the absence of biological function for Ub-ssDNA/RNA and the inability to detect it in cells. Despite this the manuscript will be of interest to those in the ubiquitin field and will likely provoke further studies and the development of tools to better assess the cellular relevance. As a result this manuscript is important. 

We agree with the reviewer’s assessment.

Minor issue: 

Figure 1A - the authors have now included the constructs used but it would be more informative if the authors lined up the various constructs under the relevant domains in the full-length protein. 

Figure 1 will be fixed in the Version of Record.

Reviewer #2 (Public Review):

The manuscript by Dearlove et al. entitled "DTX3L ubiquitin ligase ubiquitinates single-stranded nucleic acids" reports a novel activity of a DELTEX E3 ligase family member, DTX3L, which can conjugate ubiquitin to the 3' hydroxyl of single-stranded oligonucleotides via an ester linkage. The findings that unmodified oligonucleotides can act as substrates for direct ubiquitylation and the identification of DTX3 as the enzyme capable of performing such oligonucleotide modification are novel, intriguing, and impactful because they represent a significant expansion of our view of the ubiquitin biology. The authors perform a detailed and diligent biochemical characterization of this novel activity, and key claims made in the article are well supported by experimental data. However, the studies leave room for some healthy skepticism about the physiological significance of the unique activity of DTX3 and DTX3L described by the authors because DTX3/DTX3L can also robustly attach ubiquitin to the ADP ribose moiety of NAD or ADP-ribosylated substrates. The study could be strengthened by a more direct and quantitative comparison between ubiquitylation of unmodified oligonucleotides by DTX3/DTX3L with the ubiquitylation of ADP-ribose, the activity that DTX3 and DTX3L share with the other members of the DELTEX family.

Comment on revised version:

In my opinion, reviewers' comments are constructively addressed by the authors in the revised manuscript, which further strengthens the revised submission and makes it an important contribution to the field. Specifically, the authors perform a direct quantitative comparison of two distinct ubiquitylation substrates, unmodified oligonucleotides and fluorescently labeled NADH and report that kcat/Km is 5-fold higher for unmodified oligos compared to NADH. This observation suggests that ubiquitylation of unmodified oligos is not a minor artifactual side reaction in vitro and that unmodified oligonucleotides may very well turn out to be the physiological substrates of the enzyme. However, the true identity of the physiological substrates and the functionally relevant modification site(s) remain to be established in further studies. 

We agree with the reviewer’s assessment.

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

Public Reviews: 

Reviewer #1 (Public Review): 

In the article by Dearlove et al., the authors present evidence in strong support of nucleotide ubiquitylation by DTX3L, suggesting it is a promiscuous E3 ligase with capacity to ubiquitylate ADP ribose and nucleotides. The authors include data to identify the likely site of attachment and the requirements for nucleotide modification. 

While this discovery potentially reveals a whole new mechanism by which nucleotide function can be regulated in cells, there are some weaknesses that should be considered. Is there any evidence of nucleotide ubiquitylation occurring cells? It seems possible, but evidence in support of this would strengthen the manuscript. The NMR data could also be strengthened as the binding interface is not reported or mapped onto the structure/model, this seems of considerable interest given that highly related proteins do have the same activity. 

The paper is for the most part well well-written and is potentially highly significant, but it could be strengthened as follows: 

(1) The authors start out by showing DTX3L binding to nucleotides and ubiquitylation of ssRNA/DNA. While ubiquitylation is subsequently dissected and ascribed to the RD domains, the binding data is not followed up. Does the RD protein alone bind to the nucleotides? Further analysis of nucleotide binding is also relevant to the Discussion where the role of the KH domains is considered, but the binding properties of these alone have not been analysed. 

We thank the reviewer for the suggestion. We have tested DTX3L RD for ssDNA binding using NMR (see Figure 4A and Figure S2), which showed that DTX3L RD binds ssDNA. We have now tested the DTX3L KH domains for RNA/ssDNA binding using an FP experiment. However, the FP experiment did not show significant changes upon titrating RNA/ssDNA, suggesting that the KH domains alone are not sufficient to bind RNA/ssDNA. We have opted to put this data in the response-to-review as future investigation will be required to examine whether other regions of DTX3L cooperate with RD to bind RNA/ssDNA. We have revised the Discussion on the KH domains. We now state that “Our findings show the DTX3L DTC domain binds nucleic acids but whether the KHL domains contribute to nucleic acid binding requires further investigation.”

Author response image 1.

Fold change of fluorescence polarisation of 6-FAM-labelled ssDNA D4 upon titrating with DTX3L variants. DTX3L KH domain fragments were expressed with a N-terminal His-MBP tag to increase the molecular weight to enhance the signal.

(2) With regard to the E3 ligase activity, can the authors account for the apparent decreased ubiquitylation activity of the 232-C protein in Figure 1/S1 compared to FL and RD? 

We found that the 232-C protein batch used in the assay was not pure and have subsequently re-purified the protein. We have repeated the ubiquitination of ssDNA and RNA (Fig. 1H and 1I) and 232-C exhibited similar activity as WT. Furthermore, we performed autoubiquitination (Fig. S1G) and E2~Ub discharge assay (Fig. S1H) to compare the activity. 232-C was slower in autoubiquitination (Fig. S1G), but showed similar activity in the E2~Ub discharge assay as WT. These findings suggest that the RING domain in 232-C is functional and 232-C likely lacks ubiquitination site(s) present in 1-231 region necessary for autoubiquitination.

(3) Was it possible to positively identify the link between Ub and ssDNA/RNA using mass spectrometry? This would overcome issues associated with labels blocking binding rather than modification. 

We have tried to use mass spectrometry to detect the linkage between Ub and ssDNA/RNA, but was unable to do so. We suspect that the oxyester linkage might be labile, posing a challenge for mass spectrometry techniques. Similarly, a recent preprint from Ahel lab, which utilises LC-MS, detects the Ub-NMP product rather than the linkage (https://www.biorxiv.org/content/10.1101/2024.04.19.590267v1.full.pdf).

(4) Furthermore, can a targeted MS approach be used to show that nucleotides are ubiquitylated in cells? 

This will require future development and improvement of the MS approach, specifically the isolation of labile oxyester-linked products from cells and the optimisation of the MS detection method.

(5) Do the authors have the assignments (even partial?) for DTX3L RD? In Figure 4 it would be helpful to identify the peaks that correspond to the residues at the proposed binding site. Also do the shifts map to a defined surface or do they suggest an extended site, particularly for the ssDNA.

We only collected HSQC spectra which was insufficient for assignments. We have performed a competition experiment using ADPr and labelled ssDNA, showing that ADPr competes against the ubiquitination of ssDNA (Figure 4D). We have also provided an additional experiment showing that ssDNA with a blocked 3’-OH can compete against ubiquitination of ADPr (Figure 4E). These data, together with our NMR analysis, further strengthen the evidence that ssDNA and ADPr compete the same binding pocket in DTX3L RD. Understanding how DTX3L RD binds ssDNA/RNA is an ongoing research in the lab.

(6) Does sequence analysis help explain the specificity of activity for the family of proteins? 

We have performed sequence alignment and structure comparison of DTX proteins using both RING and DTC domains (Fig. S3). These analyses showed that DTX3 and DTX3L RING domains lack a N-terminal helix and two loop insertions compared to DTX1, DTX2 and DTX4. These additions make DTX1, DTX2 and DTX4 RING domain larger than DTX3L and DTX3. It is not clear how these would influence the orientation of the recruited E2~Ub. Comparison of the DTC domain showed that DTX1, DTX2 and DTX4 contain an Ala-Arg motif, which causes a bulge at one end of DTC pocket. In the absence of Ala-Arg motif, DTC pockets of DTX3 and DTX3L contain an extended groove which might accommodate one or more of the nucleotides 5' to the targeted terminal nucleotide. It seems that both features of RING and DTC domains might attribute to the specificity of DTX3L and DTX3. We have included these comparisons in the discussion and suggested that future structural characterization is necessary to unveil the specificity.

(7) While including a summary mechanism (Figure 5I) is helpful, the schematic included does not necessarily make it easier for the reader to appreciate the key findings of the manuscript or to account for the specificity of activity observed. While this figure could be modified, it might also be helpful to highlight the range of substrates that DTX3L can modify - nucleotide, ADPr, ADPr on nucleotides etc. 

We have modified this Figure to include the range of substrates.

Reviewer #2 (Public Review): 

Summary: 

The manuscript by Dearlove et al. entitled "DTX3L ubiquitin ligase ubiquitinates single-stranded nucleic acids" reports a novel activity of a DELTEX E3 ligase family member, DTX3L, which can conjugate ubiquitin to the 3' hydroxyl of single-stranded oligonucleotides via an ester linkage. The findings that unmodified oligonucleotides can act as substrates for direct ubiquitylation and the identification of DTX3 as the enzyme capable of performing such oligonucleotide modification are novel, intriguing, and impactful because they represent a significant expansion of our view of the ubiquitin biology. The authors perform a detailed and diligent biochemical characterization of this novel activity, and key claims made in the article are well supported by experimental data. However, the studies leave room for some healthy skepticism about the physiological significance of the unique activity of DTX3 and DTX3L described by the authors because DTX3/DTX3L can also robustly attach ubiquitin to the ADP ribose moiety of NAD or ADP-ribosylated substrates. The study could be strengthened by a more direct and quantitative comparison between ubiquitylation of unmodified oligonucleotides by DTX3/DTX3L with the ubiquitylation of ADP-ribose, the activity that DTX3 and DTX3L share with the other members of the DELTEX family. 

Strengths: 

The manuscript reports a novel and exciting observation that ubiquitin can be directly attached to the 3' hydroxyl of unmodified, single-stranded oligonucleotides by DTX3L. The study builds on the extensive expertise and the impactful previous studies by the Huang laboratory of the DELTEX family of E3 ubiquitin ligases. The authors perform a detailed and diligent biochemical characterization of this novel activity, and all claims made in the article are well supported by experimental data. The manuscript is clearly written and easy to read, which further elevates the overall quality of submitted work. The findings are impactful and will help illuminate multiple avenues for future follow-up investigations that may help establish how this novel biochemical activity observed in vitro may contribute to the biological function of DTX3L. The authors demonstrate that the activity is unique to the DTX3/DTX3L members of the DELTEX family and show that the enzyme requires at least two single-stranded nucleotides at the 3' end of the oligonucleotide substrate and that the adenine nucleotide is preferred in the 3' position. Most notably, the authors describe a chimeric construct containing RING domain of DTX3L fused to the DTC domain DTX2, which displays robust NAD ubiquitylation, but lacks the ability to ubiquitylate unmodified oligonucleotides. This construct will be invaluable in the future cell-based studies of DTX3L biology that may help establish the physiological relevance of 3' ubiquitylation of nucleic acids. 

Weaknesses: 

The main weakness of the study is in the lack of direct evidence that the ubiquitylation of unmodified oligonucleotides reported by the authors plays any role in the biological function of DTX3L. The study leaves plenty of room for natural skepticism regarding the physiological relevance of the reported activity, because, akin to other DELTEX family members, DTX3 and DTX3L can also catalyze attachment of ubiquitin to NAD, ADP ribose and ADP-ribosylated substrates. Unfortunately, the study does not offer any quantitative comparison of the two distinct activities of the enzyme, which leaves plenty of room for doubt. One is left wondering, whether ubiquitylation of unmodified oligonucleotides is just a minor and artifactual side activity owing to the high concentration of the oligonucleotide substrates and E2~Ub conjugates present in the in-vitro conditions and the somewhat lower specificity of the DTX3 and DTX3L DTC domains (compared to DTX2 and other DELTEX family members) for ADP ribose over other adenine-containing substrates such as unmodified oligonucleotides, ADP/ATP/dADP/dATP, etc. The intriguing coincidence that DTX3L, which is the only DTX protein capable of ubiquitylating unmodified oligonucleotides, is also the only family member that contains nucleic acid interacting domains in the N-terminus, is suggestive but not compelling. A recently published DTX3L study by a competing laboratory (PMID: 38000390), which is not cited in the manuscript, suggests that ADP-ribose-modified nucleic acids could be the physiologically relevant substrates of DTX3L. That competing hypothesis appears more convincing than ubiquitylation of unmodified oligonucleotides because experiments in that study demonstrate that ubiquitylation of ADP-ribosylated oligos is quite robust in comparison to ubiquitylation of unmodified oligos, which is undetectable. It is possible that the unmodified oligonucleotides in the competing study did not have adenine in the 3' position, which may explain the apparent discrepancy between the two studies. In summary, a quantitative comparison of ubiquitylation of ADP ribose vs. unmodified oligonucleotides could strengthen the study. 

We thank the reviewer for the constructive feedback. We agree that evidence for the biological function is lacking. While we have tried to detect Ub-ssDNA/RNA from cells, we found that isolating and detecting labile oxyester-linked Ub-ssDNA/RNA products remain challenging due to (1) low levels of Ub-ssDNA/RNA products, (2) the presence of DUBs and nucleases that rapidly remove the products during the experiments, and (3) our lack of a suitable MS approach to detect the product. For these reasons, we feel that discovering the biological function will require future effort and expertise and is beyond the scope of our current manuscript.

In the manuscript (PMID: 38000390), the authors used PARP10 to catalyse ADP-ribosylation onto 5’-phosphorylated ssDNA/RNA. They used the following sequences which lacks 3’-adenosine, which could explain the lack of ubiquitination.

E15_5′P_RNA [Phos]GUGGCGCGGAGACUU

E15_5′P_DNA [Phos]GTGGCGCGGAGACTT

We have performed the experiment using this sequence to verify this (see Author response image 2 below). We have cited this manuscript but for some reasons, Pubmed has updated its published date from mid 2023 to Jan 2024. We have updated the Endnote in the revised manuscript.

Author response image 2.

Fluorescently detected SDS-PAGE gel of in vitro ubiquitination catalysed by DTX3L-RD in the presence ubiquitination components and 6-FAM-labelled ssDNA D4 or D31.

We agree that it is crucial to compare ubiquitination of oligonucleotides and ADPr by DTX3L to find its preferred substrate. We have challenged oligonucleotide ubiquitination by adding excess ADPr and found that ADPr efficiently competes with oligonucleotide (Figure 4D). We have also performed an experiment showing that ssDNA with a blocked 3’-OH can compete against ubiquitination of ADPr (Figure 4E). These data support that ADPr and ssDNA compete for the same binding site on DTX3L.

We also performed kinetic analysis of ubiquitination of fluorescently labelled ssDNA (D4) and NAD+ by DTX3L-RD (Fig. 4F and Fig. S2D–G) to assess substrate preferences. Here, we used fluorescent-labelled NAD+ (F-NAD+) in place of ADPr as labelled NAD+ is commercially available. With the known concentration of fluorescently labelled ssDNA and NAD+ as the standard, we could estimate the rate of ubiquitinated product formation across different substrate concentrations. We have included this finding in the main text “DTX3L-RD displayed _k_cat value of 0.0358 ± 0.0034 min-1 and a _K_m value of 6.56 ± 1.80 mM for Ub-D4 formation, whereas the Michaelis-Menten curve did not reach saturation for Ub-F-NAD+ formation (Fig. 4F and fig. S2, D-G). Comparison of the estimated catalytic efficiency (_k_cat/_K_m = 5457  M-1 min-1 for D4 and estimated _k_cat/_K_m = 1190  M-1 min-1 for F-NAD+; Fig. 4F) suggested that DTX3L-RD exhibited 4.5-fold higher catalytic efficiency for D4 than F-NAD+. This difference primarily results from a better _K_m value for D4 compared to F-NAD+. Although DTX3L-RD showed weak _K_m for F-NAD+, it displays a higher rate for converting F-NAD+ to Ub-F-NAD+ at higher substrate concentration (Fig. 4F). Thus, substrate concentration will play a role in determining the preference.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Writing/technical points: 

(1) The introduction is relatively complex and the last paragraph, which reviews the discoveries on the paper, is long. It may be helpful to highlight the significance and frame the experiments as what they have addressed, rather than detailing each set of experiments completed. 

We have modified the last paragraph in the introduction to highlight the major discovery of our work.

(2) Line 24, Abstract. 'Its N-terminal region' is not obvious 

We have changed “Its N-terminal region” to “the N-terminal region of DTX3L”.

(3) Line 44 - split sentence to emphasize E3 ligase point? 

We have modified the sentence as suggested.

(4) Figures 1B and 1C could be larger - currently they are not very helpful. Also atoms (ADPr?) are shown, but not indicated in the legend or labelled on the panel. 

We have enlarged Figures 1B and 1C and indicated RNA on the structure.

(5) The structure of the D2 domain of DTX3L has recently been reported (Vela-Rodriguez et al). It might be helpful to comment on this manuscript. 

We have now commented on D2 domain in the results section and in the discussion.

(6) It would be helpful to indicate the DTX3L constructs used in Figure 1a. 

We have included all DTX3L constructs used in Figure 1a.

(7) Interpretation of Figure 4A is difficult, the authors may wish to consider other ways to visualize the data. 

We have now removed the black arrow in Figure 4A as it was confusing. Instead, we drew a black box on the cross-peak where the close-up views are shown in Figures 4B and 4C.

(8) Figure 4A. Please indicate which binding partner is highlighted by red/black arrows. 

We have removed black arrow. The red arrows indicate cross-peaks which undergo chemical shift perturbation when DTX3L-RD was titrated with ssDNA or ADPr, highlighting their binding sites on DTX3L-RD overlap.

(9) Line 284 - please indicate the bulge in Figure S3. 

We have indicated the bulge on Figure S3.

(10) Aspects of the discussion are speculative, given that evidence of Ub conjugated to nucleotides in cells is yet to be obtained and the functional consequences of modification are uncertain. 

We understand that the discussion on the potential roles of ubiquitination of ssNAs is speculative. We have now modified it to: “Based on the known functions of the DTX3L/PARP9 complex and the findings of this study, we propose several hypotheses for future research”, so that readers will understand that these are speculative.

(11) Line 295 onwards - this paragraph discusses the role of the KH domains in nucleotide binding, but it is not clear that the authors have directly demonstrated that the KH domains bind nucleotides as all constructs used in the binding experiments in Figure 1/S1 include the RING-DTC domains. 

We found that KH domains alone did not bind ssDNA or RNA. We have modified line 295. This section now reads “Typically, KH domains contain a GXXG motif within the loop between the first and second α helix (22). However, analysis of the sequence of the KHL domains in DTX3L shows these domains lack this motif. Multiple studies have shown that mutation in this motif abolishes binding to nucleic acids (23-26). Our findings show the DTX3L DTC domain binds nucleic acids but whether the KHL domains contribute to nucleic acid binding requires further investigation. Additionally, the structure of the first KHL domain was recently reported and shown to form a tetrameric assembly (20). Our analysis with DTX3L 232-C, which lacks the first KHL domain and RRM, indicate that it can still bind ssDNA and ssRNA. Despite this, a more detailed analysis will be required to determine whether oligomerization plays a role in nucleic acid binding and ubiquitination.”

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Contractile Injection Systems (CIS) are versatile machines that can form pores in membranes or deliver effectors. They can act extra or intracellularly. When intracellular they are positioned to face the exterior of the cell and hence should be anchored to the cell envelope. The authors previously reported the characterization of a CIS in Streptomyces coelicolor, including significant information on the architecture of the apparatus. However, how the tubular structure is attached to the envelope was not investigated. Here they provide a wealth of evidence to demonstrate that a specific gene within the CIS gene cluster, cisA, encodes a membrane protein that anchors the CIS to the envelope. More specifically, they show that:

- CisA is not required for assembly of the structure but is important for proper contraction and CIS-mediated cell death

- CisA is associated to the membrane (fluorescence microscopy, cell fractionation) through a transmembrane segment (lacZ-phoA topology fusions in E. coli)

- Structural prediction of interaction between CisA and a CIS baseplate component<br /> - In addition they provide a high-resolution model structure of the >750-polypeptide Streptomyces CIS in its extended conformation, revealing new details of this fascinating machine, notably in the baseplate and cap complexes.

All the experiments are well controlled including trans-complemented of all tested phenotypes.

One important information we miss is the oligomeric state of CisA.

Thank you for this suggestion. We now provide information on the potential oligomeric state of CisA. We performed further AlphaFold3 modelling of CisA using an increasing number of CisA protomers (1 to 8). We ran predictions for the configuration using the sequence of the well-folded C-terminal CisA domain (amino acids 285-468), which includes the transmembrane domain and the conserved domain that shares similarities to carbohydrate-degrading domains. The obtained confidence scores (mean values for pTM=0.73, ipTM=0.7, n=5) indicate that CisA can assemble into a pentamer and that this oligomerization is mediated through the interaction of the C-terminal solute-binding like superfamily domain.

We have added this information to the revised manuscript (Fig. 3b/c) and further discuss the possible implications of CisA oligomerization for its proposed mode of action.

While it would have been great to test the interaction between CisA and Cis11, to perform cryo-electron microscopy assays of detergent-extracted CIS structures to maintain the interaction with CisA, I believe that the toxicity of CisA upon overexpression or upon expression in E. coli render these studies difficult and will require a significant amount of time and optimization to be performed. It is worth mentioning that this study is of significant novelty in the CIS field because, except for Type VI secretion systems, very few membrane proteins or complexes responsible for CIS attachment have been identified and studied.

We thank this reviewer for their highly supportive and positive comments on our manuscript and we are grateful for their recognition of the novelty of our study, particularly in the context of membrane proteins and complexes involved in CIS attachment.

We agree that further experimental evidence on direct interaction between CisA and Cis11 would have strengthened our model on CisA function. However, as noted by this reviewer, this additional work is technically challenging and currently beyond the scope of this study.

Reviewer #2 (Public review):

Summary:

The overall question that is addressed in this study is how the S. coelicolor contractile injection system (CISSc) works and affects both cell viability and differentiation, which it has been implicated to do in previous work from this group and others. The CISSc system has been enigmatic in the sense that it is free-floating in the cytoplasm in an extended form and is seen in contracted conformation (i.e. after having been triggered) mainly in dead and partially lysed cells, suggesting involvement in some kind of regulated cell death. So, how do the structure and function of the CISSc system compare to those of related CIS from other bacteria, does it interact with the cytoplasmic membrane, how does it do that, and is the membrane interaction involved in the suggested role in stress-induced, regulated cell death? The authors address these questions by investigating the role of a membrane protein, CisA, that is encoded by a gene in the CIS gene cluster in S. coelicolor. Further, they analyse the structure of the assembled CISSc, purified from the cytoplasm of S. coelicolor, using single-particle cryo-electron microscopy.

Strengths:

The beautiful visualisation of the CIS system both by cryo-electron tomography of intact bacterial cells and by single-particle electron microscopy of purified CIS assemblies are clearly the strengths of the paper, both in terms of methods and results. Further, the paper provides genetic evidence that the membrane protein CisA is required for the contraction of the CISSc assemblies that are seen in partially lysed or ghost cells of the wild type. The conclusion that CisA is a transmembrane protein and the inferred membrane topology are well supported by experimental data. The cryo-EM data suggest that CisA is not a stable part of the extended form of the CISSc assemblies. These findings raise the question of what CisA does.

We thank Reviewer #2 for the overall positive evaluation of our manuscript and the constructive criticism.

Weaknesses:

The investigations of the role of CisA in function, membrane interaction, and triggering of contraction of CIS assemblies, are important parts of the paper and are highlighted in the title. However, the experimental data provided to answer these questions appear partially incomplete and not as conclusive as one would expect.

We acknowledge that some aspects of our work remain unanswered. We are currently unable to conduct additional experiments because the two leading postdoctoral researchers on this project have moved on to new positions. We currently don’t have the extra manpower with a similar skill set to pick up the project.

The stress-induced loss of viability is only monitored with one method: an in vivo assay where cytoplasmic sfGFP signal is compared to FM5-95 membrane stain. Addition of a sublethal level of nisin lead to loss of sfGFP signal in individual hyphae in the WT, but not in the cisA mutant (similarly to what was previously reported for a CIS-negative mutant). Technically, this experiment and the example images that are shown give rise to some concern. Only individual hyphal fragments are shown that do not look like healthy and growing S. coelicolor hyphae. Under the stated growth conditions, S. coelicolor strains would normally have grown as dense hyphal pellets. It is therefore surprising that only these unbranched hyphal fragments are shown in Fig. 4ab.

We thank this Reviewer for their thoughtful criticism regarding the viability assays and the data presented in Figure 4. We acknowledge the importance of ensuring that the presented images reflect the physiological state of S. coelicolor under the stated growth conditions and recognize that hyphal fragments shown in Figure 4 do not fully capture the typical morphology of S. coelicolor. As pointed out by this reviewer, S. coelicolor grows in large hyphal clumps when cultured in liquid media, making the quantification of fluorescence intensities in hyphae expressing cytoplasmic GFP or stained with the membrane dye FM5-95 particularly challenging. To improve the image analysis and quantification of GFP and FM5-95-fluorescent intensities across the three S. coelicolor strains (wildtype, cisA deletion mutant and the complemented cisA mutant), we vortexed the cell samples before imaging to break up hyphal clumps, increasing hyphal fragments. The hyphae shown in our images were selected as representative examples across three biological replicates.

Further, S. coelicolor would likely be in a stationary phase when grown 48 h in the rich medium that is stated, giving rise to concern about the physiological state of the hyphae that were used for the viability assay. It would be valuable to know whether actively growing mycelium is affected in the same way by the nisin treatment, and also whether the cell death effect could be detected by other methods.

The reasoning behind growing S. coelicolor for 48 h before performing the fluorescence-based viability assay was that we (DOI: 10.1038/s41564-023-01341-x ) and others (e.g.: DOI: 10.1038/s41467-023-37087-7 ) previously showed that the levels of CIS particles peak at the transition from vegetative to reproductive/stationary growth, thus indicating that CIS activity is highest during this growth stage. The obtained results in this manuscript are consistent with previous results, in which we showed a similar effect on the viability of wildtype versus cis-deficient S. coelicolor strains (DOI: 10.1038/s41564-023-01341-x ) using nisin, the protonophore CCCP and UV radiation. The results presented in this study and our previous study are based on biological triplicate experiments and appropriate controls. Furthermore, our results are in agreement with the findings reported in a complementary study by Vladimirov et al. (DOI: 10.1038/s41467-023-37087-7 ) that used a different approach (SYTO9/PI staining of hyphal pellets) to demonstrate that CIS-deficient mutants exhibit decreased hyphal death.

Taken together, we believe that the results obtained from our fluorescence-based viability assay provide strong experimental evidence that functional CIS mediate hyphal cell death in response to exogenous stress.

The model presented in Fig. 5 suggests that stress leads to a CisA-dependent attachment of CIS assemblies to the cytoplasmic membrane, and then triggering of contraction, leading to cell death. This model makes testable predictions that have not been challenged experimentally. Given that sublethal doses of nisin seem to trigger cell death, there appear to be possibilities to monitor whether activation of the system (via CisA?) indeed leads to at least temporally increased interaction of CIS with the membrane.

We thank this reviewer for their suggestions on how to test our model further. This is a challenging experiment because we do not know the exact dynamics of how nisin stress is perceived and transmitted to CisA and CIS particles.

In an attempt to address this point, we have performed co-immunoprecipitation experiments using S. coelicolor cells that produced CisA-FLAG as bait, and which were treated with a sub-lethal nisin concentration for 0/15/45 min.  Mass spectrometry analysis of co-eluted peptides did not show the presence of CIS-associated peptides at the analyzed timepoints. While we cannot exclude the possibility that our experimental assay requires further optimization to successfully demonstrate a CisA-CIS interaction (e.g. optimization of the use of detergents to improve the solubilization of CisA from Streptomyces membrane, which is currently not an established method), an alternative and equally valid hypothesis is that the interaction between CIS particles and CisA is transient and therefore difficult to capture. We would like to mention, however, that we did detect CisA peptides in crude purifications of CIS particles from nisin-stressed cells (Supplementary Table 2, manuscript: line 301/302), supporting our proposed model that CisA can associate with CIS particles in vivo.

Further, would not the model predict that stress leads to an increased number of contracted CIS assemblies in the cytoplasm? No clear difference in length of the isolated assemblies if Fig. S7 is seen between untreated and nisin-exposed cells, and also no difference between assemblies from WT and cisA mutant hyphae.

The reviewer is correct that there is no clear difference in length in the isolated CIS particles shown in Figure S7. This is in line with our results, which show that CisA is not required for the correct assembly of CIS particles and their ability to contract in the presence and absence of nisin treatment. The purpose of Figure S7 was to support this statement. We would like to note that the particles shown in Figure S7 were purified from cell lysates using a crude sheath preparation protocol, during which CIS particles generally contract irrespective of the presence or absence of CisA. Thus, we cannot comment on whether there is an increased number of contracted CIS assemblies in the cytoplasm of nisin-exposed cells. To answer this point, we would need to acquire additional cryo-electron tomograms (cyroET) of the different strains treated with nisin. CryoET is an extremely time and labor-intensive task and given that we currently don’t know the exact dynamics of the CIS-CisA interaction following exogenous stress, we believe this experiment is beyond the scope of this work.

The interaction of CisA with the CIS assembly is critical for the model but is only supported by Alphafold modelling, predicting interaction between cytoplasmic parts of CisA and Cis11 protein in the baseplate wedge. An experimental demonstration of this interaction would have strengthened the conclusions.

We agree that direct experimental evidence of this interaction would have further strengthened the conclusions of our study, and we have extensively tried to provide additional experimental evidence. Unfortunately, because of the toxicity of cisA expression in E. coli and the possibly transient nature of the interaction under the experimental conditions used, we were unable to confirm this interaction by biochemical or biophysical techniques, such as co-purification or bacterial two-hybrid assays. Despite these technical challenges, we believe that the AlphaFold predictions provided a valuable hypothesis about the role of CisA in firing and the function of CIS particles in S. coelicolor.

The cisA mutant showed a similarly accelerated sporulation as was previously reported for CIS-negative strains, which supports the conclusion that CisA is required for function of CISSc. But the results do not add any new insights into how CIS/CisA affects the progression of the developmental life cycle and whether this effect has anything to do with the regulated cell death that is caused by CIS. The same applies to the effect on secondary metabolite production, with no further mechanistic insights added, except reporting similar effects of CIS and CisA inactivations.

Thank you for your feedback on this aspect of the manuscript. We would like to note that the main focus of this study was to provide further insight into how CIS contraction and firing are mediated in Streptomyces. We used the analysis of accelerated sporulation and secondary metabolite production as a readout to directly assess the functionality of CIS in the presence or absence of CisA and to complement the in situ cryoET data. In summary, our data significantly expand our knowledge of CIS function and firing in Streptomyces and suggest a model in which CisA plays an essential role in mediating the interaction of CIS particles with the membrane, which is required for CIS-mediated cell death. We discuss this model in more detail in the revised manuscript (Line 274-283).

We agree that we still don’t fully understand the full nature of the signals that trigger CIS contraction, but we do know that the production of CIS is an integral part of the Streptomyces multicellular life cycle as demonstrated by two independent previous studies by us and others (DOI: 10.1038/s41564-023-01341-x and DOI: 10.1038/s41467-023-37087-7 ).

We further speculate that the assembly and CisA-dependent firing of Streptomyces CIS particles could present a molecular mechanism to dismantle part of the vegetative mycelium. This form of “regulated cell death” could provide two key benefits: (1) to prevent the spread of local cellular damage to the rest of mycelium and (2) to provide additional nutrients for the rest of the mycelium to delay the terminal differentiation into spores, which in turn also affects the production of secondary metabolites.

Concluding remarks:

The work will be of interest to anyone interested in contractile injection systems, T6SS, or similar machineries, as well for people working on the biology of streptomycetes. There is also a potential impact of the work in the understanding of how such molecular machineries could have been co-opted during evolution to become a mechanism for regulated cell death. However, this latter aspect remains still poorly understood. Even though this paper adds excellent new structural insights and identifies a putative membrane anchor, it remains elusive how the Streptomyces CIS may lead to cell death. It is also unclear what the advantage would be to trigger death of hyphal compartments in response to stress, as well as how such cell death may impact (or accelerate) the developmental progression. Finally, it is inescapable to wonder whether the Streptomyces CIS could have any role in protection against phage infection.

We thank Reviewer #2 for the overall supportive assessment of our work. We will briefly discuss functional CIS's impact on Streptomyces development in the revised manuscript. We previously tested if Streptomyces could defend against phages but have not found any experimental evidence to support this idea (unpublished data). The analysis of phage defense mechanisms is an underdeveloped area in Streptomyces research, partly due to the currently limited availability of a diverse phage panel.

Reviewer #3 (Public review):

Summary:

In this work, Casu et al. have reported the characterization of a previously uncharacterized membrane protein CisA encoded in a non-canonical contractile injection system of Streptomyces coelicolor, CISSc, which is a cytosolic CISs significantly distinct from both intracellular membrane-anchored T6SSs and extracellular CISs. The authors have presented the first high-resolution structure of extended CISSc structure. It revealed important structural insights in this conformational state. To further explore how CISSc interacted with cytoplasmic membrane, they further set out to investigate CisA that was previously hypothesized to be the membrane adaptor. However, the structure revealed that it was not associated with CISSc. Using fluorescence microscope and cell fractionation assay, the authors verified that CisA is indeed a membrane-associated protein. They further determined experimentally that CisA had a cytosolic N-terminal domain and a periplasmic C-terminus. The functional analysis of cisA mutant revealed that it is not required for CISSc assembly but is essential for the contraction, as a result, the deletion significantly affects CISSc-mediated cell death upon stress, timely differentiation, as well as secondary metabolite production. Although the work did not resolve the mechanistic detail how CisA interacts with CISSc structure, it provides solid data and a strong foundation for future investigation toward understanding the mechanism of CISSc contraction, and potentially, the relation between the membrane association of CISSc, the sheath contraction and the cell death.

Strengths:

The paper is well-structured, and the conclusion of the study is supported by solid data and careful data interpretation was presented. The authors provided strong evidence on (1) the high-resolution structure of extended CISSc determined by cryo-EM, and the subsequent comparison with known eCIS structures, which sheds light on both its similarity and different features from other subtypes of eCISs in detail; (2) the topological features of CisA using fluorescence microscopic analysis, cell fractionation and PhoA-LacZα reporter assays, (3) functions of CisA in CISSc-mediated cell death and secondary metabolite production, likely via the regulation of sheath contraction.

Weaknesses:

(1) The data presented are not sufficient to provide mechanistic details of CisA-mediated CISSc contraction, as authors are not able to experimentally demonstrate the direct interaction between CisA with baseplate complex of CISSc (hypothesized to be via Cis11 by structural modeling), since they could not express cisA in E. coli due to its potential toxicity. Therefore, there is a lack of biochemical analysis of direct interaction between CisA and baseplate wedge. In addition, there is no direct evidence showing that CisA is responsible for tethering CISSc to the membrane upon stress, and the spatial and temporal relation between membrane association and contraction remains unclear. Further investigation will be needed to address these questions in future.

We thank Reviewer #3 for the supportive evaluation and constructive feedback of our study in the non-public review. We appreciate the recognition of the technical limitations of experimentally demonstrating a direct interaction between CisA and CIS baseplate complex, and we agree that further investigations in the future will hopefully provide a full mechanistic understanding of the spatiotemporal interaction of CisA and CIS particular and the subsequent CIS firing.

To further improve the manuscript, we will revise the text and clarify figures and figure legends as suggested in the non-public review.

Discussion:

Overall, the work provides a valuable contribution to our understanding on the structure of a much less understood subtype of CISs, which is unique compared to both membrane-anchored T6SSs and host-membrane targeting eCISs. Importantly, the work serves as a good foundation to further investigate how the sheath contraction works here. The work contributes to expanding our understanding of the diverse CIS superfamilies.

Thank you.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

- Magnification of the potential CisA-Cis11 model, with side chains at the interface, should be shown in Supplementary Figures 9/10 to help the reader appreciates the intercation between the two subunits.

Done. A zoomed-in view of the relevant side chains at the CisA-Cis11 interface has been added to Supplementary Figure 9e. For clarity, we decided not to highlight these residues in Supplementary Figure 10 because they are identical to those in Figure 9e.

- A model where CisA is positionned onto the baseplate (by merging the CisA-Cis11 model and the baseplate structure) will also be informative for the reader.

We agree that such a presentation would be helpful to visualize the proposed CisA-Cis11 interaction. However, the Cis11 residues predicted to bind CisA are buried in our cryoEM single-particle structure of the elongated Streptomyces CIS. This is not surprising, as the structure is based on a previously established non-contractile CIS mutant variant (PMCID: PMC10066040), which means we were only able to capture one specific configuration of the baseplate complex in the current work. This baseplate configuration is most likely structurally distinct from the baseplate configuration in contracted CIS particles. A similar observation was also reported for the baseplate complex of eCIS particles from Algoriphagus machipongonesis (PMCID: PMC8894135 ).  

We speculate that in Streptomyces, initial non-specific contacts between CisA and cytoplasmic CIS particles induce a rearrangement of baseplate components, resulting in the exposure of the relevant Cis11 residues, which in turn facilitates a transient interaction between CisA and Cis11. This interaction then leads to additional conformational changes within the baseplate complex, triggering sheath contraction and CIS firing.

We believe that a transient binding step is a crucial part of the activation process, contributing to the dynamic nature of the system.

- Providing information on the oligomeric state of CisA will strenghten the manuscript. Authors may consider having blue-native gel analysis of CisA-3xFLAG extracted from Streptomyces or E. coli membranes, or in vivo chemical cross-linking coupled to SDS-PAGE analyses. In case these quite straightforward experiments are not possible, the authors may consider providing AF3 models of various CisA multimers.

Thank you for these suggestions. Unfortunately, we currently don’t have the capability to conduct additional experiments. However, we have performed additional AF3 modelling to explore potential different configurations of CisA. The results of these analyses suggest that CisA can assemble into a pentamer (see also Response to reviewer 1). We speculate that CisA may exist in different oligomeric states and that membrane-localized CisA monomers oligomerize into a larger protein complex in response to a cellular or extracellular (e.g. nisin) signal, which could then directly or indirectly interact with CIS particles in the cytoplasm to facilitate their recruitment to the membrane and CIS firing. Such a stress-dependent conformational change of CisA could also be a safety mechanism to prevent accidental interaction of CisA with CIS particles and CIS firing.

We now show the AF model for the predicted CisA pentamer in Figure 3b/c and discuss the potential implications of the different CisA configurations in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

- The quantification of contracted versus extended CIS assemblies in the cytoplasm is only presented for the tomograms from the cisA mutant (graph in Fig. S2d). However, there are no data for the WT and complemented mutant to compare with. It would help to add such data, or at least refer to the previous quantification done for the WT in the previous paper. Further, would it be possible to illustrate the difference by measuring lengths of CIS assemblies and plot length distributions (assuming the extended ones are long and contracted are short)?

Thank you for your suggestions. We have included the results from our previous quantification of CIS assembly states observed in the WT in the revised manuscript (lines 106–110).

In the acquired tomograms of CIS particles observed in intact and dead hyphae, we consistently observed only two CIS conformations: the fully extended state (average length of 233 nm, diameter of 18 nm) and the fully contracted state (average length of 124 nm, diameter of 23 nm). We have added this information to the revised manuscript (lines 112-114).

- The Western blot in Fig. 3d, top panel, contains additional bands that are not mentioned. Are they non-specific bands? Absent in disA mutant? It would help if it was clarified in the legend what they are.

Correct, these additional bands are unspecific bands, which are also visible in the lysate and soluble fraction of wild-type sample (negative control, no FLAG-tagged protein). We have now labelled these bands in the figure and clarified the figure legend.

- Fig. S8a needs improvement. It was not possible to clearly see the stated effect of disA deletion on secondary metabolite production in these photos.

We agree and have removed figure panel S8a from the manuscript. The quantification of total actinorhodin production shown in Figure S8b convincingly shows a significantly reduction of actinorhodin production in the cisA deletion mutant compared to the wildtype and the complement mutant.

- It is not an important point, but the paragraph in lines 109-116 appears more like a re-iteration of the Introduction than Results.

We agree. We have removed the highlighted text from the Results section and added some of the information to the introduction.

- Line 206 appears to have a typo. Should it not be WT instead of WT cisA?

Correct. This is a typo which has been fixed. Thank you.

- At the end of the Discussion, it is suggested that a stepwise mechanism of recruiting CIS to the membrane and then triggering firing would prevent unwanted activation and self-inflicted death. Since both steps appear to be dependent in DisA, it would be good to more clearly spell out how such a stepwise mechanism would work and how it could prevent spontaneous and erroneous firing of the system.

Thank you for this suggestion. We have revised the text to clarify the proposed stepwise mechanism. Based on additional structural modeling, we propose that the conserved extra-cytoplasmic domain of CisA may play a role in sensing stress signals. Binding of a ‘stress-associated molecule’ could induce a conformational change in CisA, a hypothesis supported by: (1) Foldseek protein structure searches, which suggest that the conserved C-terminal CisA domain resembles substrate/solute-binding proteins, and (2) AlphaFold3 models predicting that CisA can form a pentamer via its putative substrate-binding domain. This suggests that a transition from CisA monomers to pentamers in response to stress may serve as a key checkpoint, activating CisA and facilitating the recruitment of CIS assemblies to the membrane, either directly or indirectly. Conversely, in the absence of a stress signal, CisA is likely to remain in its monomeric (resting) form, incapable of triggering CIS firing. We have revised the discussion to explain the proposed model in more detail.

We recognize that this model poses many testable hypotheses that we currently cannot test but aim to address in the future.

Reviewer #3 (Recommendations for the authors):

There are a few concerns potentially worth addressing to strengthen the study or for future investigation.

(1) It would be worth considering moving the first part of the result ('CisA is required for CISSc contraction in situ') after presenting the structure of extended CISSc, and combining it with the last part of the result section ('CisA is essential for the cellular function of CISSc'), as both parts describe the functional characterization of CisA.

We appreciate the reviewer’s suggestion but have chosen to retain the current order of the results. As this manuscript focuses on the role of CisA, we believe that first establishing a functional link between CisA and CIS contraction provides essential context and motivation for the study.

(2) Line 169: it is not clear to me if the fusion of CisA with mCherry is functional (if it complements the native CisA). Moreover, it was not shown if its localization changes under nisin stress or in the strain with non-contractile CISSc.

We have not tested if the CisA-mCherry fusion is fully functional. While we cannot exclude the possibility that the activity of this protein fusion is compromised in vivo, we believe that the described accumulation of CisA-mCherry at the membrane is accurate. This conclusion is further supported by the results obtained from protein fractionation experiments and the membrane topology assay (Figure 3).

We did not examine if the localization of CisA-mCherry changes in CIS mutant strains under nisin-stress, but this is something we will follow up on in the future.

(3) In ref 18, the previous work from the same team presented a functional fluorescent fusion of Cis2 (sheath), thus, it will be interesting to see if (i) Cis2 localization and dynamics is affected by the absence of CisA under normal and stressed conditions; (ii) if Cis2 shows any co-localization with CisA under normal and especially stressed conditions, and potentially, its timing correlation to ghost cell formation by time-lapse imaging of both fusions.

We thank this reviewer for the suggestions, and we plan to address these questions in the future.

(4) Line 261: it was hypothesized by authors that the cytosolic portion of CisA was required for interacting with Cis11. While it was not possible to verify the direct interaction at current state, a S. coelicolor mutant lacking this cytosolic domain may be of help to indirectly test the hypothesis. Moreover, it would be interesting to see if the cytosolic region alone is enough to induce the contraction upon stress (by removing the TM-C region). If so, whether it leads to cell death, or if it is insufficient to cause cell death without membrane association despite the sheath contraction. If not, it would suggest that membrane association occurs before contraction.

These are really great suggestions and if we had the manpower and resources, we would have performed these experiments. We plan to follow up on these questions in the future.

However, additional structural modelling of CisA indicates that CisA may exist in different configurations (see response to Reviewer #1 and #2), a monomeric and/or a pentameric configuration. In these structural models (revised Figure 3), CisA oligomerization is mediated by the annotated periplasmic solute-binding domain. It is conceivable that CisA oligomerization (e.g. in response to a stress signal) presents a critical checkpoint that results in a conformational change within CisA monomers that subsequently drives CisA oligomerization into a configuration primed to interact with CIS particles. We would therefore speculate that the expression of just the cytoplasmic CisA domain may not be sufficient for CIS contraction and cell death.

(5) Line 263: as it was not possible to express full-length cisA in E. coli, making it difficult to assess the interaction between CisA and Cis11, it may be worth considering expressing the cytosolic portion of CisA (ΔTM-C) instead of full-length CisA, or alternatively performing a co-immunoprecipitation assay of CisA (i.e., with an affinity tag) from S. coelicolor cultures under stressed conditions. However, I am aware that these may be beyond the scope of this work but can be considered for future investigation in general.

Thank you for your suggestions and your understanding that some of this work is beyond the scope of this work. We have performed CisA-FLAG co-immunoprecipitation experiments from S. coelicolor cultures that were treated with nisin for 0/15/45 min. However, mass spectrometry analysis of co-eluted peptides did not show the presence of CIS-associated peptides at the analysed timepoints. While we cannot exclude technical issues with our assays that resulted in an inefficient solubilization of CisA from Streptomyces membranes, an alternative hypothesis is that the interaction between CIS particles and CisA is very transient and therefore difficult to capture. We would like to mention, however, that we did detect CisA peptides in crude purifications of CIS particles from nisin-stressed cells (Supplementary Table 2, manuscript: line 301/302), supporting our proposed model that CisA can associate with CIS particles in vivo.

Minor points:

(1) I will suggest moving Supplementary Fig 2d with control quantification of WT strain and complementation strain (similar to Fig 3g from ref 18) to the main Fig 1, as the quantitative representation with better comparison without going back and forth to ref 18.

Thank you for your suggestion. Instead of moving Supplementary Fig. 2d to the main figure, we have added additional information in lines 106–110 to discuss the previous quantification of CIS assembly states in the WT, as described in our earlier work. We believe this approach allows readers to easily reference our established quantification without compromising the flow of the main figures.

(2) Line 52/785: as work of Ref 12 has recently been published DOI: 10.1126/sciadv.adp7088, the reference should be updated accordingly.

This reference has been updated. Thank you.

(3) A brief description of key differences between contracted (ref 18) and extended sheath structure will be a good addition for a broader audience.

Thank you for this suggestion. We have added more information on lines 178–180.

(4) Fig 3d: it is not clear how well the samples from different fractions were normalized in amount (volume and cell density), but there was an inconsistency in the amount of CisA-Flag in lysate, vs. soluble and membrane fractions (total protein amount combined from soluble fraction and membrane fraction together seemed to be more than in the lysate, while in theory it should be more or less equal; and the amount of WhiA from WT seemed to be less than from the CisA-Flag strain). In the method section, it was mentioned that 'The final pellet was dissolved in 1/10 of the initial volume with wash buffer (no urea). Equi-volume amounts of fractions were mixed with 2x SDS sample buffer and analyzed by immunoblotting.' But it is still not clear whether equivalent amounts (normalized to the same OD for example) were used and if we could directly compare. A brief clarification in the legend of how samples were prepared is needed.

The samples were normalized by first using the same volume of starting material (similar culture density and incubation period for each strain) and by loading equal volumes of each fraction for analysis. After fractionation, equi-volume amounts of the soluble and membrane protein fractions were mixed with 2× SDS sample buffer and subjected to immunoblotting, ensuring a consistent basis for comparison between samples. We have revised the figure legend and Material and Method sections to make this clear.

We agree that the amount of CisA-3xFLAG appears slightly lower in the “Lysate” fraction compared to the “Membrane” fraction in Figure 3d (now Fig. 3f). However, this does not affect the overall conclusion of this experiment, showing that CisA-3xFLAG is clearly enriched in the membrane fraction.

For reference, please find below the uncropped version of this Western blot image. Based on the signal of the unspecific bands, we would like to argue that equal amounts of samples obtained from the WT control strain (no FLAG epitope present) and a strain producing CisA-3xFLAG were loaded for each of the fractions. When we revisited this data, we noted that the protein size marker was wrong. This has been fixed.

Author response image 1.

(5) Fig. 4f: statistical analysis is missing.

The missing statistical analysis has been added to this figure and figure legend.

Author Response

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

eLife assessment

This study, utilizing CITE-Seq to explore CML, is considered a useful contribution to our understanding of treatment response. However, the reviewers express concern about the incomplete evidence due to the small sample size and recommend addressing these limitations. Strengthening the study with additional patient samples and validation measures would enhance its significance.

We thank the editors for the assessment of our manuscript. In view of the comments of the three reviewers, we have increased the number of CML patient samples analyzed to confirm all the major findings included in the manuscript. In total, more than 80 patient samples across different approaches have now been analyzed and incorporated in the revised manuscript.

To the best of our knowledge, this is the first single cell multiomics report in CML and differs substantially from the recent single cell omics-based reports where single modalities were measured one at a time (Krishnan et al., 2023; Patel et al., 2022). Thus, the sc-multiomic investigation of LSCs and HSCs from the same patient addresses a major gap in the field towards managing efficacy and toxicity of TKI treatment by enumerating CD26+CD35- LSCs and CD26-CD35+ HSCs burden and their ratio at diagnosis vs. 3 months of therapy. The findings suggest design of a simpler and cheaper FACS assay to simultaneously stratify CML patients for TKI efficacy as well as hematologic toxicity.

Reviewer 1:

Summary:

This manuscript by Warfvinge et al. reports the results of CITE-seq to generate singlecell multi-omics maps from BM CD34+ and CD34+CD38- cells from nine CML patients at diagnosis. Patients were retrospectively stratified by molecular response after 12 months of TKI therapy using European Leukemia Net (ELN) recommendations. They demonstrate heterogeneity of stem and progenitor cell composition at diagnosis, and show that compared to optimal responders, patients with treatment failure after 12 months of therapy demonstrate increased frequency of molecularly defined primitive cells at diagnosis. These results were validated by deconvolution of an independent previously published dataset of bulk transcriptomes from 59 CML patients. They further applied a BCR-ABL-associated gene signature to classify primitive Lin-CD34+CD38- stem cells as BCR:ABL+ and BCR:ABL-. They identified variability in the ratio of leukemic to non-leukemic primitive cells between patients, showed differences in the expression of cell surface markers, and determined that a combination of CD26 and CD35 cell surface markers could be used to prospectively isolate the two populations. The relative proportion of CD26-CD35+ (BCR:ABL-) primitive stem cells was higher in optimal responders compared to treatment failures, both at diagnosis and following 3 months of TKI therapy.

Strengths:

The studies are carefully conducted and the results are very clearly presented. The data generated will be a valuable resource for further studies. The strengths of this study are the application of single-cell multi-omics using CITE-Seq to study individual variations in stem and progenitor clusters at diagnosis that are associated with good versus poor outcomes in response to TKI treatment. These results were confirmed by deconvolution of a historical bulk RNAseq data set. Moreover, they are also consistent with a recent report from Krishnan et al. and are a useful confirmation of those results. The major new contribution of this study is the use of gene expression profiles to distinguish BCRABL+ and BCR-ABL- populations within CML primitive stem cell clusters and then applying antibody-derived tag (ADT) data to define molecularly identified BCR:ABL+ and BCR-ABL- primitive cells by expression of surface markers. This approach allowed them to show an association between the ratio of BCR-ABL+ vs BCR-ABL- primitive cells and TKI response and study dynamic changes in these populations following short-term TKI treatment.

Weaknesses:

One of the limitations of the study is the small number of samples employed, which is insufficient to make associations with outcomes with confidence. Although the authors discuss the potential heterogeneity of primitive stem, they do not directly address the heterogeneity of hematopoietic potential or response to TKI treatment in the results presented. Another limitation is that the BCR-ABL + versus BCR-ABL- status of cells was not confirmed by direct sequencing for BCR-ABL. The BCR-ABL status of cells sorted based on CD26 and CD35 was evaluated in only two samples. We also note that the surface markers identified were previously reported by the same authors using different single-cell approaches, which limits the novelty of the findings. It will be important to determine whether the GEP and surface markers identified here are able to distinguish BCR-ABL+ and BCR-ABL- primitive stem cells later in the course of TKI treatment. Finally, although the authors do describe differential gene expression between CML and normal, BCR:ABL+ and BCR:ABL-, primitive stem cells they have not as yet taken the opportunity to use these findings to address questions regarding biological mechanisms related to CML LSC that impact on TKI response and outcomes.

Reviewer #1 (Recommendations For The Authors):

Minor comment: Fig 4 legend -E and F should be C and D.

We thank the reviewer for positive assessment of our work. Here, we highlight the updates in the revised manuscript considering the feedback received.

Minor comment: Fig 4 legend -E and F should be C and D.

We have edited the revised manuscript accordingly

One of the limitations of the study is the small number of samples employed, which is insufficient to make associations with outcomes with confidence.

Although we performed CITE-seq for 9 CML patient samples at diagnosis, we extended our investigations to include additional samples (e.g., largescale deconvolution analysis of samples, Fig 3 C-E, qPCR for BCR::ABL1 status, Fig. 6A, and the ratio between CD35+ and CD26+ populations at diagnosis and during TKI therapy, Fig. 6C-D) as described in the manuscript.

In comparison to a scRNA-seq, multiomic CITE-seq involves preparation and sequencing of separate libraries corresponding to RNA and ADTs thereby being even more resource demanding limiting our capacity to process an extensive number of patient samples. To confirm our findings in a larger cohort we have therefore adopted a computational deconvolution approach, CIBERSORT to analyze a larger number of independent samples (n=59). This reflects a growing, sustainable trend to study larger number of patients in face of still prohibitively expensive but potentially insightful scomics approaches (For example, please see Zeng et al, A cellular hierarchy framework for understanding heterogeneity and predicting drug response in acute myeloid leukemia, Nature Medicine, 2022).

However, in view of the comment, we have now substantially increased the number of analyzed patients in the revised manuscript. These include increased number of patient samples to investigate the ratio between CD35 and CD26 marked populations at diagnosis, and 3 months of TKI therapy (from n=8 to n=12 with now 6 optimal responders and 5 treatment failure at diagnosis and after TKI therapy), qPCR for BCR::ABL1 expression status at diagnosis (from n=3 to n=9) , and followed up the BCR::ABL1 expression in three additional samples after TKI therapy. Moreover, we examined the CD26 and CD35 marked populations for expression of GAS2, one of our top candidate LSC signature genes in three additional samples at diagnosis and at 3m follow up. Thus, >80 patient samples across different approaches have been analyzed to strengthen all major conclusions of the study.

We emphasize that we were cautious in generalizing the observation obtained from any one approach and sought to confirm any major finding using at least one complementary method. As an example, although CITE-seq (n=9) showed altered frequency of all cell clusters between optimal and poor responders (Fig. 3B), we refrained from generalizing because our independent large-scale computational deconvolution analysis (n=59) only substantiated the altered proportion of primitive and myeloid cell clusters (Fig. 3E).

Although the authors discuss the potential heterogeneity of primitive stem, they do not directly address the heterogeneity of hematopoietic potential or response to TKI treatment in the results presented.

Thanks for noting the discussion on heterogeneity of the primitive stem cells. As described in the original manuscript, the figure 6 D-E showed a relationship between heterogeneity and TKI therapy response. The results showed that CD35+/CD26+ ratio within the HSC fraction associated with this therapy response. We have now increased the number of patient samples analyzed and present the updated results in the revised manuscript (now figure 6 C-D). These observations set the stage for assessing whether long term therapy outcome can also be influenced by heterogeneity at diagnosis.

We have shown the hematopoietic potential of HSCs marked by CD35 expression in an independent parallel study and therefore only mentioned it concisely in the current manuscript. A combination of scRNA-seq, scATAC-seq and cell surface proteomics showed CD35+ cells at the apex of healthy human hematopoiesis, containing an HSCspecific epigenetic signature and molecular program, as well as possessing self-renewal capacity and multilineage reconstitution in vivo and vitro. The preprint is available as Sommarin et al. ‘Single-cell multiomics reveals distinct cell states at the top of the human hematopoietic hierarchy’, Biorxiv; https://www.biorxiv.org/content/10.1101/2021.04.01.437998v2.full

We also note that the surface markers identified were previously reported by the same authors using different single-cell approaches, which limits the novelty of the findings.

Our current manuscript is indeed a continuation of and builds onto our previous paper (Warfvinge R et al. Blood, 2017). In contrast to our previous report which was limited to examination of only 96 genes per cell, CITE-seq allowed us to examine the molecular program of cells using unbiased global gene expression profiling. Finally, although CD26 appears, once again as a reliable marker of BCR::ABL1+ primitive cells, CD35 emerges as a novel and previously undescribed marker of BCR::ABL1- residual stem cells. A combination of CD35 and CD26 allowed us to efficiently distinguish between the two populations housed within the Lin-34+38/low stem cell immunophenotype.

Another limitation is that the BCR-ABL + versus BCR-ABL- status of cells was not confirmed by direct sequencing for BCR-ABL. The BCR-ABL status of cells sorted based on CD26 and CD35 was evaluated in only two samples

Single cell detection of fusion transcripts is challenging with low detection sensitivity in single cell RNA-seq as has been noted previously (Krishnan et al. Blood, 2023, Giustacchini et al. Nature Medicine, 2017, Rodriguez-Meira et al. Molecular Cell, 2019). However, this is likely to change with the inclusion of targetspecific probes in scRNA-seq library preparation protocols. Nonetheless, in view of the comment, we have included more patient samples (from the previous n=3 to current n=10 (including TKI treated samples) for direct assessment of BCR-ABL1 status by qPCR analysis; the updated results are included in the revised manuscript (Figure 6A).

It will be important to determine whether the GEP and surface markers identified here are able to distinguish BCR-ABL+ and BCR-ABL- primitive stem cells later in the course of TKI treatment.

We performed qPCR to check for BCR::ABL1 status, and the level of GAS2, one of the top genes expressed in CML cells within CD26+ and CD35+ cells at diagnosis and following 3 months of TKI therapy. The results showed that while CD26+ are BCR::ABL1+, the CD35+ cells are BCR::ABL1- at both time points. Moreover, the expression of LSC-specific gene, GAS2 was specific to BCR::ABL1+ CD26+ cells at both diagnosis as well as following 3 months of TKI therapy. The new results are presented in figure 6B in the revised manuscript.

Finally, although the authors do describe differential gene expression between CML and normal, BCR:ABL+ and BCR:ABL-, primitive stem cells they have not as yet taken the opportunity to use these findings to address questions regarding biological mechanisms related to CML LSC that impact on TKI response and outcomes.

We agree with the reviewer that our major focus here was to characterize the cellular heterogeneity coupled to treatment outcome and therefore we did not delve deep into the molecular mechanisms underlying TKI response. However, in response to this comment, as mentioned above, we noted that one of the top genes in BCR::ABL1 cells (Fig. 4 C; right; in red), GAS2 (Growth Specific Arrest 2) was expressed at both diagnosis and TKI therapy within CD26+ cells relative to CD35+ cells (updated figure 6B). Interestingly, GAS2 was also detected in CML LSCs in a recent scRNA-seq study (Krishnan et al. Blood, 2023) suggesting GAS2 upregulation could be a consistent molecular feature of CML cells. GAS2 has been previously noted as deregulated in CML (Janssen JJ et al. Leukemia, 2005, Radich J et al, PNAS, 2006), control of cell cycle, apoptosis, and response to Imatinib (Zhou et al. PLoS One, 2014). Future investigations are warranted to assess whether GAS2 could play a role in the outcome of long-term TKI therapy.

Reviewer 2:

Summary:

The authors use single-cell "multi-comics" to study clonal heterogeneity in chronic myeloid leukemia (CML) and its impact on treatment response and resistance. Their main results suggest 1) Cell compartments and gene expression signatures both shared in CML cells (versus normal), yet 2) some heterogeneity of multiomic mapping correlated with ELN treatment response; 3) further definition of s unique combination of CD26 and CD35 surface markers associated with gene expression defined BCR::ABL1+ LSCs and BCR::ABL1- HSCs. The manuscript is well-written, and the method and figures are clear and informative. The results fit the expanding view of cancer and its therapy as a complex Darwinian exercise of clonal heterogeneity and the selective pressures of treatments.

Strengths:

Cutting-edge technology by one of the expert groups of single-cell 'comics.

Weaknesses:

Very small sample sizes, without a validation set. The obvious main problem with the study is that an enormous amount of results and conjecture arise from a very small data set: only nine cases for the treatment response section (three in each of the ELN categories), only two normal marrows, and only two patient cases for the division kinetic studies. Thus, it is very difficult to know the "noise" in the system - the stability of clusters and gene expression and the normal variation one might expect, versus patterns that may be reproducibly study artifact, effects of gene expression from freezing-thawing, time on the bench, antibody labeling, etc. This is not so much a criticism as a statement of reality: these elegant experiments are difficult, timeconsuming, and very expensive. Thus in the Discussion, it would be helpful for the authors to just frankly lay out these limitations for the reader to consider. Also in the Discussion, it would be interesting for the authors to consider what's next: what type of validation would be needed to make these studies translatable to the clinic? Is there a clever way to use these data to design a faster/cheaper assay?

We thank the reviewer for appraisal of our manuscript. We take the opportunity to point out the updates in the revised manuscript in view of the comments.

Very small sample sizes, without a validation set. The obvious main problem with the study is that an enormous amount of results and conjecture arise from a very small data set: only nine cases for the treatment response section (three in each of the ELN categories), only two normal marrows, and only two patient cases for the division kinetic studies.

As the reviewer has noted the single cell omics experiments remain resource demanding thereby placing a limitation on the number of patients analyzed. As described above in response to the comments from reviewer 1, multiomic CITE-seq allows extraction of two modalities in comparison to a typical scRNA-seq, however, this also makes it even more limited in the number of samples processed in a sustainable way. This was one of the motivations to analyze a larger number of independent samples (n=59) while benefiting from the insights gained from CITE-seq (n=9). Furthermore, by analyzing CD34+ cells from bone marrow and peripheral blood of CML patients, including both responders and non-responders after one year of Imatinib therapy, we were able to significantly diversity the patient pool, which was lacking in our CITE-seq patient pool. As mentioned above, this reflects a growing trend to analyze larger number of patients while anchoring the analysis on prohibitively expensive but potentially insightful sc-omics approaches (For example, please see Zeng et al, A cellular hierarchy framework for understanding heterogeneity and predicting drug response in acute myeloid leukemia, Nature Medicine, 2022).

As emphasized above, we frequently sought to confirm the findings from one approach using a complementary method and independent samples. For example, although CITE-seq (n=9) showed altered frequency of all cell clusters between optimal and poor responders (Fig. 3B), we refrained from generalizing because an independent largescale computational deconvolution analysis (n=59) only substantiated the altered proportion of primitive and myeloid clusters.

In view of the comment, we have now increased the number of patients analyzed during the revision process. These include increased numbers to investigate the ratio between CD35+ and CD26+ populations at diagnosis, as well as 3 months of TKI therapy, qPCR for BCR::ABL1, and patients examined for GAS2, one of the top genes expressed in CML cells (see response to reviewer 1 for details). Altogether, >80 patient samples across different approaches were analyzed to strengthen the conclusions.

During the revision, we have analyzed cells from 8 CML patients for cell cycle using gene activity scores. This is in addition to the cell division kinetics data reported previously are now together described in the supplementary figures 9C-F.

It is very difficult to know the "noise" in the system - the stability of clusters and gene expression and the normal variation one might expect, versus patterns that may be reproducibly study artifact, effects of gene expression from freezing-thawing, time on the bench, antibody labeling, etc. This is not so much a criticism as a statement of reality: these elegant experiments are difficult, time-consuming, and very expensive. Thus in the Discussion, it would be helpful for the authors to just frankly lay out these limitations for the reader to consider.

We agree with the reviewer that sc-omics approaches can be noisy despite continuing efforts to denoise single cell datasets through both experimental and bioinformatic innovations. Therefore, we have updated the discussion as recommended by the reviewer (paragraph 5 in the discussion).

We also note that CITE-seq, in contrast to scRNA-seq alone provides dual features: surface marker/protein as well as RNA for annotating the same cluster. In our manuscript, for example, cell clusters in UMAP for normal BM; Fig 1B were described using both surface markers (Fig. 1C) and RNA (Fig. 1D) making the cluster identity robust. To further elaborate this approach, a new supplementary figure 1C shows annotations of clusters using both RNA and surface markers.

To potentially address the issue of stability of clusters and gene expression, we compared the marker genes for major clusters from nBM from this study (supplementary table 4, Warfvinge et al.) with those described recently in a scRNA-seq study by Krishnan et al. supplementary table 8, Blood, 2023 using Cell Radar, a tool that identifies and visualizes which hematopoietic cell types are enriched within a given gene set (description: https://github.com/KarlssonG/cellradar

Direct link: https://karlssong.github.io/cellradar/). To compare, we used our in-house gene list for the major clusters as well as mapped the same number of top marker genes based on log2FC from corresponding cluster from Krishnan et al. as inputs to Cell Radar. The Cell Radar plot outputs are shown below.

Author response image 1.

This approach showed broad similarities across clusters from this study with their counterparts from the other study suggesting the cluster identities reported here are likely to be robust. Please note these figures are for reviewer response only and not included in the final manuscript.

Also in the Discussion, it would be interesting for the authors to consider what's next: what type of validation would be needed to make these studies translatable to the clinic? Is there a clever way to use these data to design a faster/cheaper assay?

Our findings on CD26+ and CD35+ surface markers to enrich BCR::ABL1+ and BCR::ABL1- cells suggest a simpler, faster and cheaper FACS panel can possibly quantify leukemic and non-leukemic stem cells in CML patients. We anticipate that future investigations, clinical studies might examine whether CD26CD35+ cells could be plausible candidates for restoring normal hematopoiesis once the TKI therapy diminishes the leukemic load, and whether patients with low counts of CD35+ cells at diagnosis have a relatively higher chance of developing hematologic toxicity such as cytopenia during therapy.

We briefly mentioned this possibility in the discussion; however, we have now moved it to another paragraph to highlight the same. Please see paragraph 5 in the revised manuscript.

Reviewer 3:

Summary:

In this study, Warfvinge and colleagues use CITE-seq to interrogate how CML stem cells change between diagnosis and after one year of TKI therapy. This provides important insight into why some CML patients are "optimal responders" to TKI therapy while others experience treatment failure. CITE-seq in CML patients revealed several important findings. First, substantial cellular heterogeneity was observed at diagnosis, suggesting that this is a hallmark of CML. Further, patients who experienced treatment failure demonstrated increased numbers of primitive cells at diagnosis compared to optimal responders. This finding was validated in a bulk gene expression dataset from 59 CML patients, in which it was shown that the proportion of primitive cells versus lineage-primed cells correlates to treatment outcome. Even more importantly, because CITE-seq quantifies cell surface protein in addition to gene expression data, the authors were able to identify that BCR/ABL+ and BCR/ABL- CML stem cells express distinct cell surface markers (CD26+/CD35- and CD26-/CD35+, respectively). In optimal responders, BCR/ABL- CD26-/CD35+ CML stem cells were predominant, while the opposite was true in patients with treatment failure. Together, these findings represent a critical step forward for the CML field and may allow more informed development of CML therapies, as well as the ability to predict patient outcomes prior to treatment.

Strengths:

This is an important, beautifully written, well-referenced study that represents a fundamental advance in the CML field. The data are clean and compelling, demonstrating convincingly that optimal responders and patients with treatment failure display significant differences in the proportion of primitive cells at diagnosis, and the ratio of BCR-ABL+ versus negative LSCs. The finding that BCR/ABL+ versus negative LSCs display distinct surface markers is also key and will allow for a more detailed interrogation of these cell populations at a molecular level.

Weaknesses:

CITE-seq was performed in only 9 CML patient samples and 2 healthy donors. Additional samples would greatly strengthen the very interesting and notable findings.

Reviewer #3 (Recommendations For The Authors):

My only recommendation is to bolster findings with additional CML and healthy donor samples.

CITE-seq was performed in only 9 CML patient samples and 2 healthy donors. Additional samples would greatly strengthen the very interesting and notable findings.

We thank the reviewer for the positive assessment of our manuscript. As mentioned in response to comments from reviewer 1 and 2, CITE-seq remains an reource consuming single cell method potentially limiting the number of patients to be analyzed. However, during the revision process, we have increased the number of patient material analyzed for other assays; these include increased number to investigate the ratio between CD35+ and CD26+ populations at diagnosis, and 3 months of TKI therapy, qPCR for BCR::ABL1, and patients examined for GAS2, one of the top genes expressed in CML cells. Thus, >80 patient samples across different assays have been analyzed to strengthen the conclusions. (Please see comment to reviewer 1 for more details)

Author response:

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

Reviewer #1 (Public review): 

Overall, the conclusions of the paper are mostly supported by the data but may be overstated in some cases, and some details are also missing or not easily recognizable within the figures. The provision of additional information and analyses would be valuable to the reader and may even benefit the authors' interpretation of the data. 

We thank the reviewer for the thoughtful and constructive feedback. We are pleased that the reviewer found the overall conclusions of our paper to be well supported by the data, and we appreciate the suggestions for improving figure clarity and interpretive accuracy. Below, we address each point with corresponding revisions.

The conclusion that DREADD expression gradually decreases after 1.5-2 years is only based on a select few of the subjects assessed; in Figure 2, it appears that only 3 hM4Di cases and 2 hM3Dq cases are assessed after the 2-year timepoint. The observed decline appears consistent within the hM4Di cases, but not for the hM3Dq cases (see Figure 2C: the AAV2.1-hSyn-hM3Dq-IRES-AcGFP line is increasing after 2 years.) 

We agree that our interpretation should be stated more cautiously, given the limited number of cases assessed beyond the two-year timepoint. In the revised manuscript, we have clarified in the Results that the observed decline is based on a subset of animals. We have also included a text stating that while a consistent decline was observed in hM4Di-expressing monkeys, the trajectory for hM3Dq expression was more variable with at least one case showing an increased signal beyond two years.

Revised Results section:

Lines 140, “hM4Di expression levels remained stable at peak levels for approximately 1.5 years, followed by a gradual decline observed in one case after 2.5 years, and after approximately 3 years in the other two cases (Figure 2B, a and e/d, respectively). Compared with hM4Di expression, hM3Dq expression exhibited greater post-peak fluctuations. Nevertheless, it remained at ~70% of peak levels after about 1 year. This post-peak fluctuation was not significantly associated with the cumulative number of DREADD agonist injections (repeated-measures two-way ANOVA, main effect of activation times, F_(1,6) = 5.745, P = 0.054). Beyond 2 years post-injection, expression declined to ~50% in one case, whereas another case showed an apparent increase (Figure 2C, c and m, respectively).”

Given that individual differences may affect expression levels, it would be helpful to see additional labels on the graphs (or in the legends) indicating which subject and which region are being represented for each line and/or data point in Figure 1C, 2B, 2C, 5A, and 5B. Alternatively, for Figures 5A and B, an accompanying table listing this information would be sufficient. 

We thank the reviewer for these helpful suggestions. In response, we have revised the relevant figures (Fig. 1C, 2B, 2C, and 5) as noted in the “Recommendations for the authors”, including simplifying visual encodings and improving labeling. We have also updated Table 2 to explicitly indicate the animal ID and brain regions associated with each data point shown in the figures.

While the authors comment on several factors that may influence peak expression levels, including serotype, promoter, titer, tag, and DREADD type, they do not comment on the volume of injection. The range in volume used per region in this study is between 2 and 54 microliters, with larger volumes typically (but not always) being used for cortical regions like the OFC and dlPFC, and smaller volumes for subcortical regions like the amygdala and putamen. This may weaken the claim that there is no significant relationship between peak expression level and brain region, as volume may be considered a confounding variable. Additionally, because of the possibility that larger volumes of viral vectors may be more likely to induce an immune response, which the authors suggest as a potential influence on transgene expression, not including volume as a factor of interest seems to be an oversight. 

We thank the reviewer for raising this important issue. We agree that injection volume could act as a confounding variable, particularly since larger volumes were used in only handheld cortical injections. This overlap makes it difficult to disentangle the effect of volume from those of brain region or injection method. Moreover, data points associated with these larger volumes also deviated when volume was included in the model.

To address this, we performed a separate analysis restricted to injections delivered via microinjector, where a comparable volume range was used across cases. In this subset, we included injection volume as additional factor in the model and found that volume did not significantly impact peak expression levels. Instead, the presence of co-expressed protein tags remained a significant predictor, while viral titer no longer showed a significant effect. These updated results have replaced the originals in the revised Results section and in the new Figure 5. We have also revised the Discussion to reflect these updated findings.

The authors conclude that vectors encoding co-expressed protein tags (such as HA) led to reduced peak expression levels, relative to vectors with an IRES-GFP sequence or with no such element at all. While interesting, this finding does not necessarily seem relevant for the efficacy of long-term expression and function, given that the authors show in Figures 1 and 2 that peak expression (as indicated by a change in binding potential relative to non-displaced radioligand, or ΔBPND) appears to taper off in all or most of the constructs assessed. The authors should take care to point out that the decline in peak expression should not be confused with the decline in longitudinal expression, as this is not clear in the discussion; i.e. the subheading, "Factors influencing DREADD expression," might be better written as, "Factors influencing peak DREADD expression," and subsequent wording in this section should specify that these particular data concern peak expression only. 

We appreciate this important clarification. In response, we have revised the title to "Protein tags reduce peak DREADD expression levels" in the Results section and “Factors influencing peak DREADD expression levels” in the Discussion section. Additionally, we specified that our analysis focused on peak ΔBP_ND values around 60 days post-injection. We have also explicitly distinguished these findings from the later-stage changes in expression seen in the longitudinal PET data in both the Results and Discussion sections.

Reviewer #1 (Recommendations for the authors):

(1) Will any of these datasets be made available to other researchers upon request?

All data used to generate the figures have been made publicly available via our GitHub repository (https://github.com/minamimoto-lab/2024-Nagai-LongitudinalPET.git). This has been stated in the "Data availability" section in the revised manuscript.

(2) Suggested modifications to figures:

a) In Figures 2B and C, the inclusion of "serotype" as a separate legend with individual shapes seems superfluous, as the serotype is also listed as part of the colour-coded vector

We agree that the serotype legend was redundant since this information is already included in the color-coded vector labels. In response, we have removed the serotype shape indicators and now represent the data using only vector-construct-based color coding for clarity in Figure 2B and C.

b) In Figures 3A and B, it would be nice to see tics (representing agonist administration) for all subjects, not just the two that are exemplified in panels C-D and F-H. Perhaps grey tics for the non-exemplified subjects could be used.

In response, we have included black and white ticks to indicate all agonist administration across all subjects in Figure 3A and B, with the type of agonist clearly specified.　

c) In Figure 4C, a Nissl- stained section is said to demonstrate the absence of neuronal loss at the vector injection sites. However, if the neuronal loss is subtle or widespread, this might not be easily visualized by Nissl. I would suggest including an additional image from the same section, in a non-injected cortical area, to show there is no significant difference between the injected and non-injected region.

To better demonstrate the absence of neuronal loss at the injection site, we have included an image from the contralateral, non-injected region of the same section for comparison (Fig. 4C).

d) In Figure 5A: is it possible that the hM3Dq construct with a titer of 5×10^13 gc/ml is an outlier, relative to the other hM3Dq constructs used?

We thank the reviewer for raising this important observation. To evaluate whether the high-titer constructs represented a statistical outlier that might artifactually influence the observed trends, we performed a permutation-based outlier analysis. This assessment identified this point in question, as well as one additional case (titer 4.6 x 10e13 gc/ml, #255, L_Put), as significant outlier relative to the distribution of the dataset.

Accordingly, we excluded these two data points from the analysis. Importantly, this exclusion did not meaningfully alter the overall trend or the statistical conclusions—specifically, the significant effect of co-expressed protein tags on peak expression levels remain robust. We have updated the Methods section to describe this outlier handling and added a corresponding note in the figure legend.

Reviewer #2 (Public review): 

Weaknesses 

This study is a meta-analysis of several experiments performed in one lab. The good side is that it combined a large amount of data that might not have been published individually; the downside is that all things were not planned and equated, creating a lot of unexplained variances in the data. This was yet judiciously used by the authors, but one might think that planned and organized multicentric experiments would provide more information and help test more parameters, including some related to inter-individual variability, and particular genetic constructs. 

We thank the reviewer for bringing this important point to our attention. We fully acknowledge that the retrospective nature of our dataset—compiled from multiple studies conducted within a single laboratory—introduces variability related to differences in injection parameters and scanning timelines. While this reflects the practical realities and constraints of long-term NHP research, we agree that more standardized and prospectively designed studies would better control such source of variances. To address this, we have added the following statement to the "Technical consideration" section in Discussion:

Lines 297, "This study included a retrospective analysis of datasets pooled from multiple studies conducted within a single laboratory, which inherently introduced variability across injection parameters and scan intervals. While such an approach reflects real-world practices in long-term NHP research, future studies, including multicenter efforts using harmonized protocols, will be valuable for systematically assessing inter-individual differences and optimizing key experimental parameters."

Reviewer #2 (Recommendations for the authors):

I just have a few minor points that might help improve the paper:

(1) Figure 1C y-axis label: should add deltaBPnd in parentheses for clarity.

We have added “ΔBP_ND” to the y-axis label for clarity.

The choice of a sigmoid curve is the simplest clear fit, but it doesn't really consider the presence of the peak described in the paper. Would there be a way to fit the dynamic including fitting the peak?

We agree that using a simple sigmoid curve for modeling expression dynamics is a limitation. In response to this and a similar comment from Reviewer #3, we tested a double logistic function (as suggested) to see if it better represented the rise and decline pattern. However, as described below, the original simple sigmoid curve was a better fit for the data. We have included a discussion regarding this limitation of this analysis. See Reviewer #3 recommendations (2) for details.

The colour scheme in Figure 1C should be changed to make things clearer, and maybe use another dimension (like dotted lines) to separate hM4Di from hM3Dq.

We have improved the visual clarity of Figure 1C by modifying the color scheme to represent vector construct and using distinct line types (dashed for hM4Di and solid for hM3Dq data) to separate DREADD type.

(2) Figure 2

I don't understand how the referencing to 100 was made: was it by selecting the overall peak value or the peak value observed between 40 and 80 days? If the former then I can't see how some values are higher than the peak. If the second then it means some peak values occurred after 80 days and data are not completely re-aligned.

We thank the reviewer for the opportunity to clarify this point. The normalization was based on the peak value observed between 40–80 days post-injection, as this window typically captured the peak expression phase in our dataset (see Figure 1). However, in some long-term cases where PET scans were limited during this period—e.g., with one scan performing at day 40—it is possible that the actual peak occurred later. Therefore, instances where ΔBP_ND values slightly exceeded the reference peak at later time points likely reflect this sampling limitation. We have clarified this methodological detail in the revised Results section to improve transparency.

The methods section mentions the use of CNO but this is not in the main paper which seems to state that only DCZ was used: the authors should clarify this

Although DCZ was the primary agonist used, CNO and C21 were also used in a few animals (e.g., monkeys #153, #221, and #207) for behavioral assessments. We have clarified this in the Results section and revised Figure 3 to indicate the specific agonist used for each subject. Additionally, we have updated the Methods section to clearly specify the use and dosage of DCZ, CNO, and C21, to avoid any confusion regarding the experimental design.

Reviewer #3 (Public review): 

Minor weaknesses are related to a few instances of suboptimal phrasing, and some room for improvement in time course visualization and quantification. These would be easily addressed in a revision. <br /> These findings will undoubtedly have a very significant impact on the rapidly growing but still highly challenging field of primate chemogenetic manipulations. As such, the work represents an invaluable resource for the community.

We thank the reviewer for the positive assessment of our manuscript and for the constructive suggestions. We address each comment in the following point-by-point responses and have revised the manuscript accordingly.

Reviewer #3 (Recommendations for the authors):

(1) Please clarify the reasoning was, behind restricting the analysis in Figure 1 only to 7 monkeys with subcortical AAV injection?

We focused the analysis shown in Figure 1 on 7 monkeys with subcortical AAV injections who received comparative injection volumes. These data were primary part of vector test studies, allowing for repeated PET scans within 150 days post-injection. In contrast, monkeys with cortical injections—including larger volumes—were allocated to behavioral studies and therefore were not scanned as frequently during the early phase. We will clarify this rationale in the Results section.

(2) Figure 1: Not sure if a simple sigmoid is the best model for these, mostly peaking and then descending somewhat, curves. I suggest testing a more complex model, for instance, double logistic function of a type f(t) = a + b/(1+exp(-c*(t-d))) - e/(1+exp(-g*(t-h))), with the first logistic term modeling the rise to peak, and the second term for partial decline and stabilization

We appreciate the reviewer’s thoughtful suggestion to use a double logistic function to better model both the rising and declining phases of the expression curve. In response to this and similar comments from Reviewer #1, we tested the proposed model and found that, while it could capture the peak and subsequent decline, the resulting fit appeared less biologically plausible (See below). Moreover, model comparison using BIC favored the original simple sigmoid model (BIC = 61.1 vs. 62.9 for the simple and double logistic model, respectively). This information has been included in the revised figure legend for clarity.

Given these results, we retained the original simple sigmoid function in the revised manuscript, as it provides a sufficient and interpretable approximation of the early expression trajectory—particularly the peak expression-time estimation, which was the main purpose of this analysis. We have updated the Methods section to clarify our modeling and rationale as follows:

Lines 530, "To model the time course of DREADD expression, we used a single sigmoid function, referencing past in vivo fluorescent measurements (Diester et al., 2011). Curve fitting was performed using least squares minimization. For comparison, a double logistic function was also tested and evaluated using the Bayesian Information Criterion (BIC) to assess model fit."

We also acknowledge that a more detailed understanding of post-peak expression changes will require additional PET measurements, particularly between 60- and 120-days post-injection, across a larger number of animals. We have included this point in the revised Discussion to highlight the need for future work focused on finer-grained modeling of expression decline:

Lines 317, “Although we modeled the time course of DREADD expression using a single sigmoid function, PET data from several monkeys showed a modest decline following the peak. While the sigmoid model captured the early-phase dynamics and offered a reliable estimate of peak timing, additional PET scans—particularly between 60- and 120-days post-injection—will be essential to fully characterize the biological basis of the post-peak expression trajectories.”

Author response image 1.<br />

(3) Figure 2: It seems that the individual curves are for different monkeys, I counted 7 in B and 8 in C, why "across 11 monkeys"? Were there several monkeys both with hM4Diand hM3Dq? Does not look like that from Table 1. Generally, I would suggest associating specific animals from Tables 1 and 2 to the panels in Figures 1 and 2.

Some animals received multiple vector types, leading to more curves than individual subjects. We have revised the figure legends and updated Table 2 to explicitly relate each curve with the specific animal and brain region.

(4) I also propose plotting the average of (interpolated) curves across animals, to convey the main message of the figure more effectively.

We agree that plotting the mean of the interpolated expression curves would help convey the group trend. We added averaged curves to Figure 2BC.

(5) Similarly, in line 155 "We assessed data from 17 monkeys to evaluate ... Monkeys expressing hM4Di were assessed through behavioral testing (N = 11) and alterations in neuronal activity using electrophysiology (N = 2)..." - please explain how 17 is derived from 11, 2, 5 and 1. It is possible to glean from Table 1 that it is the calculation is 11 (including 2 with ephys) + 5 + 1 = 17, but it might appear as a mistake if one does not go deep into Table 1.

We have clarified in both the text and Table 1 that some monkeys (e.g., #201 and #207) underwent both behavioral and electrophysiological assessments, resulting in the overlapping counts. Specifically, the dataset includes 11 monkeys for hM4Di-related behavior testing (two of which underwent electrophysiology testing), 5 monkeys assessed for hM3Dq with FDG-PET, and 1 monkey assessed for hM3Dq with electrophysiology, totaling 19 assessments across 17 monkeys. We have revised the Results section to make this distinction more explicit to avoid confusion, as follows:

Lines 164, "Monkeys expressing hM4Di (N = 11) were assessed through behavioral testing, two of which also underwent electrophysiological assessment. Monkeys expressing hM3Dq (N = 6) were assessed for changes in glucose metabolism via [¹⁸F]FDG-PET (N = 5) or alterations in neuronal activity using electrophysiology (N = 1).”

(6) Line 473: "These stock solutions were then diluted in saline to a final volume of 0.1 ml (2.5% DMSO in saline), achieving a dose of 0.1 ml/kg and 3 mg/kg for DCZ and CNO, respectively." Please clarify: the injection volume was always 0.1 ml? then it is not clear how the dose can be 0.1 ml/kg (for a several kg monkey), and why DCZ and CNO doses are described in ml/kg vs mg/kg?

We thank the reviewer for pointing out this ambiguity. We apologize for the oversight and also acknowledge that we omitted mention of C21, which was used in a small number of cases. To address this, we have revised the “Administration of DREADD agonist” section of the Methods to clearly describe the preparation, the volume, and dosage for each agonist (DCZ, CNO, and C21) as follows:

Lines 493, “Deschloroclozapine (DCZ; HY-42110, MedChemExpress) was the primary agonist used. DCZ was first dissolved in dimethyl sulfoxide (DMSO; FUJIFILM Wako Pure Chemical Corp.) and then diluted in saline to a final volume of 1 mL, with the final DMSO concentration adjusted to 2.5% or less. DCZ was administered intramuscularly at a dose of 0.1 mg/kg for hM4Di activation, and at 1–3 µg/kg for hM3Dq activation. For behavioral testing, DCZ was injected approximately 15 min before the start of the experiment unless otherwise noted. Fresh DCZ solutions were prepared daily.

In a limited number of cases, clozapine-N-oxide (CNO; Toronto Research Chemicals) or Compound 21 (C21; Tocris) was used as an alternative DREADD agonist for some hM4Di experiments. Both compounds were dissolved in DMSO and then diluted in saline to a final volume of 2–3 mL, also maintaining DMSO concentrations below 2.5%. CNO and C21 were administered intravenously at doses of 3 mg/kg and 0.3 mg/kg, respectively.”

(7) Figure 5A: What do regression lines represent? Do they show a simple linear regression (then please report statistics such as R-squared and p-values), or is it related to the linear model described in Table 3 (but then I am not sure how separate DREADDs can be plotted if they are one of the factors)?

We thank the reviewer for the insightful question. In the original version of Figure 5A, the regression lines represented simple linear fits used to illustrate the relationship between viral titer and peak expression levels, based on our initial analysis in which titer appeared to have a significant effect without any notable interaction with other factors (such as DREADD type).

However, after conducting a more detailed analysis that incorporated injection volume as an additional factor and excluded cortical injections and statistical outliers (as suggested by Reviewer #1), viral titer was no longer found to significantly predict peak expression levels. Consequently, we revised the figure to focus on the effect of reporter tag, which remained the most consistent and robust predictor in our model.

In the updated Figure 5, we have removed the relationship between viral titer and expression level with regression lines.

Author response:

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

Reviewer #1 (Recommendations for the authors):

Because many conclusions are drawn from overexpression studies and from a single cell line (HEK293), it is unclear how general these effects are. In particular, one of the main claims put forth in this manuscript is that of specificity, namely, that FZD5/8, and none of the other FZDs, are uniquely involved in this internalization and degradation. While there are examples of similar specificities, many of these examples can be attributed to a particular cellular context. Without demonstrating that this FZD5/8 specificity is observed in multiple cell lines and contexts, this point remains unconvincing and questionable. One way to address this point of criticism is to omit the word "specifically" in the title and soften the language concerning this idea throughout the manuscript.

We appreciate your valuable comments and suggestions. We have removed the word “specifically” from the title and softened the language concerning this idea throughout the manuscript. Moreover, we performed new experiments to show that Wnt3a/5a induces FZD5/8 endocytosis and degradation and that IWP-2 treatment increases the cell surface levels of FZD5/8 in cell lines other than 293A (Figure 1-Figure supplement 1 and Figure 2-Figure supplement 1). These results indicate that Wnt-induced FZD5/8 endocytosis and degradation are not cell specific.

The starting point for these studies is a survey of all 10 FZDs, V5-tagged and overexpressed in HEK293 cells. Here, the authors observed a decline in cell surface levels of only FZD5 and 8 in response to Wnt3a and Wnt5a. As illustrated in the immunoblot (Fig 1B), several FZDs were poorly expressed, including FZD1, 3, 6 and 9, which calls into question that only FZD5 and 8 were affected. Furthermore, total levels of FZD8 don't diminish appreciably, as claimed by the authors, and only FZD5 shows a subtle decline upon WNT treatment. All of these experiments are performed with overexpressed V5-tagged FZD proteins or with endogenously V5-tagged (KI) proteins, and it is possible that overexpression or tagging lead to potentially artifactual observations. Examining the effects of WNTs on FZD protein localization and levels need to be done with endogenously expressed, non-tagged FZDs. In this context, it is somewhat puzzling that the authors don't show such an experiment using the pan- and FZD5/8-specific antibodies, which they use in multiple experiments throughout the manuscript. With these available tools it should be possible to examine FZD levels at the cell surface in response to Wnt3a and Wnt5a, ideally in multiple cell lines.

We appreciate your valuable comments and suggestions. Figure 1B shows the results of the follow-up study shown in Figure 1A. As shown in Figure 1A, we used flow cytometry analysis to detect the cell surface levels of stably expressed FZDs and found that Wnt3a/5a specifically reduced the levels of FZD5/8 on the cell surface, suggesting that Wnt3a/5a induces FZD5/8 endocytosis. As shown in Figure 1B and C, we performed immunoblotting to examine whether Wnt3a/5a-induced FZD5/8 internalization resulted in FZD5/8 degradation. Notably, most FZDs exhibit two bands on immunoblots, as also suggested by other published studies, and the upper bands represent the mature form that is fully glycosylated and presented to the cell surface (see also new Figure 2L), whereas the lower bands represent the immature form. Our results clearly indicated that Wnt3a/5a treatment reduced the levels of the mature forms of both FZD5 and FZD8, although the immunoblotting signals of the mature form of FZD8 (upper bands) were relatively weak. The immunoblotting signals of the other FZDs varied, and some of them (including FZD1, -3, -6 and -9) were relatively weak; however, according to the results in Figure 1A, all of the FZDs were expressed and present on the cell surface.

Commercially available FZD5/8 antibodies, including those used in published studies, cannot detect endogenous FZD5/8 or can only recognize immature FZD5 in our hands, which is why we have to use the CRISPR-CAS9-based KI technique to introduce a V5 tag to FZD5 and FZD7. Notably, in the overexpression experiments, the V5 tag is on the amino terminus, and in the KI experiments, the V5 tag is on the carboxyl terminus of FZDs, which may minimize the potential artificial effects of the V5 tag on the immunoblotting assays.

The monoclonal antibodies used in this study, such as anti-pan-FZD, anti-FZD5/8, and anti-FZD4 antibodies, are neutralizing antibodies that can compete with Wnt ligands to bind to the FZD CRD. These antibodies have been successfully used to detect the surface levels of FZDs via flow cytometry assays. However, as the binding affinity of the Wnt-FZD CRD is comparable to the binding affinity of the antibody-FZD, we were cautious in using these antibodies to detect the cell surface levels of FZDs when the cells were treated with Wnt3a/5a CM, which contains relatively high concentrations of Wnt3a/5a. As shown in Author response image 1, Wnt3a or Wnt5a treatment dramatically reduced the endogenous cell surface level of FZD5/8, as detected by flow cytometry using the anti-FZD5/8 antibody. However, in another experiment, HEK293A cells were first incubated with cold Wnt3a or Wnt5a CM at 4°C to minimize endocytosis and then analyzed via flow cytometry using the anti-FZD5/8 antibody. The results showed that Wnt3a/5a incubation reduced the floe cytometry signals, suggesting that Wnt3a/5a binding to FZD5/8 might interfere with antibody-FZD5/8 binding, although we cannot exclude the possibility that Wnt3a/5a may induce FZD5/8 endocytosis at 4°C (Author response image 1).

Author response image 1.

(A) HEK293A cells were treated with control, Wnt3a or Wnt5a CM for 2 hours at 37°C in a humidified incubator and were analyzed via flow cytometry using the anti-FZD5/8 antibody.

(B) HEK293A cells were incubated with control, Wnt3a or Wnt5a CM for 1 h at 4°C and analyzed by flow cytometry using the anti-FZD5/8 antibody.

Several experiments rely on gene-edited clonal cell lines, including knockouts of FZD5/8, RNF43/ZNRF3, and DVL. Gene knockouts were confirmed by genomic DNA sequencing and, for DVL and FZD5/8, by loss of protein expression. While these KO lines are powerful tools to study gene function, there is a concern for clonal variability. Each cell line may have acquired additional changes as a result of gene editing. In addition, there may be compensatory changes in gene expression as a consequence of the loss of certain genes. For example, expression of other FZDs may increase in FZD5/8 DKO cells. To address this critique, the authors should show that re-expression of the knocked-out genes rescues the observed effect. This is done in some instances (Fig 5E, G, H) but not in other instances, such as with the DVL TKO (Fig. 3). Since the authors assert that DVL is important for FZD internalization in the absence of WNT, but not for FZD internalization in the presence of WNT, this particular rescue experiment is important. This is a potentially important finding and it should be confirmed by re-expression of DVL in the TKO line. As an alternative, conditional knockdown using Tet-inducible shRNA expression could address concerns for clonal variability.

We appreciate your valuable comments and suggestions. We re-expressed DVL2 in DVLTKO cells stably expressing V5-linker-FZD5 or V5-linker-FZD7. As shown in Figure 3G-K, re-expression of DVL2 rescued the decreased Wnt-independent endocytosis of FZD5 and FZD7 caused by DVL1/2/3 knockout.

Given the significant differences in signaling activity by Wnt3a and Wnt5a, it is somewhat surprising that all experiments shown in this manuscript do not identify distinguishing features between Wnt3a and Wnt5a. In addition, it is unclear why the authors switch between Wnt3a and Wnt5a. For example, Figures 1C, 3G-J, 4C-D only use Wnt5a. In contrast, Figures 6E and H use Wnt3a, most likely because b-catenin stabilization is examined, an effect generally not observed with Wnt5a. The choice of which Wnt is examined/used appears to be somewhat arbitrary and the authors never provide any explanations for these choices. In the end, this type of inconsistency becomes puzzling when the authors present, quite convincingly, in Figure 7, that both Wnt3a and 5a promote an interaction between FZD5/8 and RNF43 through proximity biotin labeling.

Although Wnt3a and Wnt5a are significantly different in triggering intracellular signaling pathways, both bind FZD5/8 and induce FZD5/8 endocytosis and degradation similarly. When FZD5 is stably overexpressed, Wnt5a has slightly stronger effects on inducing FZD5 endocytosis and degradation, possibly because the Wnt5a concentration may be higher than the Wnt3a concentration in our CM, which is why we used Wnt5a CM in some experiments when V5-FZD5 was overexpressed. In the revised manuscript, we used both Wnt3a and Wnt5a CM in the experiments as you suggested, as shown in Figure 1C, 3G-K and Figure 4-Figure supplement 1.

Minor Points:

Figure 3G and I: it is curious that individual cells are shown in the "0 h" samples, while the "Con 1 h" and "Wnt5a 1 h" show multiple cells with several making direct contact with each other. This is notable because the V5 staining at sites of cell-cell contact are quite distinct and variable between control and Wnt5a-treated and WT versus DVL TKO cells. Also, sub-cellular localization of FZD5 (V5 tag) puncta is quite distinct between Con and Wnt5a: puncta in Wnt5a-treated cells appear to be more plasma membrane proximal than in Con cells. These points may be easy to address by showing images of cells that are more similar with respect to cell number and density for each condition.

Thank you for your suggestions. We repeated these experiments and added Wnt3a treatment and adjusted the cell density. Images including an individual cell were selected for presentation.

Figure 5E: the following statement is confusing/misleading: "Furthermore, reintroducing ZNRF3 or RNF43 into ZRDKO cells efficiently restored the increase in cytosolic β-catenin levels, whereas the expression of RNF130 or RNF150, two structurally similar transmembrane E3 ubiquitin ligases, did not (Fig. 5E)." First, reintroduction of ZNRF3 or RNF43 restores cytosolic b-catenin levels; it does not restore the increase in b-catenin. Second, the claim that RNF130 fails to have this effect is not substantiated since it is barely expressed.

Thank you for your suggestions and comments. We reorganized the language to make the statement clearer. Notably, the expression level of RNF130 was relatively low compared with that of other E3 ligases, but RNF130 was expressed (Figure 5E darker exposure) and could reduce the cell surface levels of FZDs, as shown in Figure 5G.

Reviewer #2 (Recommendations for the authors):

(1) Given their results the authors conclude that upregulation of Frizzled on the plasma membrane is not sufficient to explain the stabilization of beta-catenin seen in the ZNRF3/RNF43 mutant cells. This interpretation is sound, and they suggest in the discussion that ZNRF3/RNF43-mediated ubiquitination could serve as a sorting signal to sort endocytosed FZD to lysosomes for degradation and that absence or inhibition of this process would promote FZD recycling. This should be relatively easy to test using surface biotinylation experiments and would considerably strengthen the manuscript.

Thank you for your valuable suggestions and comments. We performed cell surface biotinylation experiments in HEK293A FZD5KI cells, as shown in Figure 2L. The results indicated that Wnt3a or Wnt5a treatment induced the degradation of FZD5 on the cell surface, which was antagonized by cotreatment with RSPO1. We did not perform a more detailed endocytosis/recycling biotinylation experiment that requires complex reversible biotinylation and multiple washing steps because HEK293A cells are fragile in culture and not easy to handle. Furthermore, the results shown in Figure 4 indicate that knockout of ZNRF3/RNF43 or RSPO1 significantly blocked the degradation of internalized FZD5 and reduced the colocalization of internalized FZD5 with lysosomal markers, suggesting that Wnt3a/5a induced lysosomal degradation of FZD5 in the presence of ZNRF3/RNF43 and that the internalized FZD5 was most likely recycled back to the cell surface when ZNRF3/RNF43 was knocked out or inhibited by RSPO1.

(2) The authors show that the FZD5 CRD domain is required for endocytosis since a mutant FZD5 protein in which the CRD is removed does not undergo endocytosis. This is perhaps not surprising since this is the site of Wnt binding, but the authors show that a chimeric FZD5CRD-FZD4 receptor can confer Wnt-dependent endocytosis to an otherwise endocytosis incompetent FZD4 protein. Since the linker region between the CRD and the first TM differs between FZD5 and FZD4, it would be interesting to understand whether the CRD specifically or the overall arrangement (such as the spacing) is the most important determinant.

Our results in Figure 1D-H clearly show that the CRD of FZD5 specifically is both necessary and sufficient for Wnt3a/5a-induced FZD5 endocytosis, as replacing the CRD alone in FZD5 with the CRD from either FZD4 or FZD7 completely abolished Wnt-induced endocytosis, whereas replacing the CRD alone in FZD4 or FZD7 with the FZD5 CRD alone could confer Wnt-induced endocytosis.

(3) I find it surprising that only FZD5 and FZD8 appear to undergo endocytosis or be stabilized at the cell surface upon ZNRF3/RNF43 knockout. Is this consistent with previous literature? Is that a cell-specific feature? These findings should be tested in a different cell line, with possibly different relative levels of ZNRF3 and RNF43 expression.

Thank you for your comments and suggestions. Our finding that ZNRF3/RNF43 specifically regulates FZD5/8 degradation is consistent with recent published studies in which FZD5 is required for the survival of RNF43-mutant PDAC or colorectal cancer cells (Nature Medicine, 2017, PMID: 27869803) and FZD5 is required for the maintenance of intestinal stem cells (Developmental Cell, 2024, PMID: 39579768 and 39579769), and in both cases, FZDs other than FZD5/8 are also expressed but not sufficient to compensate for the function of FZD5. The mechanism by which Wnt3a/5a specifically induces FZD5/8 endocytosis and degradation is currently unknown and needs to be explored in the future. We speculate that Wnt binding to FZD5/8 may recruit another protein on the cell surface to specifically facilitate FZD5/8 endocytosis. On the other hand, we cannot exclude the possibility that Wnts other than Wnt3a/5a may induce the endocytosis and degradation of FZDs other than FZD5/8 since there are 19 Wnts and 10 FZDs in humans. Notably, several previous studies have suggested that ZNRF3/RNF43 may regulate the endocytosis and degradation of all FZDs without selectivity (such as Nature, 2012, PMID: 22575959; Nature, 2012, PMID: 22895187; Mol Cell, 2015, PMID: 25891077). However, their conclusions were drawn mostly on the basis of overexpression studies. According to the results shown in Figure 5E-H, overexpressing a membrane-tethered E3 ligase (such as ZNRF3, RNF43, RNF130, or RNF150) may nonspecifically degrade FZD proteins on the cell surface.

Furthermore, in the revised manuscript, we showed that Wnt3a/5a induced FZD5/8 endocytosis and degradation in multiple cell lines, including Huh7, U2OS, MCF7, and 769P cells (Figure 1-Figure supplement 1 and Figure 2-Figure supplement 1), suggesting that these phenomena are not specific to 293A cells.

(4) If FZD7 is not a substrate of ZNRF3/RNF43 and therefore is not ubiquitinated and degraded, how do the authors reconcile that its overexpression does not lead to elevated cytosolic beta-catenin levels in Figure 5B?

We are currently not sure of the mechanism underlying this result. Considering that most FZDs are expressed in 293A cells, we do not know how much of the mature form of overexpressed FZD7 was presented to the plasma membrane.

(5) For Figure 5B, it would be interesting if the authors could evaluate whether overexpression of FZD5 in the ZNRF3/RNF43 double knockout lines would synergize and lead to further increase in cytosolic beta-catenin levels. As control if the substrate selectivity is clear FZD7 overexpression in that line should not do anything.

Thank you for your suggestion. We performed these experiments as suggested, and the results indicated that overexpressing FZD5 further increased cytosolic beta-catenin levels in ZRDKO cells, whereas FZD7 had no effect (Figure 6D).

(6) In Figure 6G, the authors need to show cytosolic levels of beta-catenin in the absence of Wnt in all cases.

We did not add Wnt CM in this experiment. RSPO1 activity, which relies on endogenous Wnt, has been well documented in previous studies.

(7) Since the authors show that DVL is not involved in the Wnt and ZRNF3-dependent endocytosis they should repeat the proximity biotinylation experiment in figure 7 in the DVL triple KO cells. This is an important experiment since previous studies showed that DVL was required for the ZRNF3/RNF43-mediated ubiqtuonation of FZD.

Thank you for your valuable suggestions. As you suggested, we performed a proximity biotinylation experiment in DVL TKO cells, and the results showed that Wnt3a/5a could still induce the interaction of FZD5 and RNF43 in DVLTKO cells (Figure 7-figure supplement 1), suggesting that the Wnt-induced FZD5‒RNF43 interaction is DVL independent.

Author Response

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

eLife assessment

This important study elucidates the molecular divergence of caspase 3 and 7 in the vertebrate lineage. Convincing biochemical and mutational data provide evidence that in humans, caspase 7 has lost the ability to cleave gasdermin E due to changes in a key residue, S234. However, the physiological relevance of the findings is incomplete and requires further experimental work.

Public Reviews:

Reviewer #1 (Public Review):

Summary

In this study, Xu et al. provide insights into the substrate divergence of CASP3 and CASP7 for GSDME cleavage and activation during vertebrate evolution vertebrates. Using biochemical assays, domain swapping, site-directed mutagenesis, and bioinformatics tools, the authors demonstrate that the human GSDME C-terminal region and the S234 residue of human CASP7 are the key determinants that impede the cleavage of human GSDME by human CASP7.

Strengths

The authors made an important contribution to the field by demonstrating how human CASP7 has functionally diverged to lose the ability to cleave GSDME and showing that reverse-mutations in CASP7 can restore GSDME cleavage. The use of multiple methods to support their conclusions strengthens the authors' findings. The unbiased mutagenesis screen performed to identify S234 in huCASP7 as the determinant of its GSDME cleavability is also a strength.

Weaknesses

While the authors utilized an in-depth experimental setup to understand the CASP7-mediated GSDME cleavage across evolution, the physiological relevance of their findings are not assessed in detail. Additional methodology information should also be provided.

Specific recommendations for the authors

(1) The authors should expand their evaluation of the physiological relevance by assessing GSDME cleavage by the human CASP7 S234N mutant in response to triggers such as etoposide or VSV, which are known to induce CASP3 to cleave GSDME (PMID: 28045099). The authors could also test whether the human CASP7 S234N mutation affects substrate preference beyond human GSDME by testing cleavage of mouse GSDME and other CASP3 and CASP7 substrates in this mutant.

(1) The physiological relevance was discussed in the revised manuscript (lines 328-340). Our study revealed the molecular mechanism underlying the divergence of CASP3- and CASP7-mediated GSDME activation in vertebrate. One of the physiological consequences is that in humans, CASP7 no longer directly participates in GSDME-mediated cell death, which enables CASP7 to be engaged in other cellular processes. Another physiological consequence is that GSDME activation is limited to CASP3 cleavage, thus restricting GSDME activity to situations more specific, such as that inducing CASP3 activation. The divergence and specialization of the physiological functions of different CASPs are consistent with and possibly conducive to the development of refined regulations of the sophisticated human GSDM pathways, which are executed by multiple GSDM members (A , B, C, D, and E), rather than by GSDME solely in teleost, such as Takifugu. More physiological consequences of CASP3/7 divergence in GSDME activation need to be explored in future studies.

With respect to the reviewer’s suggestion of assessing GSDME cleavage by the human CASP7 S234N mutant in response to triggers such as etoposide or VSV: (i) CASP7 S234N is a creation of our study, not a natural human product, hence its response to CASP7 triggers cannot happen under normal physiological conditions except in the case of application, such as medical application, which is not the aim of our study. (ii) CASP3/7 activators (such as raptinal) induced robust activation of the endogenous CASP3 (Heimer et al., Cell Death Dis. 2019;10:556) and CASP7 (Author response image 1, below) in human cells. Since CASP3 is the natural activator of GSDME, the presence of the triggers inevitably activates GSDME via CASP3. Hence, under this condition, it will be difficult to examine the effect of CASP7 S234N.

Author response image 1.

HsCASP7 activation by raptinal. HEK293T cells were transfected with the empty vector (-), or the vector expressing HsCASP7 or HsCASP7-S234N for 24 h. The cells were then treated with or without (control) 5 μM raptinal for 4 h. The cells were lysed, and the lysates were blotted with anti-CASP7 antibody.

(2) As suggested by the reviewer, the cleavage of other CASP7 substrates, i.e., poly (ADP-ribose) polymerase 1 (PARP1) and gelsolin, by HsCASP7 and S234N mutant was determined. The results showed that HsCASP7 and HsCASP7-S234N exhibited similar cleavage capacities. Figure 5-figure supplement 1 and lines 212-214.

(2) It would also be interesting to examine the GSDME structure in different species to gain insight into the nature of mouse GSDME, which cannot be cleaved by either mouse or human CASP7.

Because the three-dimensional structure of GSDME is not solved, we are unable to explore the structural mechanism underlying the GSDME cleavage by caspase. Since our results showed that the C-terminal domain was essential for caspase-mediated cleavage of GSDME, it is likely that the C-terminal domain of mouse GSDME may possess some specific features that render it to resist mouse and human CASP7.

(3) The evolutionary analysis does not explain why mammalian CASP7 evolved independently to acquire an amino acid change (N234 to S234) in the substrate-binding motif. Since it is difficult to experimentally identify why a functional divergence occurs, it would be beneficial for the authors to speculate on how CASP7 may have acquired functional divergence in mammals; potentially this occurred because of functional redundancies in cell death pathways, for example.

According to the reviewer’s suggestion, a speculation was added. Lines 328-340.

(4) For the recombinant proteins produced for these analyses, it would be helpful to know whether size-exclusion chromatography was used to purify these proteins and whether these purified proteins are soluble. Additionally, the SDS-PAGE in Figure S1B and C show multiple bands for recombinant mutants of TrCASP7 and HsCASP7. Performing protein ID to confirm that the detected bands belong to the respective proteins would be beneficial.

The recombinant proteins in this study are soluble and purified by Ni-NTA affinity chromatography. Size-exclusion chromatography was not used in protein purification.

For the SDS-PAGE in Figure 4-figure supplement 1B and C (Figure S1B and C in the previous submission), the multiple bands are most likely due to the activation cleavage of the TrCASP7 and HsCASP7 variants, which can result in multiple bands, including p10 and p20. According to the reviewer’s suggestion, the cleaved p10 was verified by immunoblotting. Figure 4-figure supplement 1B and C.

(5) For Figures 3C and 4A, it would be helpful to mention what parameters or PDB files were used to attribute these secondary structural features to the proteins. In particular, in Figure 3C, residues 261-266 are displayed as a β-strand; however, the well-known α-model represents this region as a loop. Providing the parameters used for these callouts could explain this difference.

For Figure 3C, in the revised manuscript, we used the structure of mouse GSDMA3 (PDB: 5b5r) for the structural analysis of HsGSDME. As indicated by the reviewer, the region of 261-266 is a loop. The description was revised in lines 172 and 174, Figure 3C and Figure 3C legend.

For Figure 4A, the alignment of CASP7 was constructed by using Esprit (https://espript.ibcp.fr/ESPript/cgi-bin/ESPript.cgi) with human CASP7 (PDB:1k86) as the template. The description was revised in the Figure legend.

(6) Were divergent sequences selected for the sequence alignment analyses (particularly in Figure 6A)? The selection of sequences can directly influence the outcome of the amino acid residues in each position, and using diverse sequences can reduce the impact of the number of sequences on the LOGO in each phylogenetic group.

In Figure 6A, the sequences were selected without bias. For Mammalia, 45 CASP3 and 43 CASP7 were selected; for Aves, 41 CASP3 and 52 CASP7 were selected; for Reptilia, 31CASP3 and 39 CASP7 were selected; for Amphibia, 11 CASP3 and 12 CASP7 were selected; for Osteichthyes, 40 CASP3 and 43 CASP7 were selected. The sequence information was shown in Table 1 and Table 2.

(7) For clarity, it would help if the authors provided additional rationale for the selection of residues for mutagenesis, such as selecting Q276, D278, and H283 as exosite residues, when the CASP7 PDB structures (4jr2, 3ibf, and 1k86) suggest that these residues are enriched with loop elements rather than the β sheets expected to facilitate substrate recognition in exosites for caspases (PMID: 32109412). It is possible that the inability to form β-sheets around these positions might indicate the absence of an exosite in CASP7, which further supports the functional effect of the exosite mutations performed.

According to the suggestion, the rationale for the selection of residues for mutagenesis was added (lines 216-222). Unlike the exosite in HsCASP1/4, which is located in a β sheet, the Q276, D278, and H283 of HsCASP7 are located in a loop region (Figure 5-figure supplement 2), which may explain the mutation results and the absence of an exosite in HsCASP7 as suggested by the reviewer.

Reviewer #2 (Public Review):

The authors wanted to address the differential processing of GSDME by caspase 3 and 7, finding that while in humans GSDME is only processed by CASP3, Takifugu GSDME, and other mammalian can be processed by CASP3 and 7. This is due to a change in a residue in the human CAPS7 active site that abrogates GSDME cleavage. This phenomenon is present in humans and other primates, but not in other mammals such as cats or rodents. This study sheds light on the evolutionary changes inside CASP7, using sequences from different species. Although the study is somehow interesting and elegantly provides strong evidence of this observation, it lacks the physiological relevance of this finding, i.e. on human side, mouse side, and fish what are the consequences of CASP3/7 vs CASP3 cleavage of GSDME.

Our study revealed the molecular mechanism underlying the divergence of CASP3- and CASP7-mediated GSDME activation in vertebrate. One of the physiological consequences is that in humans, CASP7 no longer directly participates in GSDME-mediated cell death, which enables CASP7 to be engaged in other cellular processes. Another physiological consequence is that GSDME activation is limited to CASP3 cleavage, thus restricting GSDME activity to situations more specific, such as that inducing CASP3 activation. The divergence and specialization of the physiological functions of different CASPs are consistent with and possibly conducive to the development of refined regulations of the sophisticated human GSDM pathways, which are executed by multiple GSDM members (A , B, C, D, and E), rather than by GSDME solely in teleost, such as Takifugu. More physiological consequences of CASP3/7 divergence in GSDME activation need to be explored in future studies. Lines 328-340.

Fish also present a duplication of GSDME gene and Takifugu present GSDMEa and GSDMEb. It is not clear in the whole study if when referring to TrGSDME is the a or b. This should be stated in the text and discussed in the differential function of both GSDME in fish physiology (i.e. PMIDs: 34252476, 32111733 or 36685536).

The TrGSDME used in this study belongs to the GSDMEa lineage of teleost GSDME. The relevant information was added. Figure 1-figure supplement 1 and lines 119, 271, 274-276, 287 and 288.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) For the chimeric and truncated constructs, such as HsNT-TrCT, TrNT-HsCT, Hsp20-Trp10, Trp20-Hsp10, etc., the authors should provide a table denoting which amino acids were taken from each protein to create the fusion or truncation.

According to the reviewer’s suggestion, the information of the truncate/chimeric proteins was provided in Table 4.

(2) Both reviewers agree that functional physiological experiments are needed to increase the significance of the work. Specifically, the physiological relevance of these findings can be assessed by using western blotting to monitor GSDME cleavage by the human CASP7 S234N mutant compared with wild type CASP7 in response to triggers such as etoposide or VSV, which are known to induce CASP3 to cleave GSDME (PMID: 28045099).

Additionally, the authors can assess cell death in HEK293 cells, HEK293 cells transfected with TrGSDME, HEK293 cells expressing TrCASP3/7 plus TrGSDME, and TrCASP3/7 plus the D255R/D258A mutant. These cells can be stimulated, and pyroptosis can be assessed by using ELISA to measure the release of the cytoplasmic enzyme LDH as well as IL-1β and IL-18, and the percentage of cell death (PI+ positive cells) may also be assessed.

(1) With respect to the physiological relevance, please see the above reply to Reviewer 1’s comment of “Specific recommendations for the authors, 1”.

(2) As shown in our results (Fig. 2), co-expression of TrCASP3/7 and TrGSDME in HEK293T cells induced robust cell death without the need of any stimulation, as evidenced by LDH release and TrGSDME cleavage. In the revised manuscript, similar experiments were performed as suggested, and cell death was assessed by Sytox Green staining (Figure 2-figure supplement 3A and B) and immunoblot to detect the cleavage of both wild type and mutant TrGSDME (Figure 2-figure supplement 3C). The results confirmed the results of Figure 2.

Reviewer #2 (Recommendations For The Authors):

Abstract:

Although the authors try to summarize the principal results of this study, please rewrite the abstract section to make it easier to follow and to empathise the implications of their results.

We have modified the Abstract as suggested by the reviewer.

Introduction:

The authors do not mention anything about the implication of the inflammasome activation to get pyroptosis by GSDM cleave by inflammatory caspases. Please consider including this in the introduction section as they do in the discussion section.

The introduction was modified according to the reviewer’s suggestion. Lines 58-61.

From the results section the authors name the human GSDM as HsGSDM and the human CASP as HsCASP, maybe the author could use the same nomenclature in the introduction section. The same for the fish GSDM (Tr) and CASP.

According to the reviewer’s suggestion, the same nomenclature was used in the introduction.

Line 39. Remove the word necrotic.

“necrotic” was removed .

Line 42. Change channels by pores. In the manuscript, change channels by pores overall.

“channels” was replaced by “pores”.

Line 42: Include that: by these pores can be released the proinflammatory cytokines and if these pores are not solved then pyroptosis occurs. Please rephrase this statement.

According to the reviewer's suggestion, the sentence was rephrased. Lines 46-48.

Line 45. GSDMF is not an approved gene name, its official nomenclature is PJVK (Uniprot Q0ZLH3). Please use PJVK instead GSDMF.

GSDMF was changed to PJVK.

Line 103: Can the authors explain better the molecular determinant?

The sentence was revised, line 109.

Results:

Line 110: Reference for this statement. The reference for this statement was added in line 116.

Figure 1A, B: Concentration or units used of HsCASP?

The unit (1 U) of HsCASPs was added to the figure legend (line 661).

Line 113: Add Hs or Tr after CASP would be helpful to follow the story.

“CASP” was changed to “HsCASP”.

Fig 1D: Why the authors do not use the DMPD tetrapeptide (HsGSDME CASP3 cut site) in this assay? Comparing with the data obtained in Fig 3B the TrCASP3 activity is going to be very closer to that obtained for VEID o VDQQD in the CASP3 panel.

The purpose of Figure 1D was to determine the cleavage preference of TrCASPs. For this purpose, a series of commercially available CASP substrates were used, including DEVD, which is commonly used as a testing substrate for CASP3. Figure 3B was to compare the cleavage of HsCASP3/7 and TrCASP3/7 specifically against the motifs from TrGSDME (DAVD) and HsGSDME (DMPD).

Figure 1D and Figure 3B are different experiments and were performed under different conditions. In Figure 1D, CASP3 was incubated with the commercial substrates at 37 ℃ for 2 h, while in Figure 3B, CASP3/7 were incubated with non-commercial DAVD (motif from TrGSDME) and DMPD (motif from HsGSDME) at 37 ℃ for 30 min. More experimental details were added to Materials and Methods, lines 443 and 447.

Fig 1H: What is the concentration used of the inhibitors?

The concentration (20 μM) was added to the figure legend (line 669).

Does the Hs CASP3/7 fail to cleave the TrGSDME mutants (D255R and D258A)? the authors do not show this result so they cannot assume that HsCASP3/7 cleave that sequence (although this is to be expected).

The result of HsCASP3/7 cleavage of the TrGSDME mutants was added as Figure 1-figure supplement 2 and described in Results, line 133.

Line 132-133: Can the author specify where is placed the mCherry tag? In the N terminal or C terminal portion of the different engineered proteins?

The mCherry tag is attached to the C-terminus. Figure 2 legend (line 676).

Fig 2A: Although is quite clear, a column histogram showing the quantification is going to be helpful.

The expression of TrGSDME-FL, -NT and -CT was determined by Western blot, and the result was added as Figure 2-figure supplement 1.

Fig 2A, B, C: After how many hours of expression are the pictures taken? Can the authors show a Western blot showing that the expression of the different constructions is similar?

The time was added to Figure 2 legend and Materials and Methods (line 466). The expression of TrGSDME-FL, -NT and -CT was determined by Western blot, and the result was added as Figure 2-figure supplement 1.

Fig 2C: Another helpful assay can be to measure the YO-PRO or another small dye internalization, to complete the LDH data.

According the reviewer’s suggestion, in addition to LDH release, Sytox Green was also used to detect cell death. The result was added as Figure 2-figure supplement 2 and described in Results, line 146.

Fig 2C: In the figure y axe change LHD by LDH.

The word was corrected.

Fig 2D: Change HKE293T by HEK293T in the caption.

The word was corrected.

Fig 2G: Please add the concentration used with the two plasmids co-transfection. A Western blot showing CASP3/7 expression vs TrGSDME is missing. Is that assay after 24h? please specify better the methodology.

The concentration of plasmid used in co-transfection and the time post transfection were added to the Materials and Methods (lines 422 and 424). In addition, the expression of CASP3/7 was added to Figure 2I.

Fig 2 J, K: Change HKE293T by HEK293T in the figure caption. The concentration of the caspase inhibitors is missing. Depending on the concentration used, these inhibitors used could provoke toxicity on the cells by themselves.

The word was corrected in the figure caption. The inhibitor concentration (10 μM) was added to the figure legend (line 690).

Line 151: TrCASP3/7 instead of CASP3/7

CASP3/7 was changed to TrCASP3/7.

Fig 3A, 3B: Please add the units used of the HsCASP

The unit was added to the figure legends (lines 697).

Fig 3A: Can the authors add the SDS-PAGE to see the Nt terminal portion as has been done in Fig 1A? Maybe in a supplementary figure.

The SDS-PAGE was added as Figure 3-figure supplement 1.

Fig 3B: If the authors could add some data about the caspase activity using any other CASP such as CASP2, CASP1 to compare the activity data with CASP3 and CASP7 would be helpful.

The proteolytic activity of TrCASP1 was provided as Figure 3-figure supplement 2.

Fig 3C: To state this (Line 160), the authors should use another prediction software to reach a consensus with the sequences of the first analysis. In fact, what happens when GSDME is modelled 3-dimensionally by comparing it to crystalized structures such as mouse GSDMA? If the authors add an arrow indicating where the Nt terminal portion ends and where Ct portion begins would make the figure clearer.

According to the suggestions of both reviewers, in the revised manuscript, we used mouse GSDMA3 (PDB: 5b5r) for the structural analysis of HsGSDME, which showed that the 261-266 region of HsGSDME was a loop. As a result, Figure 3C was revised. Relevant change in Results: lines 172 and 174.

As suggested by the reviewer, we modelled the three-dimensional structure of HsGSDME by using SWISS-MODEL with mouse GSDMA3 as the template (Author response image 2, below).

Author response image 2.

The three-dimensional structure model of HsGSDME. (A) The structure of HsGSDME was modeled by using mouse GSDMA3 (MmGSDMA3) as the template. The N-terminal domain (1-246 aa) and the C-terminal domain (279-468 aa) of HsGSDME are shown in red and blue, respectively. (B) The superposed structure of HsGSDME (cyan) and MmGSDMA3 (purple).

Fig 3F: if this is an immunoblotting why NT can be seen? In other Western blots only the CT is detected, why? The use of the TrGSDME mouse polyclonal needs more details (is a purify Ab, was produced for this study, what are the dilution used...)

Since the anti-TrGSDME antibody was generated using the full-length TrGSDME, it reacted with both the N-terminal and the C-terminal fragments of TrGSDME in Figure 3F. In Figure 3G, the GSDME chimera contained only TrGSDME-CT, so only the CT fragment was detected by anti-TrGSDME antibody. More information on antibody preparation and immunoblot was added to “Materials and Methods” (lines 390 and 391).

Fig 4B: Can the authors show in which amino acid the p20 finish for each CASP? (Similarly, as they have done in panel 3E)

Fig 4B was revised as suggested.

Fig 5F: With 4 units of WT CASP7 the authors show a HsGSDME Ct in the same proportion than when the S234N mutant is used (at lower concentrations). How do the authors explain this?

The result showed that the cleavage by 4U of HsCASP7 was comparable to the cleavage by 0.25U of HsCASP7-S234N, indicating that S234 mutation increased the cleavage ability of HsCASP7 by 16 folds.

Line 203: Can the authors show an alignment between this region of casp1/4 and 7? Maybe in supplementary figures.

As reported by Wang et. al (PMID: 32109412), the βIII/βIII’ sheet of CASP1/4 forms the exosite critical for GSDMD recognition. The structural comparison among HsCASP1/4/7 and the sequence alignment of HsCASP1/4 βIII/βIII’ region with its corresponding region in HsCASP7 were added as Figure 5-figure supplement 2.

Line 205: A mutation including S234N with the exosite mutations (S234+Q276W+D278E+H283S) is required to support this statement.

The sentence of “suggesting that, unlike human GSDMD, HsGSDME cleavage by CASPs probably did not involve exosite interaction” was deleted in the revised manuscript.

Fig 5I, 5J: which is the amount of HsGSDME and TrGSDME? I would place these figures in supplementary material.

The protein expression of TrGSDME/HsGSDME was shown in the figure. Fig 5I and 5J were moved to Figure 5-figure supplement 3.

Line 218: I would specify that this importance is in HUMAN CASP7 to cleavage Human GSDME.

“CASP7” and “GSDME” were changed to “HsCASP7” and “HsGSDME”, respectively.

Fig 6C: 4 units is the amount of S234N mutant needed to see an optimal HsGSDME cleavage in Fig 5F.

In Figure 6C, the cleavage efficacy of HsCASP3-N208S was apparently decreased compared to that of HsCASP3, and 4U of HsCASP3-N208S was roughly equivalent to 1U of HsCASP3 in cleavage efficacy. In Figure 5F, cleavage by 4U of HsCASP7 was comparable to the cleavage by 0.25U of HsCASP7-S234N. Together, these results confirmed the critical role of S234/N208 in HsCASP3/7 cleavage of HsGSDM.

Fig 6I: Could be the fact that the mouse GSDME has a longer Ct than human GSDME affect the interaction with CASP7? Less accessible to the cut site? Needs a positive control of mouse GSDME with mouse Caspase 3.

Although mouse GSDME (MmGSDME) (512 aa) is larger than HsGSDME (496 aa), the length of the C-terminal domain of MmGSDME (186 aa) is comparable to that of HsGSDME (190 aa).

Author response image 3.

Conserved domain analysis of mouse (upper) and human (lower) GSDME.

As suggested by the reviewer, the cleavage of MmGSDME by mouse caspase-3 (MmCASP3) was added as Figure 6-figure supplement 2 and described in Results, lines 258.

Material and Methods:

-Overall, concentrations or amounts used in this study regarding the active enzyme or plasmids used are missing and need to be added.

The missing concentrations of the enzymes and plasmids were added in Material and Methods (lines 421, 453, 457, and 470) or figure legends (Figure 1 and 3).

-It would be helpful if the authors label in the immunoblotting panels what is the GSDME that they are using. (Hs GSDME FL...).

As suggested, the labels were added to Figures 1A ,1B, and 3.

-Add the units of enzyme used.

The units of enzyme were added to figure legends (Figure 1A, 3A, 3D, and 3F) or Material and Methods (lines 453 and 457).

The GSDME sequence obtained for Takifugu after amplification of the RNA extracted should be shown and specified (GSDMEa or GSDMEb). From which tissue was the RNA extracted?

The details were added to Materials and Methods (lines 398 and 402).

Author Response

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

Reviewer #1 (Public Review):

In this study, the authors attempt to describe alterations in gene expression, protein expression, and protein phosphorylation as a consequence of chronic adenylyl cyclase 8 overexpression in a mouse model. This model is claimed to have resilience to cardiac stress.

Major strengths of the study include 1) the large dataset generated which will have utility for further scientific inquiry for the authors and others in the field, 2) the innovative approach of using cross-analyses linking transcriptomic data to proteomic and phosphoproteomic data. One weakness is the lack of a focused question and clear relevance to human disease. These are all critical biological pathways that the authors are studying and essentially, they have compiled a database that could be surveyed to generate and test future hypotheses.

Thank you for your efforts to review our manuscript, we are delighted to learn that you found our approach to link transcriptomic, proteomic and phosphoproteome data in our analysis to be innovative. Your comment that we have not focused on a question with clear relevance to human disease is “right on point!”

During chronic pathophysiologic states e.g., chronic heart failure (CHF) in humans, AC/cAMP/PKA/Ca2+ signaling increases progressively the degree of heart failure progresses, leading to cardiac inflammation, mediated in part, by cyclic-AMP- induced up- regulation of renin-angiotensin system (RAS) signaling. Standard therapies for CHF include β-adrenoreceptor blockers and RAS inhibitors, which although effective, are suboptimal in amelioration of heart failure progression. One strategy to devise novel and better therapies for heart failure, would be to uncover the full spectrum of concentric cardio- protective adaptations that becomes activated in response to severe, chronic AC/cAMP/PKA/Ca2+ -induced cardiac stress.

We employed unbiased omics analyses, in our prior study (https://elifesciences.org/articles/80949v1) of the mouse harboring cardiac specific overexpression of adenylyl cyclase type 8 (TGAC8), and identified more than 2,000 transcripts and proteins, comprising a broad array of biological processes across multiple cellular compartments, that differed in TGAC8 left ventricle compared to WT. These bioinformatic analyses revealed that marked overexpression of AC8 engages complex, concentric adaptation "circuity" that has evolved in mammalian cells to confer resilience to stressors that threaten health or life. The main human disease category identified in these analyses was Organismal Injury and Abnormalities, suggesting that defenses against stress were activated as would be expected, in response to cardiac stress. Specific concentric signaling pathways that were enriched and activated within the TGAC8 protection circuitry included cell survival initiation, protection from apoptosis, proliferation, prevention of cardiac-myocyte hypertrophy, increased protein synthesis and quality control, increased inflammatory and immune responses, facilitation of tissue damage repair and regeneration and increased aerobic energetics. These TGAC8 stress response circuits resemble many adaptive mechanisms that occur in response to the stress of disease states and may be of biological significance to allow for proper healing in disease states such as myocardial infarction or failure of the heart. The main human cardiac diseases identified in bioinformatic analyses were multiple types cardiomyopathies, again suggesting that mechanisms that confer resilience to the stress of chronic increased AC-PKA-Ca2+ signaling are activated in the absence of heart failure in the super-performing TGAC8 heart at 3-months of age.

In the present study, we performed a comprehensive in silico analysis of transcription, translation, and post-translational patterns, seeking to discover whether the coordinated transcriptome and proteome regulation of the adaptive protective circuitry within the AC8 heart that is common to many types of cardiac disease states identified in our previous study (https://elifesciences.org/articles/80949v1) extends to the phosphoproteome.

Reviewer #2 (Public Review):

In this study, the investigators describe an unbiased phosphoproteomic analysis of cardiac-specific overexpression of adenylyl cyclase type 8 (TGAC8) mice that was then integrated with transcriptomic and proteomic data. The phosphoproteomic analysis was performed using tandem mass tag-labeling mass spectrometry of left ventricular (LV) tissue in TGAC8 and wild-type mice. The initial principal component analysis showed differences between the TGAC8 and WT groups. The integrated analysis demonstrated that many stress-response, immune, and metabolic signaling pathways were activated at transcriptional, translational, and/or post-translational levels.

The authors are to be commended for a well-conducted study with quality control steps described for the various analyses. The rationale for following up on prior transcriptomic and proteomic analyses is described. The analysis appears thorough and well-integrated with the group's prior work. Confirmational data using Western blot is provided to support their conclusions. Their findings have the potential of identifying novel pathways involved in cardiac performance and cardioprotection.

Thank you for your efforts to review our manuscript, we are delighted to learn that you found our approach to link transcriptomic, proteomic and phosphoproteome data in our analysis. We are delighted that you found our work to be well-conducted, to have been well performed, and that our analysis was thorough and well-integrated with our prior work in this arena and that are findings have the potential of identifying novel pathways involved in cardiac performance and cardioprotection.

Reviewer #1 (Recommendations For The Authors):

I humbly suggest that the authors reconsider the title, as it could be more clear as to what they are studying. Are the authors trying to highlight pathways related to cardiac resilience? Resilience might be a clearer word than "performance and protection circuitry".

Thank you for this important comment. We have revised the title accordingly: Reprogramming of cardiac phosphoproteome, proteome and transcriptome confers resilience to chronic adenylyl cyclase-driven stress.

Perhaps the text can be reviewed in detail by a copy-editor, as there are many grammatically 'awkward' elements (for example, line 56: "mammalians" instead of mammals), inappropriate colloquialisms (for example, line 73: "port-of-call"), and stylistic unevenness that make it difficult to read.

We have reviewed the text in detail, with the assistance of a copy editor, in order to identify and correct awkward elements and to search for other colloquialisms. Finally, although “stylistic unevenness” to which you refer may be difficult for us to identify during our re-edits, we have tried our best to identify and revise them.

The best-written sections are the first few paragraphs of the discussion section, which finally clarify why the TGAC8 mouse is important in understanding cardiac resilience to stress and how the present study leverages this model to disentangle the biological processes underlying the resilience. I wish this had been presented in this manner earlier in the paper, (in the abstract and introduction) so I could have had a clearer context in which to interpret the data. It would also be helpful to point out whether the TGAC8 mouse has any correlates with human disease.

Thank you for this very important comment. Well put! In addition to recasting the title to include the concept of resilience, we have revised both the abstract and introduction to feature what you consider to be important to the understanding of cardiac resilience to stress, and how the present study leverages this model to disentangle the biological processes underlying the resilience.

Reviewer #2 (Recommendations For The Authors):

1. How were the cutoffs determined to distinguish between upregulated/downregulated phosphoproteins and phosphopeptides?

Thank you for this important question. We used the same criteria to distinguish differences between TGAC8 and WT for unnormalized and normalized phosphoproteins, -log10(p-value) > 1.3, and log2FoldChange <= -0.4 (down) or log2FoldChange >= 0.4 (up), as stated in the methods section, main text and figure legend. The results were consistent across all analyses and selectively verified by experiments.

1. Were other models assessed for correlation between transcriptome and phosphoproteome other than a linear relationship of log2 fold change?

Thank you for this comment. In addition to a linear relationship of log2 fold change of molecule expression, we also compared protein activities, e.g., Fig 4F, and pathways enriched from different omics, e.g., Fig 3D, 5J, 6B and 6F.

1. Figures 1A and 5G seem to show outliers. How many biological and technical replicates would be needed to minimize error?

Thank you for the question. Figures 1A and 5G were PCA plots which, as expected, manifested some genetic variability among the same genotypes. The PCA plots, however, are useful in determining how the identified items separated, both within and among genotypes. For bioinformatics analysis such as ours, 4-5 samples are sufficient to accomplish this, as demonstrated by separation, by genotype, of samples in PCA. Thus, in addition to discovery of true heterogeneity among the samples, our results are still able to robustly discover the true differences between the genotypes.

1. Were the up/downregulated genes more likely to be lowly expressed (which would lead to larger log2 changes identified)?

In response to your query, we calculated the average expression of phosphorylation levels across all samples to observe whether they were expressed in low abundance in all samples. We also generated the MA plots, an application of a Bland–Altman plot, to create a visual representation of omics data. The MA plots in Author response image 1 illustrate that the target molecules with significantly changed phosphorylation levels did not aggregate within the very low abundance. To confirm this conclusion, we adopted two sets of cutoffs: (1) change: -log10(p-value) > 1.3, and log2FoldChange < 0 (down) or log2FoldChange > 0 (up); and (2) change_2: -log10(p-value) > 1.3, and log2FoldChange <= -0.4 (down) or log2FoldChange >= 0.4 (up).

Author response image 1.

1. "We verified some results through wet lab experiments" in the abstract is vague.

Thank you for the good suggestion. What we meant to indicate here was that identified genotypic differences in selected proteins, phosphoproteins and RNAs discovered in omics were verified by western blots, protein synthesis detection, proteosome activity detection, and protein soluble and insoluble fractions detection. However, we have deleted the reference to the wet lab experiments in the revised manuscript.

1. There are minor syntactical errors throughout the text.

Thank you very much for the suggestion. As noted in our response, we have edited and revised those errors throughout the text.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Tiedje et al. investigated the transient impact of indoor residual spraying (IRS) followed by seasonal malaria chemoprevention (SMC) on the plasmodium falciparum parasite population in a high transmission setting. The parasite population was characterized by sequencing the highly variable DBL$\alpha$ tag as a proxy for var genes, a method known as varcoding. Varcoding presents a unique opportunity due to the extraordinary diversity observed as well as the extremely low overlap of repertoires between parasite strains. The authors also present a new Bayesian approach to estimating individual multiplicity of infection (MOI) from the measured DBL$\alpha$ repertoire, addressing some of the potential shortcomings of the approach that have been previously discussed. The authors also present a new epidemiological endpoint, the so-called "census population size", to evaluate the impact of interventions. This study provides a nice example of how varcoding technology can be leveraged, as well as the importance of using diverse genetic markers for characterizing populations, especially in the context of high transmission. The data are robust and clearly show the transient impact of IRS in a high transmission setting, however, some aspects of the analysis are confusing.

(1) Approaching MOI estimation with a Bayesian framework is a well-received addition to the varcoding methodology that helps to address the uncertainty associated with not knowing the true repertoire size. It's unfortunate that while the authors clearly explored the ability to estimate the population MOI distribution, they opted to use only MAP estimates. Embracing the Bayesian methodology fully would have been interesting, as the posterior distribution of population MOI could have been better explored. 

We thank the reviewer for appreciating the extension of var_coding we present here. We believe the comment on maximum _a posteriori (MAP) refers to the way we obtained population-level MOI from the individual MOI estimates. We would like to note that reliance on MAP was only one of two approaches we described, although we then presented only MAP.  Having calculated both, we did not observe major differences between the two, for this data set.  Nonetheless, we revised the manuscript to include the result based on the mixture distribution which considers all the individual MOI distributions in the Figure supplement 6.

(2) The "census population size" endpoint has unclear utility. It is defined as the sum of MOI across measured samples, making it sensitive to the total number of samples collected and genotyped. This means that the values are not comparable outside of this study, and are only roughly comparable between strata in the context of prevalence where we understand that approximately the same number of samples were collected. In contrast, mean MOI would be insensitive to differences in sample size, why was this not explored? It's also unclear in what way this is a "census". While the sample size is certainly large, it is nowhere near a complete enumeration of the parasite population in question, as evidenced by the extremely low level of pairwise type sharing in the observed data. 

We consider the quantity a census in that it is a total enumeration or count of infections in a given population sample and over a given time period. In this sense, it gives us a tangible notion of the size of the parasite population, in an ecological sense, distinct from the formal effective population size used in population genetics. Given the low overlap between var repertoires of parasites (as observed in monoclonal infections), the population size we have calculated translates to a diversity of strains or repertoires.  But our focus here is in a measure of population size itself.  The distinction between population size in terms of infection counts and effective population size from population genetics has been made before for pathogens (see for example Bedford et al. for the seasonal influenza virus and for the measles virus (Bedford et al., 2011)), and it is also clear in the ecological literature for non-pathogen populations (Palstra and Fraser, 2012). 

We completely agree with the dependence of our quantity on sample size. We used it for comparisons across time of samples of the same depth, to describe the large population size characteristic of high transmission which persists across the IRS intervention. Of course, one would like to be able to use this quantity across studies that differ in sampling depth and the reviewer makes an insightful and useful suggestion.  It is true that we can use mean MOI, and indeed there is a simple map between our population size and mean MOI (as we just need to divide or multiply by sample size, respectively) (Table supplement 7).  We can go further, as with mean MOI we can presumably extrapolate to the full sample size of the host population, or to the population size of another sample in another location. What is needed for this purpose is a stable mean MOI relative to sample size.  We can show that indeed in our study mean MOI is stable in that way, by subsampling to different depths our original sample (Figure supplement 8 in the revised manuscript). We now include in the revision discussion of this point, which allows an extrapolation of the census population size to the whole population of hosts in the local area.

We have also clarified the time denominator: Given the typical duration of infection, we expect our population size to be representative of a per-generation measure_._

(3) The extraordinary diversity of DBL$\alpha$ presents challenges to analyzing the data. The authors explore the variability in repertoire richness and frequency over the course of the study, noting that richness rapidly declined following IRS and later rebounded, while the frequency of rare types increased, and then later declined back to baseline levels. The authors attribute this to fundamental changes in population structure. While there may have been some changes to the population, the observed differences in richness as well as frequency before and after IRS may also be compatible with simply sampling fewer cases, and thus fewer DBL$\alpha$ sequences. The shift back to frequency and richness that is similar to pre-IRS also coincides with a similar total number of samples collected. The authors explore this to some degree with their survival analysis, demonstrating that a substantial number of rare sequences did not persist between timepoints and that rarer sequences had a higher probability of dropping out. This might also be explained by the extreme stochasticity of the highly diverse DBL$\alpha$, especially for rare sequences that are observed only once, rather than any fundamental shifts in the population structure.

We thank the reviewer raising this question which led us to consider whether the change in the number of DBLα types over the course of the study (and intervention) follows from simply sampling fewer P. falciparum cases. We interpreted this question as basically meaning that one can predict the former from the latter in a simple way, and that therefore, tracking the changes in DBLα type diversity would be unnecessary.  A simple map would be for example a linear relationship (a given proportion of DBLα types lost given genomes lost), and even more trivially, a linear loss with a slope of one (same proportion).  Note, however, that for such expectations, one needs to rely on some knowledge of strain structure and gene composition. In particular, we would need to assume a complete lack of overlap and no gene repeats in a given genome. We have previously shown that immune selection leads to selection for minimum overlap and distinct genes in repertoires at high transmission (see for example (He et al., 2018)) for theoretical and empirical evidence of both patterns). Also, since the size of the gene pool is very large, even random repertoires would lead to limited overlap (even though the empirical overlap is even smaller than that expected at random (Day et al., 2017)). Despite these conservators, we cannot a priori assume a pattern of complete non-overlap and distinct genes, and ignore plausible complexities introduced by the gene frequency distribution.  

To examine this insightful question, we simulated the loss of a given proportion of genomes from baseline in 2012 and examined the resulting loss of DBLα types. We specifically cumulated the loss of infections in individuals until it reached a given proportion (we can do this on the basis of the estimated individual MOI values). We repeated this procedure 500 times for each proportion, as the random selection of individual infection to be removed, introduces some variation. Figure 2 below shows that the relationship is nonlinear, and that one quantity is not a simple proportion of the other.  For example, the loss of half the genomes does not result in the loss of half the DBLα types. 

Author response image 1.

Non-linear relationship between the loss of DBLα types and the loss of a given proportion of genomes. The graph shows that the removal of parasite genomes from the population through intervention does not lead to the loss of the same proportion of DBLα types, as the initial removal of genomes involves the loss of rare DBLα types mostly whereas common DBLα types persist until a high proportion of genomes are lost. The survey data (pink dots) used for this subsampling analysis was sampled at the end of wet/high transmission season in Oct 2012 from Bongo District from northern Ghana. We used the Bayesian formulation of the _var_coding method proposed in this work to calculate the multiplicity of infection of each isolate to further obtain the total number of genomes. The randomized surveys (black dots) were obtained based on “curveball algorithm” (Strona et al., 2014) which keep isolate lengths and type frequency distribution.

We also investigated whether the resulting pattern changed significantly if we randomized the composition of the isolates.  We performed such randomization with the “curveball algorithm” (Strona et al., 2014). This algorithm randomizes the presence-absence matrix with rows corresponding to the isolates and columns, to the different DBLα types; importantly, it preserves the DBLα type frequency and the length of isolates. We generated 500 randomizations and repeated the simulated loss of genomes as above. The data presented in Figure 2 above show that the pattern is similar to that obtained for the empirical data presented in this study in Ghana. We interpret this to mean that the number of genes is so large, that the reduced overlap relative to random due to immune selection (see (Day et al., 2017)) does not play a key role in this specific pattern. 

Reviewer #2 (Public Review):  

In this manuscript, Tiedje and colleagues longitudinally track changes in parasite numbers across four time points as a way of assessing the effect of malaria control interventions in Ghana. Some of the study results have been reported previously, and in this publication, the authors focus on age-stratification of the results. Malaria prevalence was lower in all age groups after IRS. Follow-up with SMC, however, maintained lower parasite prevalence in the targeted age group but not the population as a whole. Additionally, they observe that diversity measures rebounds more slowly than prevalence measures. Overall, I found these results clear, convincing, and well-presented. They add to a growing literature that demonstrates the relevance of asymptomatic reservoirs.  There is growing interest in developing an expanded toolkit for genomic epidemiology in malaria, and detecting changes in transmission intensity is one major application. As the authors summarize, there is no one-size-fits-all approach, and the Bayesian MOIvar estimate developed here has the potential to complement currently used methods. I find its extension to a calculation of absolute parasite numbers appealing as this could serve as both a conceptually straightforward and biologically meaningful metric. However, I am not fully convinced the current implementation will be applied meaningfully across additional studies. 

(1) I find the term "census population size" problematic as the groups being analyzed (hosts grouped by age at a single time point) do not delineate distinct parasite populations. Separate parasite lineages are not moving through time within these host bins. Rather, there is a single parasite population that is stochastically divided across hosts at each time point. I find this distinction important for interpreting the results and remaining mindful that the 2,000 samples at each time point comprise a subsample of the true population. Instead of "census population size", I suggest simplifying it to "census count" or "parasite lineage count".  It would be fascinating to use the obtained results to model absolute parasite numbers at the whole population level (taking into account, for instance, the age structure of the population), and I do hope this group takes that on at some point even if it remains outside the scope of this paper. Such work could enable calculations of absolute---rather than relative---fitness and help us further understand parasite distributions across hosts.

Lineages moving exclusively through a given type of host or “patch”  are not a necessary requirement for enumerating the size of the total infections in such subset.  It is true that what we have is a single parasite population, but we are enumerating for the season the respective size in host classes (children and adults). This is akin to enumerating subsets of a population in ecological settings where one has multiple habitat patches, with individuals able to move across patches.

Remaining mindful that the count is relative to sample size is an important point. Please see our response to comment (2) of reviewer 1, also for the choice of terminology. We prefer not to adopt “census count” as a census in our mind is a count, and we are not clear on the concept of lineage for these highly recombinant parasites.  Also, census population size has been adopted already in the literature for both pathogens and non-pathogens, to make a distinction with the notion of effective population size in population genetics (see our response to reviewer 1) and is consistent with our usage as outlined in the introduction. 

Thank you for the comment on an absolute number which would extrapolate to the whole host population.  Please see again our response to comment (2) of reviewer 1, on how we can use mean MOI for this purpose once the sampling is sufficient for this quantity to become constant/stable with sampling effort.

(2) I'm uncertain how to contextualize the diversity results without taking into account the total number of samples analyzed in each group. Because of this, I would like a further explanation as to why the authors consider absolute parasite count more relevant than the combined MOI distribution itself (which would have sample count as a denominator). It seems to me that the "per host" component is needed to compare across age groups and time points---let alone different studies.

Again, thank you for the insightful comment. We provide this number as a separate quantity and not a distribution, although it is clearly related to the mean MOI of such distribution. It gives a tangible sense for the actual infection count (different from prevalence) from the perspective of the parasite population in the ecological sense. The “per host” notion which enables an extrapolation to any host population size for the purpose of a complete count, or for comparison with another study site, has been discussed in the above responses for reviewer 1 and now in the revision of the discussion.

(3) Thinking about the applicability of this approach to other studies, I would be interested in a larger treatment of how overlapping DBLα repertoires would impact MOIvar estimates. Is there a definable upper bound above which the method is unreliable? Alternatively, can repertoire overlap be incorporated into the MOI estimator? 

This is a very good point and one we now discuss further in our revision. There is no predefined upper bound one can present a priori. Intuitively, the approach to estimate MOI would appear to breakdown as overlap moves away from extremely low values, and therefore for locations with low transmission intensity.  Interestingly, we have observed that this is not the case in our paper by Labbe et al. (Labbé et al., 2023) where we used model simulations in a gradient of three transmission intensities, from high to low values. The original _var_coding method performed well across the gradient. This robustness may arise from a nonlinear and fast transition from low to high overlap that is accompanied by MOI changing rapidly from primarily multiclonal (MOI > 1) to monoclonal (MOI = 1). This matter clearly needs to be investigated further, including ways to extend the estimation to explicitly include the distribution of overlap.

Smaller comments:

- Figure 1 provides confidence intervals for the prevalence estimates, but these aren't carried through on the other plots (and Figure 5 has lost CIs for both metrics). The relationship between prevalence and diversity is one of the interesting points in this paper, and it would be helpful to have CIs for both metrics when they are directly compared. 

Based on the reviewer’s advice we have revised both Figure 4 and Figure 5, to include the missing uncertainty intervals. The specific approach for each quantity is described in the corresponding caption.

Reviewer #3 (Public Review): 

Summary: 

The manuscript coins a term "the census population size" which they define from the diversity of malaria parasites observed in the human community. They use it to explore changes in parasite diversity in more than 2000 people in Ghana following different control interventions. 

Strengths: 

This is a good demonstration of how genetic information can be used to augment routinely recorded epidemiological and entomological data to understand the dynamics of malaria and how it is controlled. The genetic information does add to our understanding, though by how much is currently unclear (in this setting it says the same thing as age-stratified parasite prevalence), and its relevance moving forward will depend on the practicalities and cost of the data collection and analysis. Nevertheless, this is a great dataset with good analysis and a good attempt to understand more about what is going on in the parasite population. 

Census population size is complementary to parasite prevalence where the former gives a measure of the “parasite population size”, and the latter describes the “proportion of infected hosts”.  The reason we see similar trends for the “genetic information” (i.e., census population size) and “age-specific parasite prevalence” is because we identify all samples for var_coding based on the microscopy (i.e., all microscopy positive _P. falciparum isolates). But what is more relevant here is the relative percentage change in parasite prevalence and census population size following the IRS intervention. To make this point clearer in the revised manuscript we have updated Figure 4 and included additional panels plotting this percentage change from the 2012 baseline, for both census population size and prevalence (Figure 4EF). Overall, we see a greater percentage change in 2014 (and 2015), relative to the 2012 baseline, for census parasite population size vs. parasite prevalence (Figure 4EF) as a consequence of the significant changes in distributions of MOI following the IRS intervention (Figure 3). As discussed in the Results following the deployment of IRS in 2014 census population size decreased by 72.5% relative to the 2012 baseline survey (pre-IRS) whereas parasite prevalence only decreased by 54.5%. 

With respect to the reviewer’s comment on “practicalities and cost”, var_coding has been used to successfully amplify _P. falciparum DNA collected as DBS that have been stored for more than 5-years from both clinical and lower density asymptomatic infection, without the additional step and added cost of sWGA ($8 to $32 USD per isolates, for costing estimates see (LaVerriere et al., 2022; Tessema et al., 2020)), which is currently required by other molecular surveillance methods (Jacob et al., 2021; LaVerriere et al., 2022; Oyola et al., 2016). _Var_coding involves a single PCR per isolate using degenerate primers, where a large number of isolates can be multiplexed into a single pool for amplicon sequencing.  Thus, the overall costs for incorporating molecular surveillance with _var_coding are mainly driven by the number of PCRs/clean-ups, the number samples indexed per sequencing run, and the NGS technology used (discussed in more detail in our publication Ghansah et al. (Ghansah et al., 2023)). Previous work has shown that _var_coding can be use both locally and globally for molecular surveillance, without the need to be customized or updated, thus it can be fairly easily deployed in malaria endemic regions (Chen et al., 2011; Day et al., 2017; Rougeron et al., 2017; Ruybal-Pesántez et al., 2022, 2021; Tonkin-Hill et al., 2021).

Weaknesses: 

Overall the manuscript is well-written and generally comprehensively explained. Some terms could be clarified to help the reader and I had some issues with a section of the methods and some of the more definitive statements given the evidence supporting them. 

Thank you for the overall positive assessment. On addressing the “issues with a section of the methods” and “some of the more definitive statements given the evidence supporting them”, it is impossible to do so however, without an explicit indication of which methods and statements the reviewer is referring to. Hopefully, the answers to the detailed comments and questions of reviewers 1 and 2 address any methodological concerns (i.e., in the Materials and Methods and Results). To the issue of “definitive statements”, etc. we are unable to respond without further information.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

Line 273: there is a reference to a figure which supports the empirical distribution of repertoire given MOI = 1, but the figure does not appear to exist.

We now included the correct figure for the repertoire size distribution as Figure supplement 3 (previously published in Labbé et al (Labbé et al., 2023)). This figure was accidently forgotten when the manuscript was submitted for review, we thank the reviewer for bringing this to our attention.

Line 299: while this likely makes little difference, an insignificant result from a Kolmogorov-Smirnov test doesn't tell you if the distributions are the same, it only means there is not enough evidence to determine they are different (i.e. fail to reject the null). Also, what does the "mean MOI difference" column in supplementary table 3 mean? 

The mean MOI difference is the difference in the mean value between the pairwise comparison of the true population-level MOI distribution, that of the population-level MOI estimates from either pooling the maximum a posteriori (MAP) estimates per individual host or the mixture distribution, or that of the population-level MOI estimates from different prior choices. This is now clarified as requested in the Table supplements 3 - 6. 

Figure 4: how are the confidence intervals for the estimated number of var repertoires calculated? Also should include horizontal error bars for prevalence measures.

The confidence intervals were calculated based on a bootstrap approach. We re-sampled 10,000 replicates from the original population-level MOI distribution with replacement. Each resampled replicate is the same size as the original sample. We then derive the 95% CI based on the distribution of the mean MOI of those resampled replicates. This is now clarified as requested in the Figure 4 caption (as well as Table supplement 7 footnotes). In addition, we have also updated Figure 4AB and have included the 95% CI for all measures for clarity. 

Reviewer #2 (Recommendations For The Authors): 

-  I would like to see a plot like Supplemental Figure 8 for the upsA DBLα repertoire size. 

The upsA repertoire size for each survey and by age group has now been provided as requested in Figure supplement 5AB. 

-  Supplemental Table 2 is cut off in the pdf. 

We have now resolved this issue so that the Table supplement 2 is no longer cut off.  

Reviewer #3 (Recommendations For The Authors): 

The manuscript terms the phrase "census population size". To me, the census is all about the number of individuals, not necessarily their diversity. I appreciate that there is no simple term for this, and I imagine the authors have considered many alternatives, but could it be clearer to say the "genetic census population size"? For example, I found the short title not particularly descriptive "Impact of IRS and SMC on census population size", which certainly didn't make me think of parasite diversity.

Please see our response to comment (2) of reviewer 1. We prefer not to add “genetic” to the phrase as the distinction from effective population size from population genetics is important, and the quantity we are after is an ecological one. 

The authors do not currently say much about the potential biases in the genetic data and how this might influence results. It seems likely that because (i) patients with sub-microscopic parasitaemia were not sampled and (ii) because a moderate number of (likely low density) samples failed to generate genetic data, that the observed MOI is an overestimate. I'd be interested to hear the authors' thoughts about how this could be overcome or taken into account in the future. 

We thank the reviewer for this this comment and agree that this is an interesting area for further consideration. However, based on research from the Day Lab that is currently under review (Tan et al. 2024, under review), the estimated MOI using the Bayesian approach is likely not an “overestimate” but rather an “underestimate”. In this research by Tan et al. (2024) isolate MOI was estimated and compared using different initial whole blood volumes (e.g., 1, 10, 50, 100 uL) for the gDNA extraction. Using _var_coding and comparing these different volumes it was found that MOI was significantly “underestimated” when small blood volumes were used for the gDNA extraction, i.e., there was a ~3-fold increase in median MOI between 1μL and 100μL blood. Ultimately these findings will allow us to make computational corrections so that more accurate estimates of MOI can be obtained from the DBS in the future.

The authors do not make much of LLIN use and for me, this can explain some of the trends. The first survey was conducted soon after a mass distribution whereas the last was done at least a year after (when fewer people would have been using the nets which are older and less effective). We have also seen a rise in pyrethroid resistance in the mosquito populations of the area which could further diminish the LLIN activity. This difference in LLIN efficacy between the first and last survey could explain similar prevalence, yet lower diversity (in Figures 4B/5). However, it also might mean that statements such as Line 478 "This is indicative of a loss of immunity during IRS which may relate to the observed loss of var richness, especially the many rare types" need to be tapered as the higher prevalence observed in this age group could be caused by lower LLIN efficacy at the time of the last survey, not loss of immunity (though both could be true).  

We thank the reviewer for this question and agree that (i) LLIN usage and (ii) pyrethroid resistance are important factors to consider. 

(i) Over the course of this study self-reported LLIN usage the previous night remained high across all age groups in each of the surveys (≥ 83.5%), in fact more participants reported sleeping under an LLIN in 2017 (96.8%) following the discontinuation of IRS compared to the 2012 baseline survey (89.1%). This increase in LLIN usage in 2017 is likely a result of several factors including a rebound in the local vector population making LLINs necessary again, increased community education and/or awareness on the importance of using LLINs, among others. Information on the LLINs (i.e., PermaNet 2.0, Olyset, or DawaPlus 2.0) distributed and participant reported usage the previous night has now been included in the Materials and Methods as requested by the reviewer.

(ii) As to the reviewer’s question on increased in pyrethroid resistance in Ghana over the study period, research undertaken by our entomology collaborators (Noguchi Memorial Insftute for Medical Research: Profs. S. Dadzie and M. Appawu; and Navrongo Health Research Centre:  Dr. V. Asoala) has shown that pyrethroid resistance is a major problem across the country, including the Upper East Region. Preliminary studies from Bongo District (2013 - 2015), were undertaken to monitor for mutations in the voltage gated sodium channel gene that have been associated with knockdown resistance to pyrethroids and DDT in West Africa (kdr-w). Through this analysis the homozygote resistance kdr-w allele (RR) was found in 90% of An. gambiae s.s. samples tested from Bongo, providing evidence of high pyrethroid resistance in Bongo District dating back to 2013, i.e., prior to the IRS intervention (S. Dadzie, M. Appawu, personal communication). Although we do not have data in Bongo District on kdr-w from 2017 (i.e., post-IRS), we can hypothesize that pyrethroid resistance likely did not decline in the area, given the widespread deployment and use of LLINs.

Thus, given this information that (i) self-reported LLIN usage remained high in all surveys (≥ 83.5%), and that (ii) there was evidence of high pyrethroid resistance in 2013 (i.e., kdr-w (RR) _~_90%), the rebound in prevalence observed for the older age groups (i.e., adolescents and adults) in 2017 is therefore best explained by a loss of immunity.

I must confess I got a little lost with some of the Bayesian model section methods and the figure supplements. Line 272 reads "The measurement error is simply the repertoire size distribution, that is, the distribution of the number of non-upsA DBLα types sequenced given MOI = 1, which is empirically available (Figure supplement 3)." This does not appear correct as this figure is measuring kl divergence. If this is not a mistake in graph ordering please consider explaining the rationale for why this graph is being used to justify your point. 

We now included the correct figure for the repertoire size distribution as Figure supplement 3 (previously published in Labbé et al (Labbé et al., 2023)). This figure was accidently forgotten when the manuscript was submitted for review, we thank the reviewer for bringing our attention to this matter. We hope that the inclusion of this Figure as well as a more detailed description of the Bayesian approach helps to makes this section in the Materials and Methods clearer for the reader. 

I was somewhat surprised that the choice of prior for estimating the MOI distribution at the population level did not make much difference. To me, the negative binomial distribution makes much more sense. I was left wondering, as you are only measuring MOI in positive individuals, whether you used zero truncated Poisson and zero truncated negative binomial distributions, and if not, whether this was a cause of a lack of difference between uniform and other priors. 

Thank you for the relevant question. We have indeed considered different priors and the robustness of our  estimates to this choice and have now better described this in the text. We focused on individuals who had a confirmed microscopic asymptomatic P. falciparum infection for our MOI estimation, as median P. falciparum densities were overall low in this population during each survey (i.e., median ≤ 520 parasites/µL, see Table supplement 1). Thus, we used either a uniform prior excluding zero or a zero truncated negative binomial distribution when exploring the impact of priors on the final population-level MOI distribution.  A uniform prior and a zero-truncated negative binomial distribution with parameters within the range typical of high-transmission endemic regions (higher mean MOI with tails around higher MOI values) produce similar MOI  estimates at both the individual and population level. However, when setting the parameter range of the zero-truncated negative binomial to be of those in low transmission endemic regions where the empirical MOI distribution centers around mono-clonal infections with the majority of MOI = 1 or 2 (mean MOI » 1.5, no tail around higher MOI values), the final population-level MOI distribution does deviate more from that assuming the aforementioned prior and parameter choices. The final individual- and population-level MOI estimates are not sensitive to the specifics of the prior MOI distribution as long as this distribution captures the tail around higher MOI values with above-zero probability.   

The high MOI in children <5yrs in 2017 (immediately after SMC) is very interesting. Any thoughts on how/why? 

This result indicates that although the prevalence of asymptomatic P. falciparum infections remained significantly lower for the younger children targeted by SMC in 2017 compared 2012, they still carried multiclonal infections, as the reviewer has pointed out (Figure 3B). Importantly this upward shift in the MOI distributions (and median MOI) was observed in all age groups in 2017, not just the younger children, and provides evidence that transmission intensity in Bongo has rebounded in 2017, 32-months a er the discontinuation of IRS.  This increase in MOI for younger children at first glance may seem to be surprising, but instead likely shows the limitations of SMC to clear and/or supress the establishment of newly acquired infections, particularly at the end of the transmission season following the final cycle of SMC (i.e., end of September 2017 in Bongo District; NMEP/GHS, personal communication) when the posttreatment prophylactic effects of SMC would have waned (Chotsiri et al., 2022).  

Line 521 in the penultimate paragraph says "we have analysed only low density...." should this not be "moderate" density, as low density infections might not be detected? The density range itself is not reported in the manuscript so could be added. 

In Table supplement 1 we have provided the median, including the inter-quartile range, across each survey by age group. For the revision we have now provided the density min-max range, as requested by the reviewer. Finally, we have revised the statement in the discussion so that it now reads “….we have analysed low- to moderate-density, chronic asymptomatic infections (see Table supplement 1)……”.   

Data availability - From the text the full breakdown of the epidemiological survey does not appear to be available, just a summary of defined age bounds in the SI. Provision of these data (with associated covariates such as parasite density and host characteristics linked to genetic samples) would facilitate more in-depth secondary analyses. 

To address this question, we have updated the “Data availability statement” section with the following statement: “All data associated with this study are available in the main text, the Supporting Information, or upon reasonable request for research purposes to the corresponding author, Prof. Karen Day (karen.day@unimelb.edu.au).”  

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Author Response

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

Reviewer #1 (Public Review):

The expression and localization of Foxc2 strongly suggest that its role is mainly confined to As undifferentiated spermatogonia (uSPGs). Lineage tracing demonstrated that all germ cells were derived from the FOXC2+ uSPGs. Specific ablation of the FOXC2+ uSPGs led to the depletion of all uSPG populations. Full spermatogenesis can be achieved through the transplantation of Foxc2+ uSPGs. Male germ cell-specific ablation of Foxc2 caused Sertoli-only testes in mice. CUT&Tag sequencing revealed that FOXC2 regulates the factors that inhibit the mitotic cell cycle, consistent with its potential role in maintaining a quiescent state in As spermatogonia. These data made the authors conclude that the FOXC2+ uSPG may be the true SSCs, essential for maintaining spermatogenesis. The conclusion is largely supported by the data presented, but two concerns should be addressed: 1) terminology used is confusing: primitive SSCs, primitive uSPGs, transit amplifying SSCs... 2) the GFP+ cells used for germ cell transplantation should be better controlled using THY1+ cells.

Thanks for your good comments. According to your suggestions, we have addressed your two concerns as follows:

1> Overall our work suggest that FOXC2+ SSCs are a subpopulation of SSCs in a quiescent state, thus we have replaced the term ‘primitive’ with ‘quiescent’ in the revised manuscript. In general, ‘transient amplifying SSCs’ is considered to be ‘progenitors’, thus we have replaced ‘transient amplifying SSCs’ with ‘progenitors’ in the revised manuscript.

2> The transplantation experiment was conducted using MACS-sorted THY1+, FACS sorted THY1+, and FACS-sorted GFP+ (FOXC2+) uSPGs simultaneously. To be consistent with the single-cell RNA-seq using the MACS-sorted THY1+ uSPGs, we only presented the results from MACS-sorted THY1+ and FACS-sorted GFP+ (FOXC2+) uSPGs in the previous manuscript. Following the reviewer’s suggestion, we have included the results derived from FACS sorted THY1+ uSPGs as the control. The overall conclusion is still fully supported by the more comprehensive dataset, i.e. FOXC2+ cells generated significant higher numbers of colonies than THY1+ cells after transplantation (Figure 2D, E).

Reviewer #2 (Public Review):

The authors found FOXC2 is mainly expressed in As of mouse undifferentiated spermatogonia (uSPG). About 60% of As uSPG were FOXC2+ MKI67-, indicating that FOXC2 uSPG were quiescent. Similar spermatogonia (ZBTB16+ FOXC2+ MKI67-) were also found in human testis.

The lineage tracing experiment using Foxc2iCreERT2/+;Rosa26LSL-T/G/LSL-T/G mice demonstrated that all germ cells were derived from the FOXC2+ uSPG. Furthermore, specific ablation of the FOXC2+ uSPGs using Foxc2iCreERT2/+;Rosa26LSL-DTA/+ mice resulted in the depletion of all uSPG population. In the regenerative condition created by busulfan injection, all FOXC2+ uSPG survived and began to proliferate at around 30 days after busulfan injection. The survived FOXC2+ uSPGs generated all germ cells eventually. To examine the role of FOXC2 in the adult testis, spermatogenesis of Foxc2f/-;Ddx4Cre/+ mice was analyzed. From a 2-month-old, the degenerative seminiferous tubules were increased and became Sertoli cell-only seminiferous tubules, indicating FOXC2 is required to maintain normal spermatogenesis in adult testes. To get insight into the role of FOXC2 in the uSPG, CUT&Tag sequencing was performed in sorted FOXC2+ uSPG from Foxc2iCreERT2/+;Rosa26LSL-T/G/LSL-T/G mice 3 days after TAM diet feeding. The results showed some unique biological processes, including negative regulation of the mitotic cell cycle, were enriched, suggesting the FOXC2 maintains a quiescent state in spermatogonia.

Lineage tracing experiments using transgenic mice of the TAM-inducing system was well-designed and demonstrated interesting results. Based on all data presented, the authors concluded that the FOXC2+ uSPG are primitive SSCs, an indispensable subpopulation to maintain adult spermatogenesis.

The conclusion of the mouse study is mostly supported by the data presented, but to accept some of the authors' claims needs additional information and explanation. Several terminologies define cell populations used in the paper may mislead readers.

1) "primitive spermatogonial stem cell (SSC)" is confusing. SSCs are considered the most immature subpopulation of uSPG. Thus, primitive uSPGs are likely SSCs. The naming, primitive SSCs, and transit-amplifying SSCs (Figure 7K) are weird. In general, the transit-amplifying cell is progenitor, not stem cell. In human and even mouse, there are several models for the classification of uSPG and SSCs, such as reserved stem cells and active stem cells. The area is highly controversial. The authors' definition of stem cells and progenitor cells should be clarified rigorously and should compare to existing models.

Thanks for your good comments. Considering that our results showed that FOXC2+ SSCs are in a quiescent state and that Mechanistically FOXC2 maintained the quiescent state of SSCs by promoting the expression of negative regulators of cell cycle, we have replaced ‘primitive SSCs’ with ‘quiescent SSCs’ in the revised manuscript. We agree with the reviewer that ‘transient amplifying SSCs’ is considered to be ‘progenitors’, thus we have replaced ‘transient amplifying SSCs’ with ‘progenitors’ in the revised manuscript. Further，from our point of view, the FOXC2+Ki67+ SSCs could be regarded as active stem cells, and the FOXC2+Ki67- SSCs could be regarded as reserved stem cells, although further research evidence is still needed to confirm this.

2) scRNA seq data analysis and an image of FOXC2+ ZBTB16+ MKI67- cells by fluorescent immunohistochemistry are not sufficient to conclude that they are human primitive SSCs as described in the Abstract. The identity of human SSCs is controversial. Although Adark spermatogonia are a candidate population of human SSCs, the molecular profile of the Adark spermatogonia seems to be heterogeneous. None of the molecular profiles was defined by a specific cell cycle phase. Thus, more rigorous analysis is required to demonstrate the identity of FOXC2+ ZBTB16+ MKI67- cells and Adark spermatogonia.

We agree with the reviewer that the identity of human SSCs remain elusive even though Adark population demonstrates certain characteristics of SSCs. To acknowledge this notion, we have revised our conclusion as such that only suggests FOXC2+ZBTB16+MKI67- represents a quiescent state of human SSCs.

3) FACS-sorted GFP+ cells and MACS-THY1 cells were used for functional transplantation assay to evaluate SSC activity. In general, the purity of MACS is significantly lower than that of FACS. Therefore, FACS-sorted THY1 cells must be used for the comparative analysis. As uSPGs in adult testes express THY1, the percentage of GFP+ cells in THY1+ cells determined by flow cytometry is important information to support the transplantation data.

Thanks for your good comments. According to your suggestions, we have addressed your concerns as follows:

1> The transplantation experiment was conducted using MACS-sorted THY1+, FACS sorted THY1+, and FACS-sorted GFP+ (FOXC2+) uSPGs simultaneously. To be consistent with the single-cell RNA-seq using the MACS-sorted THY1+ uSPGs, we only presented the results from MACS-sorted THY1+ and FACS-sorted GFP+ (FOXC2+) uSPGs in the previous manuscript. Following the reviewer’s suggestion, we have included the results derived from FACS sorted THY1+ uSPGs as the control. The overall conclusion is still fully supported by the more comprehensive dataset, i.e. FOXC2+ cells generated significant higher numbers of colonies than THY1+ cells after transplantation (Figure 2D, E).

2> We performed FACS analysis to determine the proportion of GFP+ cells in FACS-sorted THY1+ cells from Rosa26LSL-T/G/LSL-T/G or Foxc2iCreERT2/+;Rosa26LSL-T/G/LSL-T/G mice at day 3 post TAM induction, and the result showed that GFP+ cells account for approximately 20.9±0.21% of THY1+ cells, See Author response image 1.

Author response image 1.

4) The lineage tracing experiments of FOXC2+-SSCs in Foxc2iCreERT2/+;Rosa26LSL-T/G/LSL-T/G showed ~95% of spermatogenic cells and 100% progeny were derived from the FOXC2+ (GFP+) spermatogonia (Figure 2I, J) at month 4 post-TAM induction, although FOXC2+ uSPG were quiescent and a very small subpopulation (~ 60% of As, ~0.03% in all cells). This means that 40% of As spermatogonia and most of Apr/Aal spermatogonia, which were FOXC2 negative, did not contribute to spermatogenesis at all eventually. This is a striking result. There is a possibility that FOXC2CRE expresses more widely in the uSPG population although immunohistochemistry could not detect them.

Thanks for your good comments. From our lineage tracing results, over 95% of the spermatogenic cells are derived from the FOXC2+ SSCs in the testes of 4-month-old mice, which means that FOXC2+ SSCs maintain a long-term stable spermatogenesis. In addition, previous studies have shown that only a portion of As spermatogonia belong to SSCs with complete self-renewal ability (PMID: 28087628, PMID: 25133429), which is consistent with our findings. Therefore, we speculate that 40% of As spermatogonia and most of Apr/Aal spermatogonia, which were FOXC2 negative, did contribute to spermatogenesis but cannot maintain a long-term spermatogenesis due to limited self-renewal ability.

5) The CUT&Tag_FOXC2 analysis on the FACS-sorted FOXC2+ showed functional enrichment in biological processes such as DNA repair and mitotic cell cycle regulation (Figure 7D). The cells sorted were induced Cre recombinase expression by TAM diet and cut the tdTomato cassette out. DNA repair process and negative regulation of the mitotic cell cycle could be induced by the Cre/lox recombination process. The cells analyzed were not FOXC2+ uSPG in a normal physiological state.

We do appreciate the reviewer’s concern on the possibility of the functions enriched in the analysis as referred might be derived from Cre/lox recombination. However, we think it is unlikely that the Cre/lox recombination process, supposed to be rather local and specific, can trigger such a systemic and robust response by the DNA damage and cell cycle regulatory pathways. The reasons are as follows: First, as far as we are aware, there has been sufficient data to support this suggested scenario. Second, we did not observe any alteration in either the SSC behaviors or spermatogenesis in general upon the TAM-induced genomic changes, suggesting the impact from the Cre/lox recombination on DNA damage or cell cycle was not significant. Third, no factors associated with the DNA repair process were revealed in the differential analysis of single-cell transcriptomes of FOXC2-WT and FOXC2-KO.

6) Wei et al (Stem Cells Dev 27, 624-636) have published that FOXC2 is expressed predominately in As and Apr spermatogonia and requires self-renewal of mouse SSCs; however, the authors did not mention this study in Introduction, but referred shortly this at the end of Discussion. Their finding should be referred to and evaluated in advance in the Introduction.

Thanks for your good comments. According to your suggestion, we have revised the introduction to refer this latest parallel work on FOXC2. We are happy to see that our discoveries are converged to the important role of FOXC2 in regulating SSCs in adult mammals.  

Reviewer #3 (Public Review):

By popular single-cell RNA-seq, the authors identified FOXC2 as an undifferentiated spermatogonia-specific expressed gene. The FOXC2+-SSCs can sufficiently initiate and sustain spermatogenesis, the ablation of this subgroup results in the depletion of the uSPG pool. The authors provide further evidence to show that this gene is essential for SSCs maintenance by negatively regulating the cell cycle in adult mice, thus well-established FOXC2 as a key regulator of SSCs quiescent state.

The experiments are well-designed and conducted, the overall conclusions are convincing. This work will be of interest to stem cell and reproductive biologists.

Thanks for the positive feedback.  

Reviewer #1 (Recommendations for the Authors):

The authors should address the following concerns:

1) The most primitive uSPGs should be the true SSCs. The term "primitive SSCs" is very confusing.

2) In addition to FACS-sorted GFP+ cells, FACS-sorted THY1+ cells should also be used for transplantation.

Thanks for your good comments. According to your suggestions, we have addressed your two concerns as follows:

1) Overall our work suggest that FOXC2+ SSCs are a subpopulation of SSCs in a quiescent state, thus we have replaced the term ‘primitive’ with ‘quiescent’ in the revised manuscript.

2) The transplantation experiment was conducted using MACS-sorted THY1+, FACS sorted THY1+, and FACS-sorted GFP+ (FOXC2+) uSPGs simultaneously. To be consistent with the single-cell RNA-seq using the MACS-sorted THY1+ uSPGs, we only presented the results from MACS-sorted THY1+ and FACS-sorted GFP+ (FOXC2+) uSPGs in the previous manuscript. Following the reviewer’s suggestion, we have included the results derived from FACS sorted THY1+ uSPGs as the control. The overall conclusion is still fully supported by the more comprehensive dataset, i.e. FOXC2+ cells generated significant higher numbers of colonies than THY1+ cells after transplantation (Figure 2D, E).

Reviewer #3 (Recommendations for the Authors):

The experiments are well-designed and conducted, the overall conclusions are convincing. The only concerns are the writing, especially the introduction which was not well-rationalized. Sounds the three subtypes and three models for SSCs' self-renew are irrelevant to the major points of this manuscript. I don't think you need to talk too much about the markers of SSCs. Instead, I suggest you provide more background about the quiescent or activation states of the SSCs. In addition to that, as a nuclear-localized protein, it cannot be used to flow cytometric sorting, I don't think it should be emphasized as a marker. You identified a key transcription factor for maintaining the quiescent state of the primitive SSCs, that's quite important!

Appreciate the positive feedback and constructive suggestions on the writing. We have substantially revised our manuscript to include the relevant advances and understanding from the field as well as highlight the importance of FOXC2 in regulating the quiescent state of SSCs.

Author response:

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

Reviewer #1 (Public Review): 

Summary: 

The study by Klug et al. investigated the pathway specificity of corticostriatal projections, focusing on two cortical regions. Using a G-deleted rabies system in D1-Cre and A2a-Cre mice to retrogradely deliver channelrhodopsin to cortical inputs, the authors found that M1 and MCC inputs to direct and indirect pathway spiny projection neurons (SPNs) are both partially segregated and asymmetrically overlapping. In general, corticostriatal inputs that target indirect pathway SPNs are likely to also target direct pathway SPNs, while inputs targeting direct pathway SPNs are less likely to also target indirect pathway SPNs. Such asymmetric overlap of corticostriatal inputs has important implications for how the cortex itself may determine striatal output. Indeed, the authors provide behavioral evidence that optogenetic activation of M1 or MCC cortical neurons that send axons to either direct or indirect pathway SPNs can have opposite effects on locomotion and different effects on action sequence execution. The conclusions of this study add to our understanding of how cortical activity may influence striatal output and offer important new clues about basal ganglia function. 

The conceptual conclusions of the manuscript are supported by the data, but the details of the magnitude of afferent overlap and causal role of asymmetric corticostriatal inputs on behavioral outcomes were not yet fully resolved. 

We appreciate the reviewer’s thoughtful understanding and acknowledgment that the conceptual conclusion of asymmetric projections from the cortex to the striatum is well supported by our data. We also recognize the importance of further elucidating the extent of afferent overlap and the causal contributions of asymmetric corticostriatal inputs to behavioral outcomes. However, we respectfully note that current technical limitations pose significant challenges to addressing these questions with high precision.

In response to the reviewer’s comments, we have now clarified the sample size, added proper analysis and elaborated on the experimental design to ensure that our conclusions are presented more transparently and are more accessible to the reader.

After virally labeling either direct pathway (D1) or indirect pathway (D2) SPNs to optogenetically tag pathway-specific cortical inputs, the authors report that a much larger number of "non-starter" D2-SPNs from D2-SPN labeled mice responded to optogenetic stimulation in slices than "non-starter" D1 SPNs from D1-SPN labeled mice did. Without knowing the relative number of D1 or D2 SPN starters used to label cortical inputs, it is difficult to interpret the exact meaning of the lower number of responsive D2-SPNs in D1 labeled mice (where only ~63% of D1-SPNs themselves respond) compared to the relatively higher number of responsive D1-SPNs (and D2-SPNs) in D2 labeled mice. While relative differences in connectivity certainly suggest that some amount of asymmetric overlap of inputs exists, differences in infection efficiency and ensuing differences in detection sensitivity in slice experiments make determining the degree of asymmetry problematic. 

Thank you for highlighting this point. As it lies at the core of our manuscript, we agree that it is essential to present it clearly and convincingly. As shown by the statistics (Fig. 2B-F), non-starter D1- and D2-SPNs appear to receive fewer projections from D1-projecting cortical neurons (Input D1-record D1, 0.63; Input D1-record D2, 0.40) compared to D2-projecting cortical neurons (Input D2 - record D1, 0.73; Input D2 -record D2, 0.79).

While it is not technically feasible to quantify the number of infected cells in brain slices following electrophysiological recordings, we addressed this limitation by collecting data from multiple animals and restricting recordings to cells located within the injection sites. In Figure 2D, we used 7 mice in the D1-projecting to D1 EGFP(+) group, 8 mice in the D1-projecting to D2 EGFP(-) group, 10 mice in the D2-projecting to D2 EGFP(+) group, and 8 mice in the D2-projecting to D1 EGFP(-) group. In Figure 2G, the group sizes were as follows: 8 mice in the D1-projecting to D2 EGFP(+) group, 7 mice in the D1-projecting to D1 EGFP(-) group, 8 mice in the D2-projecting to D1 EGFP(+) group, and 10 mice in the D2-projecting to D2 EGFP(-) group. In both panels, connection ratios were compared using Fisher’s exact test. Comparisons were then made across experimental groups. Furthermore, as detailed in our Methods section (page 20, line 399-401), we assessed cortical expression levels prior to performing whole-cell recordings. Taken together, these precautions help ensure that the calculated connection ratios are unlikely to be confounded by differences in infection efficiency.

It is also unclear if retrograde labeling of D1-SPN- vs D2-SPN- targeting afferents labels the same densities of cortical neurons. This gets to the point of specificity in the behavioral experiments. If the target-based labeling strategies used to introduce channelrhodopsin into specific SPN afferents label significantly different numbers of cortical neurons, might the difference in the relative numbers of optogenetically activated cortical neurons itself lead to behavioral differences? 

Thank you for bringing this concern to our attention. While optogenetic manipulation has become a widely adopted tool in functional studies of neural circuits, it remains subject to several technical limitations due to the nature of its implementation. Factors such as opsin expression efficiency, optic fiber placement, light intensity, stimulation spread, and other variables can all influence the specificity and extent of neuronal activation or inhibition. As such, rigorous experimental controls are essential when interpreting the outcomes of optogenetic experiments.

In our study, we verified both the expression of channelrhodopsin in D1- or D2-projecting cortical neurons and the placement of the optic fiber following the completion of behavioral testing. To account for variability, we compared the behavioral effects of optogenetic stimulation within the same animals, stimulated versus non-stimulated conditions, as shown in Figures 3 and 4. Moreover, Figure S3 includes important controls that rule out the possibility that the behavioral effects observed were due to direct activation of D1- or D2-SPNs in striatum or to light alone in the cortex.

An additional point worth emphasizing is that the behavioral effects observed in the open field and ICSS tests cannot be attributed to differences in the number of neurons activated. Specifically, activation of D1-projecting cortical neurons promoted locomotion in the open field, whereas activation of D2-projecting cortical neurons did not. However, in the ICSS test, activation of both D1- and D2-projecting cortical neurons reinforced lever pressing. Given that only D1-SPN activation, but not D2-SPN activation, supports ICSS behavior, these effects are unlikely to result merely from differences in the number of neurons recruited.

This rationale underlies our use of multiple behavioral paradigms to examine the functions of D1- and D2-projecting cortical neurons. By assessing behavior across distinct tasks, we aimed to approach the question from multiple angles and reduce the likelihood of spurious or confounding effects influencing our interpretation.

In general, the manuscript would also benefit from more clarity about the statistical comparisons that were made and sample sizes used to reach their conclusions.

We thank the reviewer for the valuable suggestion to improve the manuscript. In response, we have made the following changes and provided additional clarification:

(1) In Figure 2D, we used 7 mice in the D1-projecting to D1 EGFP(+) group, 8 mice in the D1-projecting to D2 EGFP(-) group, 10 mice in the D2-projecting to D2 EGFP(+) group, and 8 mice in the D2-projecting to D1 EGFP(-) group. In Figure 2G, the group sizes were as follows: 8 mice in the D1-projecting to D2 EGFP(+) group, 7 mice in the D1-projecting to D1 EGFP(-) group, 8 mice in the D2-projecting to D1 EGFP(+) group, and 10 mice in the D2-projecting to D2 EGFP(-) group. In both panels, connection ratios were compared using Fisher’s exact test.

(2) In Figure 3, we reanalyzed the data in panels O, P, R, and S using permutation tests to assess whether each individual group exhibited a significant ICSS learning effect. The figure legend has been revised accordingly as follows:

(O-P) D1-SPN (red) but not D2-SPN stimulation (black) drives ICSS behavior in both the DMS (O: D1, n = 6, permutation test, slope = 1.5060, P = 0.0378; D2, n = 5, permutation test, slope = -0.2214, P = 0.1021; one-tailed Mann Whitney test, Day 7 D1 vs. D2, P = 0.0130) and the DLS (P: D1, n = 6, permutation test, slope = 28.1429, P = 0.0082; D2, n = 5, permutation test, slope = -0.3429, P = 0.0463; one-tailed Mann Whitney test, Day 7 D1 vs. D2, P = 0.0390). *, P < 0.05. (Q) Timeline of helper virus injections, rabies-ChR2 injections and optogenetic stimulation for ICSS behavior. (R-S) Optogenetic stimulation of the cortical neurons projecting to either D1- or D2-SPNs induces ICSS behavior in both the MCC (R: MCC-D1, n = 5, permutation test, Day1-Day7, slope = 2.5857, P = 0.0034; MCC-D2, n = 5, Day2-Day7, permutation test, slope = 1.4229, P = 0.0344; no significant effect on Day7, MCC-D1 vs. MCC-D2,  two-tailed Mann Whitney test, P = 0.9999) and the M1 (S: M1-D1, n = 5, permutation test, Day1-Day7, slope = 1.8214, P = 0.0259; M1-D2, n = 5, Day1-Day7, permutation test, slope = 1.8214, P = 0.0025; no significant effect on Day7, M1-D1 vs. M1-D2, two-tailed Mann Whitney test, P = 0.3810). n.s., not statistically significant.

(3) In Figure 4, we have added a comparison against a theoretical percentage change of zero to better evaluate the net effect of each manipulation. The results showed that in Figure 4D, optogenetic stimulation of D1-projecting MCC neurons significantly increased the pressing rate, whereas stimulation of D2-projecting MCC neurons did not (MCC-D1: n = 8, one-sample two-tailed t-test, t = 2.814, P = 0.0131; MCC-D2: n = 7, t = 0.8481, P = 0.4117). In contrast, in Figure 4H, optogenetic stimulation of both D1- and D2-projecting M1 neurons significantly increased the sequence press rate (M1-D1: n = 6, one-sample two-tailed Wilcoxon signed-rank test, P = 0.0046; M1-D2: n = 7, P = 0.0479).

Reviewer #2 (Public Review):

Summary: 

Klug et al. use monosynaptic rabies tracing of inputs to D1- vs D2-SPNs in the striatum to study how separate populations of cortical neurons project to D1- and D2-SPNs. They use rabies to express ChR2, then patch D1-or D2-SPNs to measure synaptic input. They report that cortical neurons labeled as D1-SPN-projecting preferentially project to D1-SPNs over D2-SPNs. In contrast, cortical neurons labeled as D2-SPN-projecting project equally to D1- and D2-SPNs. They go on to conduct pathway-specific behavioral stimulation experiments. They compare direct optogenetic stimulation of D1- or D2-SPNs to stimulation of MCC inputs to DMS and M1 inputs to DLS. In three different behavioral assays (open field, intra-cranial self-stimulation, and a fixed ratio 8 task), they show that stimulating MCC or M1 cortical inputs to D1-SPNs is similar to D1-SPN stimulation, but that stimulating MCC or M1 cortical inputs to D2-SPNs does not recapitulate the effects of D2-SPN stimulation (presumably because both D1- and D2-SPNs are being activated by these cortical inputs). 

Strengths: 

Showing these same effects in three distinct behaviors is strong. Overall, the functional verification of the consequences of the anatomy is very nice to see. It is a good choice to patch only from mCherry-negative non-starter cells in the striatum.

Thank you for your profound understanding and appreciation of our manuscript’s design and the methodologies employed. In the realm of neuroscience, quantifying synaptic connections is a formidable challenge. While the roles of the direct and indirect pathways in motor control have long been explored, the mechanism by which upstream cortical inputs govern these pathways remains shrouded in mystery at the circuitry level.

In the ‘Go/No-Go’ model, the direct and indirect pathways operate antagonistically; in contrast, the ‘Co-activation’ model suggests that they work cooperatively to orchestrate movement. These distinct theories raise a compelling question: Do these two pathways receive inputs from the same upstream cortical neurons, or are they modulated by distinct subpopulations? Answering this question could provide vital clues as to whether these pathways collaborate or operate independently.

Previous studies have revealed both differences and similarities in the cortical inputs to direct and indirect pathways at population level. However, our investigation delves deeper to understand how a singular cortical input simultaneously drives these pathways, or might it regulate one pathway through distinct subpopulations? To address this, we employed rabies virus–mediated retrograde tracing from D1- or D2-SPNs and recorded non-starter SPNs to determine if they receive the same inputs as the starter SPNs. This approach allowed us to calculate the connection ratio and estimate the probable connection properties.

Weaknesses: 

One limitation is that all inputs to SPNs are expressing ChR2, so they cannot distinguish between different cortical subregions during patching experiments. Their results could arise because the same innervation patterns are repeated in many cortical subregions or because some subregions have preferential D1-SPN input while others do not.

Thank you for raising this thoughtful concern. It is indeed not feasible to restrict ChR2 expression to a specific cortical region using the first-generation rabies-ChR2 system alone. A more refined approach would involve injecting Cre-dependent TVA and RG into the striatum of D1- or A2A-Cre mice, followed by rabies-Flp infection. Subsequently, a Flp-dependent ChR2 virus could be injected into the MCC or M1 to selectively label D1- or D2-projecting cortical neurons. This strategy would allow for more precise targeting and address many of the current limitations.

However, a significant challenge lies in the cytotoxicity associated with rabies virus infection. Neuronal health begins to deteriorate substantially around 10 days post-infection, which provides an insufficient window for robust Flp-dependent ChR2 expression. We have tested several new rabies virus variants with extended survival times (Chatterjee et al., 2018; Jin et al., 2024), but unfortunately, they did not perform effectively or suitably in the corticostriatal systems we examined.

In our experimental design, the aim is to delineate the connectivity probabilities to D1 or D2-SPNs from cortical neurons. Our hypothesis considered includes the possibility that similar innervation patterns could occur across multiple cortical subregions, or that some subregions might show preferential input to D1-SPNs while others do not, or a combination of both scenarios. This leads us to perform a series behavior test that using optogenetic activation of the D1- or D2-projecting cortical populations to see which could be the case.

In the cortical areas we examined, MCC and M1, during behavioral testing, there is consistency with our electrophysiological results. Specifically, when we stimulated the D1-projecting cortical neurons either in MCC or in M1, mice exhibited facilitated local motion in open field test, which is the same to the activation of D1 SPNs in the striatum along (MCC: Fig 3C & D vs. I; M1: Fig 3F & G vs. L). Conversely, stimulation of D2-projecting MCC or M1 cortical neurons resulted in behavioral effects that appeared to combine characteristics of both D1- and D2-SPNs activation in the striatum (MCC: Fig 3C & D vs. J; M1: Fig 3F & G vs. M). The similar results were observed in the ICSS test. Our interpretation of these results is that the activation of D1-projecting neurons in the cortex induces behavior changes akin to D1 neuron activation, while activation of D2-projecting neurons in the cortex leads to a combined effect of both D1 and D2 neuron activation. This suggests that at least some cortical regions, the ones we tested, follow the hypothesis we proposed.

There are also some caveats with respect to the efficacy of rabies tracing. Although they only patch non-starter cells in the striatum, only 63% of D1-SPNs receive input from D1-SPN-projecting cortical neurons. It's hard to say whether this is "high" or "low," but one question is how far from the starter cell region they are patching. Without this spatial indication of where the cells that are being patched are relative to the starter population, it is difficult to interpret if the cells being patched are receiving cortical inputs from the same neurons that are projecting to the starter population. Convergence of cortical inputs onto SPNs may vary with distance from the starter cell region quite dramatically, as other mapping studies of corticostriatal inputs have shown specialized local input regions can be defined based on cortical input patterns (Hintiryan et al., Nat Neurosci, 2016, Hunnicutt et al., eLife 2016, Peters et al., Nature, 2021).

This is a valid concern regarding anatomical studies. Investigating cortico-striatal connectivity at the single-cell level remains technically challenging due to current methodological limitations. At present, we rely on rabies virus-mediated trans-synaptic retrograde tracing to identify D1- or D2-projecting cortical populations. This anatomical approach is coupled with ex vivo slice electrophysiology to assess the functional connectivity between these projection-defined cortical neurons and striatal SPNs. This enables us to quantify connection ratios, for example, the proportion of D1-projecting cortical neurons that functionally synapse onto non-starter D1-SPNs.

To ensure the robustness of our conclusions, it is essential that both the starter cells and the recorded non-starter SPNs receive comparable topographical input from the cortex and other brain regions. Therefore, we carefully designed our experiments so that all recorded cells were located within the injection site, were mCherry-negative (i.e., non-starter cells), and were surrounded by ChR2-mCherry-positive neurons. This configuration ensured that the distance between recorded and starter cells did not exceed 100 µm, maintaining close anatomical proximity and thereby preserving the likelihood of shared cortical innervation within the examined circuitry.

These methodological details are also described in the section on ex vivo brain slice electrophysiology, specifically in the Methods section, lines 396–399:

“D1-SPNs (eGFP-positive in D1-eGFP mice, or eGFP-negative in D2-eGFP mice) or D2-SPNs (eGFP-positive in D2-eGFP mice, or eGFP-negative in D1-eGFP mice) that were ChR2-mCherry-negative, but in the injection site and surrounded by cells expressing ChR2-mCherry were targeted for recording.”

This experimental strategy was implemented to control for potential spatial biases and to enhance the interpretability of our connectivity measurements.

A caveat for the optogenetic behavioral experiments is that these optogenetic experiments did not include fluorophore-only controls.

Thank you for bringing this to our attention. A fluorophore-only control is indeed a valuable negative control, commonly used to rule out effects caused by light exposure independent of optogenetic manipulation. In this study, however, comparisons were made between light-on and light-off conditions within the same animal. This within-subject design, as employed in recent studies (Geddes et al., 2018; Zhu et al., 2025), is considered sufficient to isolate the effects of optogenetic manipulation.

Furthermore, as shown in Figure S3, we conducted an additional control experiment in which optogenetic stimulation was applied to M1, while ensuring that ChR2 expression was restricted to the striatum via targeted viral infection. This approach serves as a functional equivalent to the control you suggested. Importantly, we observed no effects that could be attributed solely to light exposure, further supporting the conclusion that the observed outcomes in our main experiments are due to targeted optogenetic manipulation, rather than confounding effects of illumination.

Lastly, by employing an in-animal comparison, measuring changes between stimulated and non-stimulated trials, we account for subject-specific variability and strengthen the interpretability of our findings.

Another point of confusion is that other studies (Cui et al, J Neurosci, 2021) have reported that stimulation of D1-SPNs in DLS inhibits rather than promotes movement.

Thank you for bringing the study by Cui and colleagues to our attention. While that study has generated some controversy, other independent investigations have demonstrated that activation of D1-SPNs in DLS facilitates local motion and lever-press behaviors (Dong et al., 2025; Geddes et al., 2018; Kravitz et al., 2010).

It is still worth to clarify. The differences in behavioral outcomes observed between our study and that of Cui et al. may be attributable to several methodological factors, including differences in both the stereotaxic targeting coordinates and the optical fiber specifications used for stimulation.

Specifically, in our experiments, the dorsomedial striatum (DMS) was targeted at coordinates AP +0.5 mm, ML ±1.5 mm, DV –2.2 mm, and the DLS at AP +0.5 mm, ML ±2.5 mm, DV –2.2 mm. In contrast, Cui et al. targeted the DMS at AP +0.9 mm, ML ±1.4 mm, DV –3.0 mm and the DLS at AP +0.7 mm, ML ±2.3 mm, DV –3.0 mm. These coordinates correspond to sites that are slightly more rostral and ventral compared to our own. Even subtle differences in anatomical targeting can result in activation of distinct neuronal subpopulations, which may account for the differing behavioral effects observed during optogenetic stimulation.

In addition, the optical fibers used in the two studies varied considerably. We employed fibers with a 200 µm core diameter and a numerical aperture (NA) of 0.37, whereas Cui et al. used fibers with a 250 µm core diameter and a higher NA of 0.66. The combination of a larger core and higher NA in their setup implies a broader spatial spread and deeper tissue penetration of light, likely resulting in activation of a larger neural volume. This expanded volume of stimulation may have engaged additional neural circuits not recruited in our experiments, further contributing to the divergent behavioral outcomes. Taken together, these differences in targeting and photostimulation parameters are likely key contributors to the distinct effects reported between the two studies.

Reviewer #3 (Public Review): 

In the manuscript by Klug and colleagues, the investigators use a rabies virus-based methodology to explore potential differences in connectivity from cortical inputs to the dorsal striatum. They report that the connectivity from cortical inputs onto D1 and D2 MSNs differs in terms of their projections onto the opposing cell type, and use these data to infer that there are differences in cross-talk between cortical cells that project to D1 vs. D2 MSNs. Overall, this manuscript adds to the overall body of work indicating that there are differential functions of different striatal pathways which likely arise at least in part by differences in connectivity that have been difficult to resolve due to difficulty in isolating pathways within striatal connectivity and several interesting and provocative observations were reported. Several different methodologies are used, with partially convergent results, to support their main points.

However, I have significant technical concerns about the manuscript as presented that make it difficult for me to interpret the results of the experiments. My comments are below.

Major:

There is generally a large caveat to the rabies studies performed here, which is that both TVA and the ChR2-expressing rabies virus have the same fluorophore. It is thus essentially impossible to determine how many starter cells there are, what the efficiency of tracing is, and which part of the striatum is being sampled in any given experiment. This is a major caveat given the spatial topography of the cortico-striatal projections. Furthermore, the authors make a point in the introduction about previous studies not having explored absolute numbers of inputs, yet this is not at all controlled in this study. It could be that their rabies virus simply replicates better in D1-MSNs than D2-MSNs. No quantifications are done, and these possibilities do not appear to have been considered. Without a greater standardization of the rabies experiments across conditions, it is difficult to interpret the results.

We thank the reviewer for raising these questions, which merit further discussion.

Firstly, the primary aim of our study is to investigate the connectivity of the corticostriatal pathway. Given the current technical limitations, it is not feasible to trace all the striatal SPNs connected to a single cortical neuron. Therefore, we approached this from the opposite direction, starting from D1- or D2-SPNs to retrogradely label upstream cortical neurons, and then identifying their connected SPNs via functional synaptic recordings. To achieve this, we employed the only available transsynaptic retrograde method: rabies virus-mediated tracing. Because we crossed D1- or D2-GFP mice with D1- or A2A-Cre mice to identify SPN subtypes during electrophysiological recordings, the conventional rabies-GFP system could not be used to distinguish starter cells without conflicting with the GFP labeling of SPNs. To overcome this, we tagged ChR2 expression with mCherry. In this setup, we recorded from mCherry-negative D1- or D2-SPNs within the injection site and surrounded by mCherry-positive neurons. This ensures that the recorded neurons are topographically matched to the starter cell population and receive input from the same cortical regions. We acknowledge that TVA-only and ChR2-expressing cells are both mCherry-positive and therefore indistinguishable in our system. As such, mCherry-positive cells likely comprise a mixture of starter cells and TVA-only cells, representing a somewhat broader population than starter cells alone. Nevertheless, by restricting recordings to mCherry-negative SPNs within the injection site, it is ensured that our conclusions about functional connectivity remain valid and aligned with the primary objective of this study.

Secondly, if rabies virus replication were significantly more efficient in D1-SPNs than in D2-SPNs, this would likely result in a higher observed connection probability in the D1-projecting group. However, we used consistent genetic strategies across all groups: D1-SPNs were defined as GFP-positive in D1-GFP mice and GFP-negative in D2-GFP mice, with D2-SPNs defined analogously. Recordings from both D1- and D2-SPNs were performed using the same methodology and under the same injection conditions within the same animals. This internal control helps mitigate the possibility that differential rabies infection efficiency biased our results.

With these experimental safeguards in place, we found that 40% of D2-SPNs received input from D1-SPN-projecting cortical neurons, while 73% of D1-SPNs received input from D2-SPN-projecting cortical neurons. Although the ideal scenario would involve an even larger sample size to refine these estimates, the technical demands of post-rabies-infection electrophysiological recordings inherently limit throughput. Nonetheless, our approach represents the most feasible and accurate method currently available, and provides a significant advance in characterizing the functional connectivity within corticostriatal circuits.

The authors claim using a few current clamp optical stimulation experiments that the cortical cells are healthy, but this result was far from comprehensive. For example, membrane resistance, capacitance, general excitability curves, etc are not reported. In Figure S2, some of the conditions look quite different (e.g., S2B, input D2-record D2, the method used yields quite different results that the authors write off as not different). Furthermore, these experiments do not consider the likely sickness and death that occurs in starter cells, as has been reported elsewhere. The health of cells in the circuit is overall a substantial concern that alone could invalidate a large portion, if not all, of the behavioral results. This is a major confound given those neurons are thought to play critical roles in the behaviors being studied. This is a major reason why first-generation rabies viruses have not been used in combination with behavior, but this significant caveat does not appear to have been considered, and controls e.g., uninfected animals, infected with AAV helpers, etc, were not included.

We understand and appreciate the reviewer’s concern regarding the potential cytotoxicity of rabies virus infection. Indeed, this is a critical consideration when interpreting functional connectivity data. We have tested several newer rabies virus variants reported to support extended survival times (Chatterjee et al., 2018; Jin et al., 2024), but unfortunately, these variants did not perform reliably in the corticostriatal circuits we examined.

Given these limitations, we relied on the rabies virus approach originally developed by Osakada et al. (Osakada et al., 2011), which demonstrated that neurons infected with rabies virus expressing ChR2 remain both viable and functional up to at least 10 days post-infection (Fig. 3, cited below). In our own experiments, we further validated the health and viability of cortical neurons, the presynaptic partners of SPNs, particularly around day 7 post-infection.

To minimize the risk of viral toxicity, we performed ex vivo slice recordings within a conservative time window, between 4 and 8 days after infection, when the health of labeled neurons is well maintained. Moreover, the recorded SPNs were consistently mCherry-negative, indicating they were not directly infected by rabies virus, thus further reducing the likelihood of recording from compromised cells.

Taken together, these steps help ensure that our synaptic recordings reflect genuine functional connectivity, rather than artifacts of viral toxicity. We hope this clarifies the rationale behind our experimental design.

For the behavioral tests, including a naïve uninfected group and an AAV helper virus-only group as negative controls could be beneficial to isolate the specific impact of rabies virus infection. However, our primary focus is on the activation of selected presynaptic inputs to D1- or D2-SPNs by optogenetic method. Therefore, comparing stimulated versus non-stimulated trials within the same animal offers more direct and relevant results for our study objectives.

It is also important to note that the ICSS test is particularly susceptible to the potential cytotoxic effects of rabies virus, as it spans a relatively extended period, from Day 4 to Day 12 post-infection. To mitigate this issue, we focused our analysis on the first 7 days of ICSS testing, thereby keeping the behavioral observations within 10 days post-rabies injection. This approach minimizes potential confounds from rabies-induced neurotoxicity while still capturing the relevant behavioral dynamics. Accordingly, we have revised Figure 3 and updated the statistical analyses to reflect this adjustment.

The overall purity (e.g., EnvA-pseudotyping efficiency) of the RABV prep is not shown. If there was a virus that was not well EnvA-pseudotyped and thus could directly infect cortical (or other) inputs, it would degrade specificity.

We agree that anatomical specificity is crucial for accurately labeling inputs to defined SPN populations in our study. The rabies virus strain employed here has been rigorously validated for its specificity in numerous previous studies from our group and others (Aoki et al., 2019; Klug et al., 2018; Osakada et al., 2011; Smith et al., 2016; Wall et al., 2013; Wickersham et al., 2007). For example, in a recent study by Aoki et al. (Aoki et al., 2019), we tested the same rabies virus strain by co-injecting the glycoprotein-deleted rabies virus and the TVA-expressing helper virus, without glycoprotein expressing AAV, into the SNr. As shown in Figure S1 (related to Figure 2), GFP expression was restricted to starter cells within the SNr, with no evidence of transsynaptic labeling in upstream regions such as the striatum, EPN, GPe, or STN (see panels F–H). These findings provide strong evidence that the rabies virus used in our experiments is properly pseudotyped and exhibits high specificity for starter cell labeling without off-target spread.

We appreciate the reviewer’s emphasis on specificity, and we hope this clarification further supports the reliability of our anatomical tracing approach.

While most of the study focuses on the cortical inputs, in slice recordings, inputs from the thalamus are not considered, yet likely contribute to the observed results. Related to this, in in vivo optogenetic experiments, technically, if the thalamic or other inputs to the dorsal striatum project to the cortex, their method will not only target cortical neurons but also terminals of other excitatory inputs. If this cannot be ruled it, stating that the authors are able to selectively activate the cortical inputs to one or the other population should be toned down.

We agree with the reviewer that the thalamus is also a significant source of excitatory input to the striatum. However, current techniques do not allow for precise and exclusive labeling of upstream neurons in a given brain region, such as the cortex or thalamus. This technical limitation indeed makes it difficult to definitively determine whether inputs from these regions follow the same projection rules. Despite this, our findings show that stimulation of defined cortical populations, specifically, D1- or D2-projecting neurons in MCC and M1, elicits behavioral outcomes that closely mirror those observed in our ex vivo slice recordings, providing strong support for the cortical origin of the effects we observed.

In our in vivo optogenetic experiments, we acknowledge that stimulating a specific cortical region may also activate axonal terminals from rabies-infected cortical or thalamic neurons. While somatic stimulation is generally more effective than terminal stimulation, we recognize the possibility that terminals on non-rabies-traced cortical neurons could be activated through presynaptic connections. To address this, we considered the finding of a previous study (Cruikshank et al., 2010), which demonstrated that while brief optogenetic stimulation (0.05 ms) of thalamo-cortical terminals can elicit few action potentials in postsynaptic cortical neurons, sustained terminal stimulation (500 ms) also results in only transient postsynaptic firing rather than prolonged activation (Fig. 3C, cited below). This suggests that cortical neurons exhibit only short-lived responses to continuous presynaptic stimulation of thalamic origin.

In comparison, our behavioral paradigms employed prolonged optogenetic stimulation protocols- 20 Hz, 10 ms pulses for 15 s (open-field test), 1 s (ICSS), and 8 s (FR4/8)—which more closely resemble sustained stimulation conditions. Given these parameters, and the robust behavioral responses observed, it means that the effects are primarily mediated by activation of rabies-labeled, ChR2-expressing D1- or D2-projecting cortical neurons rather than indirect activation through thalamic input.

We appreciate the reviewer’s valuable comment, and we have now incorporated this point into the revised manuscript (page 13, line 265 to 275) to more clearly address the potential contribution of thalamic inputs in our experimental design.

The statements about specificity of connectivity are not well-founded. It may be that in the specific case where they are assessing outside of the area of injections, their conclusions may hold (e.g., excitatory inputs onto D2s have more inputs onto D1s than vice versa). However, how this relates to the actual site of injection is not clear. At face value, if such a connectivity exists, it would suggest that D1-MSNs receive substantially more overall excitatory inputs than D2s. It is thus possible that this observation would not hold over other spatial intervals. This was not explored and thus the conclusions are over-generalized. e.g., the distance from the area of red cells in the striatum to recordings was not quantified, what constituted a high level of cortical labeling was not quantified, etc. Without more rigorous quantification of what was being done, it is difficult to interpret the results. 

We sincerely thank the reviewer for the thoughtful comments and critical insights into our interpretation of connectivity data. These concerns are valid and provide an important opportunity to clarify and reinforce our experimental design and conclusions.

Firstly, as described in our previous response, all patched neurons were carefully selected to be within the injection site and in close proximity to ChR2-mCherry-positive cells. Specifically, the estimated distance from each recorded neuron to the nearest starter cells did not exceed 100 µm. This design choice was made to minimize variability associated with spatial distance or heterogeneity in viral expression, thereby allowing for a more consistent sampling of putatively connected neurons.

Secondly, quantifying both the number of starter and input neurons would, in principle, provide a more comprehensive picture of connectivity. However, given the technical limitations of the current approach particularly when combining rabies tracing with functional recordings it is not feasible to obtain such precise cell counts. Instead, we focused on connection ratios derived from targeted electrophysiological recordings, which offer a reliable and practical means of estimating connectivity within these defined circuits.

Thirdly, regarding the potential influence of rabies-labeled neurons beyond the immediate recording site: while we acknowledge that rabies tracing labels a broad set of upstream neurons, our analysis was confined to a well-defined and localized area. The analogy we find helpful here is that of a spotlight - our recordings were restricted to the illuminated region directly under the beam, where the projection pattern is fixed and interpretable, regardless of what lies outside that area. Although we cannot fully account for all possible upstream connections, our methodology was designed to minimize variability and maintain consistency in the region of interest, which we believe supports the robustness of our conclusions in the ex vivo slice recording experiment.

We hope this additional explanation addresses the reviewer’s concerns and helps clarify the rationale of our experimental strategy.

The results in figure 3 are not well controlled. The authors show contrasting effects of optogenetic stimulation of D1-MSNs and D2-MSNs in the DMS and DLS, results which are largely consistent with the canon of basal ganglia function. However, when stimulating cortical inputs, stimulating the inputs from D1-MSNs gives the expected results (increased locomotion) while stimulating putative inputs to D2-MSNs had no effect. This is not the same as showing a decrease in locomotion - showing no effect here is not possible to interpret.

We apologize for any confusion and appreciate the opportunity to clarify this point. Our electrophysiological recordings demonstrated that D1-projecting cortical neurons preferentially innervate D1-SPNs in the striatum, whereas D2-projecting cortical neurons provide input to both D1- and D2-SPNs, without a clear preference. These synaptic connectivity patterns are further supported by our behavioral experiments: optogenetic stimulation of D1-projecting neurons in cortical areas such as MCC and M1 led to behavioral effects consistent with direct D1-SPN activation. In contrast, stimulation of D2-projecting cortical neurons produced behavioral outcomes that appeared to reflect a mixture of both D1- and D2-SPN activation.

We acknowledge that interpreting negative behavioral findings poses inherent challenges, as it is difficult to distinguish between a true lack of effect and insufficient experimental manipulation. To mitigate this, we ensured that all animals included in the analysis exhibited appropriate viral expression and correctly placed optic fibers in the targeted regions. These controls help to confirm that the observed behavioral effects - or lack thereof - are indeed due to the activation of the intended neuronal populations rather than technical artifacts such as weak expression or fiber misplacement.

As shown in Author response image 1 below, our verification of virus expression and fiber positioning confirms effective targeting in MCC and M1 of A2A-Cre mice. Therefore, we interpret the negative behavioral outcomes as meaningful consequences of specific neural circuit activation.

Author response image 1.

Confocal image from A2A-Cre mouse showing targeted optogenetic stimulation of D2-projecting cortical neurons in MCC or M1. ChR2-mCherry expression highlights D2-projecting neurons, selectively labeled via rabies-mediated tracing. Optic fiber placement is confirmed above the cortical region of interest. Image illustrates robust expression and anatomical specificity necessary for pathway-selective stimulation in behavioral assays.

In light of their circuit model, the result showing that inputs to D2-MSNs drive ICSS is confusing. How can the authors account for the fact that these cells are not locomotor-activating, stimulation of their putative downstream cells (D2-MSNs) does not drive ICSS, yet the cortical inputs drive ICSS? Is the idea that these inputs somehow also drive D1s? If this is the case, how do D2s get activated, if all of the cortical inputs tested net activate D1s and not D2s? Same with the results in figure 4 - the inputs and putative downstream cells do not have the same effects. Given the potential caveats of differences in viral efficiency, spatial location of injections, and cellular toxicity, I cannot interpret these experiments.

We apologize for any confusion in our previous explanation. In our behavioral experiments, the primary objective was to determine whether activation of D1- or D2-projecting cortical neurons would produce behavioral outcomes distinct from those observed with pure D1 or D2 activation.

Our findings show that stimulation of D1-projecting cortical neurons produced behavioral effects closely resembling those of selective D1 activation in both open field and ICSS tests. This is consistent with our slice recording data, which revealed that D1-projecting cortical neurons exhibit a higher connection probability with D1-SPNs than with D2-SPNs.

In contrast, interpreting the effects of D2-projecting cortical neuron stimulation is inherently more nuanced. In the open field test, activation of these neurons did not significantly modulate local motion. This could reflect a balanced influence of D1 activation, which facilitates movement, and D2 activation, which suppresses it - resulting in a net neutral behavioral outcome. In the ICSS test, the absence of a strong reinforcement effect typically associated with D2 activation, combined with partial reinforcement likely due to concurrent D1 activation, suggests that stimulation of D2-projecting neurons produces a mixed behavioral signal. This outcome supports the interpretation that these neurons synapse onto both D1- and D2-SPNs, leading to a blended behavioral response that differs from selective D1 or D2 activation alone.

Together, these two behavioral assays offer complementary perspectives, providing a more complete view of how projection-specific cortical inputs influence striatal output and behavior.

In Figure 4 of the current manuscript (as cited below), we show that optogenetic activation of MCC neurons projecting to D1-SPNs facilitates sequence lever pressing, whereas activation of MCC neurons projecting to D2-SPNs does not induce significant behavioral changes. Conversely, activation of M1 neurons projecting to either D1- or D2-SPNs enhances lever pressing sequences. These observations align with our prior findings (Geddes et al., 2018; Jin et al., 2014), where we demonstrated that in the striatum, D1-SPN activation facilitates ongoing lever pressing, whereas D2-SPN activation is more involved in suppressing ongoing actions and promoting transitions between sub-sequences, shown in Fig. 4 from (Geddes et al., 2018; Jin et al., 2014) and Fig. 5K from (Jin et al., 2014) . Taken together, the facilitation of lever pressing by D1-projecting MCC and M1 neurons is consistent with their preferential connectivity to D1-SPNs and their established behavioral role.

What is particularly intriguing, though admittedly more complex, is the behavioral divergence observed upon activation of D2-SPN-projecting cortical neurons. Activation of D2-projecting MCC neurons does not alter lever pressing, possibly reflecting a counterbalancing effect from concurrent D1- and D2-SPN activation. In contrast, stimulation of D2-projecting M1 neurons facilitates lever pressing, albeit less robustly than their D1-projecting counterparts. This discrepancy may reflect regional differences in striatal targets, DMS for MCC versus DLS for M1, as also supported by our open field test results. Furthermore, our recent findings (Zhang et al., 2025) show that synaptic strength from Cg to D2-SPNs is stronger than to D1-SPNs, whereas the M1 pathway exhibits the opposite pattern. These data suggest that beyond projection ratios, synaptic strength also shapes cortico-striatal functional output. Thus, stronger D2-SPN synapses in the DMS may offset D1-SPN activation during MCC-D2 stimulation, dampening lever pressing increase. Conversely, weaker D2 synapses in the DLS may permit M1-D2 projections to facilitate behavior more readily.

In summary, the behavioral outcomes of our optogenetic manipulations support the proposed asymmetric cortico-striatal connectivity model. While the effects of D2-projecting neurons are not uniform, they reflect varying balances of D1 and D2-SPN influence, which further underscores the asymmetrical connections of cortical inputs to the striatum.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors): 

(1) What are the sample sizes for Fig S2? Some trends that are listed as nonsignificant look like they may just be underpowered. Related to this point, S2C indicates that PPR is statistically similar in all conditions. The traces shown in Figure 2 suggest that PPR is quite different in "Input D1"- vs "Input D2" projections. If there is indeed no difference, the exemplar traces should be replaced with more representative ones to avoid confusion. 

Thank you for your suggestion. The sample size reported in Figure S2 corresponds to the neurons identified as connected in Figure 2. The representative traces shown in Figure 2 were selected based on their close alignment with the amplitude statistics and are intended to reflect typical responses. Given this, it is appropriate to retain the current examples as they accurately illustrate the underlying data.

(2) Previous studies have described that SPN-SPN collateral inhibition is also asymmetric, with D2->D1 SPN connectivity stronger than the other direction. While cortical inputs to D2-SPNs may also strongly innervate D1-SPNs, it would be helpful to speculate on how collateral inhibition may further shape the biases (or lack thereof) reported here. 

This would indeed be an interesting topic to explore. SPN-SPN mutual inhibition and/or interneuron inhibition may also play a role in the functional organization and output of the striatum. In the present study, we focused on the primary layer of cortico-striatal connectivity to examine how cortical neurons selectively connect to the striatal direct and indirect pathways, as these pathways have been shown to have distinct yet cooperative functions. To achieve this, we applied a GABAA receptor inhibitor to isolate only excitatory synaptic currents in SPNs, yielding the relevant results.

To investigate additional circuit organization involving SPN-SPN mutual inhibition, the current available technique would involve single-cell initiated rabies tracing. This approach would help identify the starter SPN and the upstream SPNs that provide input to the starter cell, thereby offering a clearer understanding of the local circuit.

(3) In Fig 3N-S there are no stats confirming that optogenetic stimulation does indeed increase lever pressing in each group (though it obviously looks like it does). It would be helpful to add statistics for this comparison, in addition to the between-group comparisons that are shown. 

We thank the reviewer for this thoughtful suggestion. To assess whether optogenetic stimulation increases lever pressing in each group shown in Figures 3O, 3P, 3R, and 3S, we employed a permutation test (10,000 permutations). This non-parametric statistical method does not rely on assumptions about the underlying data distribution and is particularly appropriate for our analysis given the relatively small sample sizes.

Additionally, in response to Reviewer 3’s concern regarding the potential cytotoxicity of rabies virus affecting behavioral outcomes during in vivo optogenetic stimulation experiments, we focused our analysis on Days 1 through 7 of the ICSS test. This time window remains within 10 days post-rabies infection, a period during which previous studies have reported minimal cytopathic effects (Osakada et al., 2011).

Accordingly, we have updated Figure 3N-S and revised the associated statistical analyses in the figure legend as follows:

(O-P) D1-SPN (red) but not D2-SPN stimulation (black) drives ICSS behavior in both the DMS (O: D1, n = 6, permutation test, slope = 1.5060, P = 0.0378; D2, n = 5, permutation test, slope = -0.2214, P = 0.1021; one-tailed Mann Whitney test, Day 7 D1 vs. D2, P = 0.0130) and the DLS (P: D1, n = 6, permutation test, slope = 28.1429, P = 0.0082; D2, n = 5, permutation test, slope = -0.3429, P = 0.0463; one-tailed Mann Whitney test, Day 7 D1 vs. D2, P = 0.0390). *, P < 0.05. (Q) Timeline of helper virus injections, rabies-ChR2 injections and optogenetic stimulation for ICSS behavior. (R-S) Optogenetic stimulation of the cortical neurons projecting to either D1- or D2-SPNs induces ICSS behavior in both the MCC (R: MCC-D1, n = 5, permutation test, Day1-Day7, slope = 2.5857, P = 0.0034; MCC-D2, n = 5, Day2-Day7, permutation test, slope = 1.4229, P = 0.0344; no significant effect on Day7, MCC-D1 vs. MCC-D2,  two-tailed Mann Whitney test, P = 0.9999) and the M1 (S: M1-D1, n = 5, permutation test, Day1-Day7, slope = 1.8214, P = 0.0259; M1-D2, n = 5, Day1-Day7, permutation test, slope = 1.8214, P = 0.0025; no significant effect on Day7, M1-D1 vs. M1-D2, two-tailed Mann Whitney test, P = 0.3810). n.s., not statistically significant.

We believe this updated analysis and additional context further strengthen the validity of our conclusions regarding the reinforcement effects.

(4) Line 206: mice were trained for "a few more days" is not a very rigorous description. It would be helpful to state the range of additional days of training. 

We thank the reviewer for the suggestion. In accordance with the Methods section, we have now specified the number of days, which is 4 days, in the main text (line 207).

(5) In Fig 4D,H, the statistical comparison is relative modulation (% change) by stimulation of D1- vs D2- projecting inputs. Please show statistics comparing the effect of stimulation on lever presses for each individual condition. For example, is the effect of MCC-D2 stimulation in panel D negative or not significant? 

Thank you for your suggestion. Below are the statistical results, which we have also incorporated into the figure legend for clarity. To assess the net effects of each manipulation, we compared the observed percentage changes with a theoretical value of zero.

In Figure 4D, optogenetic stimulation of D1-projecting MCC neurons significantly increased the pressing rate (MCC-D1, n = 8, one-sample two-tailed t-test, t = 2.814, P = 0.0131), whereas stimulation of D2-projecting MCC neurons did not produce a significant effect (MCC-D2, n = 7, one-sample two-tailed t-test, t = 0.8481, P = 0.4117).

In contrast, Figure 4H shows that optogenetic stimulation of both D1- and D2-projecting M1 neurons significantly increased the sequence press rate (M1-D1, n = 6, one-sample two-tailed Wilcoxon signed-rank test, P = 0.0046; M1-D2, n = 7, one-sample two-tailed Wilcoxon signed-rank test, P = 0.0479).

These analyses help clarify the distinct behavioral effects of manipulating different corticostriatal projections.

(6) Are data in Fig 1G-H from a D1- or A2a- cre mouse? 

The data in Fig 1G-H are from a D1-Cre mouse.

(7) In Fig S3 it looks like there may actually be an effect of 20Hz simulation of D2-SPNs. Though it probably doesn't affect the interpretation. 

As indicated by the statistics, there is a slight, but not statistically significant, decrease in local motion when 20 Hz stimulation is delivered to the motor cortex with ChR2 expression in D2-SPNs in the striatum.

Reviewer #2 (Recommendations For The Authors): 

The rabies tracing is referred to on several occasions as "new" but the reference papers are from 2011, 2013, and 2018. It is unclear what is new about the system used in the paper and what new feature is relevant to the experiments that were performed. Either clarify or remove "new" terminology. 

Thank you for bringing this to our attention. We have revised the relevant text accordingly at line 20 in the Abstract, line 31 in the In Brief, line 69 in the Introduction, line 83 in the Results, and line 226 in the Discussion to improve clarity and accuracy.

In Figure 2 D and G, D1 eGFP (+) and D2 eGFP(-) are plotted separately. These are the same cell type; therefore it may work best to combine that data. This could also be done for 'input to D2- Record D2' in panel D as well as 'input D1-Record D2' and 'input D2-Record D1' in panel G. Combining the information in panel D and G and comparing all 4 conditions to each other would give a better understanding of the comparison of functional connectivity between cortical neurons and D1 and D2 SPNs. 

We thank the reviewer for the thoughtful suggestion. While presenting single bars for each condition (e.g., ‘input D1 - record D1’) might improve visual simplicity, it would obscure an important aspect of our experimental design. Specifically, we aimed to highlight that the comparisons between D1- and D2-projecting neurons to D1 and D2 SPNs were counterbalanced within the same animals - not just across different groups. By showing both D1-eGFP(+) and D2-eGFP(-), or vice versa, within each group and at similar proportions, we provide a more complete picture of the internal control built into our design. This format helps ensure the audience that our conclusions are not biased by group-level differences, but are supported by within-subject comparisons. Therefore, that the current presentation better could serve to communicate the rigor and balance of our experimental approach.

The findings in Figure 2 are stated as D1 projecting excitatory inputs have a higher probability of targeting D1 SPNs while D2 projecting excitatory inputs target both D1 SPNs and D2 SPNs. It may be more clear to say that some cortical neurons project specifically to D1 SPNs while other cortical neurons project to both D1 and D2 SPNs equally. A better summary diagram could also help with clarity. 

Thank you for bringing this up. The data we present reflect the connection probabilities of D1- or D2-projecting cortical neurons to D1 or D2 SPNs. One possible interpretation is like the reviewer said that a subset of cortical neurons preferentially target D1 SPNs, while others exhibit more balanced projections to both D1 and D2 SPNs. However, we cannot rule out alternative explanations - for example, that some D2-projecting neurons preferentially target D2 SPNs, or that the observed differences arise from the overall proportions of D1- and D2-projecting cortical neurons connecting to each striatal subtype.

There are multiple possible patterns of connectivity that could give rise to the observed differences in connection ratios. Based on our current data, we can confidently conclude the existence of asymmetric cortico-striatal projections to the direct and indirect pathways, but the precise nature of this asymmetry will require further investigation.

Figure 4 introduces the FR8 task, but there are similar takeaways to the findings from Figure 3. Is there another justification for the FR8 task or interesting way of interpreting that data that could add richness to the manuscript?

The FR8 task is a self-initiated operant sequence task that relies on motor learning mechanisms, whereas the open field test solely assesses spontaneous locomotion. Furthermore, the sequence task enables us to dissect the functional role of specific neuronal populations in the initiation, maintenance, and termination of sequential movements through closed-loop optogenetic manipulations integrated into the task design. These methodological advantages underscore the rationale for including Figure 4 in the manuscript, as it highlights the unique insights afforded by this experimental paradigm.

I am somewhat surprised to see that D1-SPN stimulation in DLS gave the results in Figure 3 F and P, as mentioned in the public review. These contrast with some previous results (Cui et al, J Neurosci, 2021). Any explanation? Would be useful to speculate or compare parameters as this could have important implications for DLS function.

Thank you for raising this point. While Cui’s study has generated some debate, several independent investigations have consistently demonstrated that stimulation of D1-SPNs in the dorsolateral striatum (DLS) facilitates local motion and lever-press behaviors (Dong et al., 2025; Geddes et al., 2018; Kravitz et al., 2010). These findings support the functional role of D1-SPNs in promoting movement and motivated actions.

The differences in behavioral outcomes observed between our study and that of Cui et al. may stem from several methodological factors, particularly related to anatomical targeting and optical stimulation parameters.

Specifically, our experiments targeted the DMS at AP +0.5 mm, ML ±1.5 mm, DV –2.2 mm, and the DLS at AP +0.5 mm, ML ±2.5 mm, DV –2.2 mm. In contrast, Cui’s study targeted the DMS at AP +0.9 mm, ML ±1.4 mm, DV –3.0 mm, and the DLS at AP +0.7 mm, ML ±2.3 mm, DV –3.0 mm. These differences indicate that their targeting was slightly more rostral and more ventral than ours, which could have led to stimulation of distinct neuronal populations within the striatum, potentially accounting for variations in behavioral effects observed during optogenetic activation.

In addition, the optical fibers used in the two studies differed markedly. We employed optical fibers with a 200 µm core diameter and a numerical aperture (NA) of 0.37. Cui’s study used fibers with a larger core diameter (250 µm) and a higher NA (0.66), which would produce a broader spread and deeper penetration of light. This increased photostimulation volume may have recruited a more extensive network of neurons, possibly including off-target circuits, thus influencing the behavioral outcomes in a manner not seen in our more spatially constrained stimulation paradigm.

Taken together, these methodological differences, both in anatomical targeting and optical stimulation parameters, likely contribute to the discrepancies in behavioral results observed between the two studies. Our findings, consistent with other independent reports, support the role of D1-SPNs in facilitating movement and reinforcement behaviors under more controlled and localized stimulation conditions.

Reviewer #3 (Recommendations For The Authors): 

Minor: 

The authors repeatedly state that they are using a new rabies virus system, but the system has been in widespread use for 16 years, including in the exact circuits the authors are studying, for over a decade. I would not consider this new. 

Thank you for bringing this to our attention. We have revised the relevant text accordingly at line 20 in the Abstract, line 31 in the In Brief, line 69 in the Introduction, line 83 in the Results, and line 226 in the Discussion to improve clarity and accuracy.

Figure 2G, how many mice were used for recordings?

In Fig. 2G, we used 8 mice in the D1-projecting to D2 EGFP(+) group, 7 mice in the D1-projecting to D1 EGFP(-) group, 8 mice in the D2-projecting to D1 EGFP(+) group, and 10 mice in the D2-projecting to D2 EGFP(-) group.

The amplitude of inputs was not reported in figure 2. This is important, as the strength of the connection matters. This is reported in Figure S2, but how exactly this relates to the presence or absence of connections should be made clearer.

The amplitude data presented in Figure S2 summarize all recorded currents from confirmed connections, as detailed in the Methods section. A connection is defined by the presence of a detectable and reliable postsynaptic current with an onset latency of less than 10 ms following laser stimulation.

Reference in the reply-to-review comments:

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Chatterjee, S., Sullivan, H.A., MacLennan, B.J., Xu, R., Hou, Y.Y., Lavin, T.K., Lea, N.E., Michalski, J.E., Babcock, K.R., Dietrich, S., et al. (2018). Nontoxic, double-deletion-mutant rabies viral vectors for retrograde targeting of projection neurons. Nat Neurosci 21, 638-646.

Cruikshank, S.J., Urabe, H., Nurmikko, A.V., and Connors, B.W. (2010). Pathway-Specific Feedforward Circuits between Thalamus and Neocortex Revealed by Selective Optical Stimulation of Axons. Neuron 65, 230-245.

Dong, J., Wang, L.P., Sullivan, B.T., Sun, L.X., Smith, V.M.M., Chang, L.S., Ding, J.H., Le, W.D., Gerfen, C.R., and Cai, H.B. (2025). Molecularly distinct striatonigral neuron subtypes differentially regulate locomotion. Nat Commun 16, 2710.

Geddes, C.E., Li, H., and Jin, X. (2018). Optogenetic Editing Reveals the Hierarchical Organization of Learned Action Sequences. Cell 174, 32-43.

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Klug, J.R., Engelhardt, M.D., Cadman, C.N., Li, H., Smith, J.B., Ayala, S., Williams, E.W., Hoffman, H., and Jin, X. (2018). Differential inputs to striatal cholinergic and parvalbumin interneurons imply functional distinctions. Elife 7, e35657.

Kravitz, A.V., Freeze, B.S., Parker, P.R.L., Kay, K., Thwin, M.T., Deisseroth, K., and Kreitzer, A.C. (2010). Regulation of parkinsonian motor behaviours by optogenetic control of basal ganglia circuitry. Nature 466, 622-626.

Osakada, F., Mori, T., Cetin, A.H., Marshel, J.H., Virgen, B., and Callaway, E.M. (2011). New Rabies Virus Variants for Monitoring and Manipulating Activity and Gene Expression in Defined Neural Circuits. Neuron 71, 617-631.

Smith, J.B., Klug, J.R., Ross, D.L., Howard, C.D., Hollon, N.G., Ko, V.I., Hoffman, H., Callaway, E.M., Gerfen, C.R., and Jin, X. (2016). Genetic-Based Dissection Unveils the Inputs and Outputs of Striatal Patch and Matrix Compartments. Neuron 91, 1069-1084.

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Zhu, Z.G., Gong, R., Rodriguez, V., Quach, K.T., Chen, X.Y., and Sternson, S.M. (2025). Hedonic eating is controlled by dopamine neurons that oppose GLP-1R satiety. Science 387, eadt0773.

Author response:

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

eLife Assessment

This useful manuscript shows a set of interesting data including the first cryo-EM structures of human PIEZO1 as well as structures of disease-related mutants in complex with the regulatory subunit MDFIC, which generate different inactivation phenotypes. The molecular basis of PIEZO channel inactivation is of great interest due to its association with several pathologies. This manuscript provides some structural insights that may help to ultimately build a molecular picture of PIEZO channel inactivation. While the structures are of use and clear conformational differences can be seen in the presence of the auxiliary subunit MDFIC, the strength of the evidence supporting the conclusions of the paper, especially the proposed role for pore lipids in inactivation, is incomplete and there is a lack of data to support them.

We thank the editors and reviewers for taking the time and effort to review our manuscript.  The evidence supporting the key role of pore lipids in hPIEZO1 activation is as follows. i. Compared with wild-type hPIEZO1, the hydrophobic acyl chain tails of the pore lipids retracted from the hydrophobic pore region in slower inactivating mutant hPIEZO1-A1988V (Fig. 7a-b). ii. Previous electrophysiological functional studies revealed that substituting this hydrophobic pore formed by I2447, V2450, and F2454 with a hydrophilic pore prolongs the inactivation time for both PIEZO1 and PIEZO2 channels (PMID: 30628892). iii. In the structure of the HX channelopathy mutant R2456H, the interaction between the hydrophilic phosphate group head of pore lipids and R2456 is disrupted, remodeling the blade and pore module and resulting in a significantly slow-inactivating rate. iv. The interaction between pore lipids and lipidated-MDFIC stabilizes the pore lipids to reseal the pore upon activation of the hPIEZO1-MDFIC complex.

According to previously proposed models for the role of pore lipids in mechanosensitive ion channels, such as MscS (PMID: 33568813), MS K2P (PMID: 25500157) and OSCA channels (PMID: 37402734), the pore lipids seal the channel pores in closed state and could be removed in open state by mechanical force induced membrane deformation, which obeys the force-from-lipids principle. Therefore, in our putative model, the pore lipids seal the hydrophobic pore of hPIEZO1 in the closed state. Upon activation of hPIEZO1, the pore lipids retract from the hydrophobic pore and interact with multi-lipidated MDFIC, stabilizing in the inactivation state. The mild channelopathy mutants make the pore lipids retract from the hydrophobic pore and harder to close upon activation. For the severe channelopathy mutant, the interaction between the pore lipids and R2456 is disrupted, resulting in the missing of pore lipids and significantly slow-inactivating. We fully understand the concern of the role of pore lipids in our proposed model. Therefore, we have toned down our putative model.

Public Reviews:  

Reviewer #1 (Public review):  

Summary:  

This manuscript by Shan, Guo, Zhang, Chen et al., shows a raft of interesting data including the first cryo-EM structures of human PIEZO1. Clearly, the molecular basis of PIEZO channel inactivation is of great interest and as such this manuscript provides some valuable extra information that may help to ultimately build a molecular picture of PIEZO channel inactivation. However, the current manuscript though does not provide any compelling evidence for a detailed mechanism of PIEZO inactivation.

Strengths:

This manuscript documents the first cryo-EM structures of human PIEZO1 and the gain of function mutants associated with hereditary anaemia. It is also the first evidence showing that PIEZO1 gain of function mutants are also regulated by the auxiliary subunit MDFIC.

We thank reviewer #1 for the encouragement.

Weaknesses:

While the structures are interesting and clear differences can be seen in the presence of the auxiliary subunit MDFIC the major conclusions and central tenets of the paper, especially a role for pore lipids in inactivation, lack data to support them. The post-translational modification of PIEZOser# auxiliary subunit MDFIC is not modelled as a covalent interaction.

We fully understand the concern of the role of pore lipids in our proposed model. Therefore, we have toned down our putative model.

The lipids densities of the post-transcriptional modification of PIEZO1 auxiliary subunit MDFIC are shown below. As the lipids densities are not confident, we only use the single-chain lipids to represent them. And the lipidated MDFIC is proven by the MDFIC identification paper.

Author response image 1.

Reviewer #2 (Public review):

Summary:

Mechanically activated ion channels PIEZOs have been widely studied for their role in mechanosensory processes like touch sensation and red blood cell volume regulation. PIEZO in vivo roles are further exemplified by the presence of gain-of-function (GOF) or loss-of-function (LOF) mutations in humans that lead to disease pathologies. Hereditary xerocytosis (HX) is one such disease caused due to GOF mutation in Human PIEZO1, which are characterized by their slow inactivation kinetics, the ability of a channel to close in the presence of stimulus. But how these mutations alter PIEZO1 inactivation or even the underlying mechanisms of channel inactivation remains unknown. Recently, MDFIC (myoblast determination family inhibitor proteins) was shown to directly interact with mouse PIEZO1 as an auxiliary subunit to prolong inactivation and alter gating kinetics. Furthermore, while lipids are known to play a role in the inactivation and gating of other mechanosensitive channels, whether this mechanism is conserved in PIEZO1 is unknown. Thus, the structural basis for PIEZO1 inactivation mechanism, and whether lipids play a role in these mechanisms represent important outstanding questions in the field and have strong implications for human health and disease.

To get at these questions, Shan et al. use cryogenic electron microscopy (Cryo-EM) to investigate the molecular basis underlying differences in inactivation and gating kinetics of PIEZO1 and human disease-causing PIEZO1 mutations. Notably, the authors provide the first structure of human PIEZO1 (hPIEZO1), which will facilitate future studies in the field. They reveal that hPIEZO1 has a more flattened shape than mouse PIEZO1 (mPIEZO1) and has lipids that insert into the hydrophobic pore region. To understand how PIEZO1 GOF mutations might affect this structure and the underlying mechanistic changes, they solve structures of hPIEZO1 as well as two HXcausing mild GOF mutations (A1988V and E756del) and a severe GOF mutation (R2456H). Unable to glean too much information due to poor resolution of the mutant channels, the authors also attempt to resolve MCFIC-bound structures of the mutants. These structures show that MDFIC inserts into the pore region of hPIEZO1, similar to its interaction with mPIEZO1, and results in a more curved and contracted state than hPIEZO1 on its own. The authors use these structures to hypothesize that differences in curvature and pore lipid position underlie the differences in inactivation kinetics between wild-type hPIEZO1, hPIEZO1 GOF mutations, and hPIEZO1 in complex with MDFIC.

Strengths:

This is the first human PIEZO1 structure. Thus, these studies become the stepping stone for future investigations to better understand how disease-causing mutations affect channel gating kinetics.

We thank reviewer #2 for the positive comments.

Weaknesses:

Many of the hypotheses made in this manuscript are not substantiated with data and are extrapolated from mid-resolution structures.

We fully understand the concern of the role of pore lipids in our proposed model. Therefore, we have toned down our putative model.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors used structural biology approaches to determine the molecular mechanism underlying the inactivation of the PIEZO1 ion channel. To this end, the authors presented structures of human PIEZO1 and its slow-inactivating mutants. The authors also determined the structures of these PIEZO1 constructs in complexes with the auxiliary subunit MDFIC, which substantially slows down PIEZO1 inactivation. From these structures, the authors suggested an anti-correlation between the inactivation kinetics and the resting curvature of PIEZO1 in detergent. The authors also observed a unique feature of human PIEZO1 in which the lipid molecules plugged the channel pore. The authors proposed that these lipid molecules could stabilize human PIEZO1 in a prolonged inactivated state.

We thank reviewer #3 for the summary.

Strengths:

Notedly, this manuscript reported the first structures of a human PIEZO1 channel, its channelopathy mutants, and their complexes with MDFIC. The evidence that lipid molecules could occupy the channel pore of human PIEZO1 is solid. The authors' proposals to correlate PIEZO1 resting curvature and pore-resident lipid molecules with the inactivation kinetics are novel and interesting.

Thanks for the positive comments.

Weaknesses:

However, in my opinion, additional evidence is needed to support the authors' proposals.

(1) The authors determined the apo structure of human PIEZO1, which showed a more flattened architecture than that of the mouse PIEZO1. Functionally, the inactivation kinetics of human PIEZO1 is faster than its mouse counterpart. From this observation (and some subsequent observations such as the complex with MDFIC), the authors proposed the anti-correlation between curvature and inactivation kinetics. However, the comparison between human and mouse PIEZO1 structure might not be justified. For example, the human and mouse structures were determined in different detergent environments, and the choice of detergent could influence the resting curvature of the PIEZO structures.

We apologize for the misleading statement about the anti-correlation between curvature and inactivation kinetics of PIEZOs. We cannot conclude that the observation of curvature variation of mPIEZO1 and hPIEZO1 is related to their inactivation kinetics based on structural studies and electrophysiological assay. The difference in structural basis between mPIEZO1 and hPIEZO1 is what we want to state. To avoid this misleading, we have revised the manuscript. 

For the concern about detergent, we cannot fully exclude its influence on the curvature of PIEZOs. However, previously reported structures of mPiezo1 (PDB: 7WLT, 5Z10, 6B3R) were in the different detergent environments or in lipid bilayer, but the curvature of mPiezo1 is similar as shown below. Considering the high sequence similarity between mPiezo1 and hPiezo1, we hypothesize that the curvature of both hPiezo1 and mPiezo1 may be unaffected by the detergent.

Author response image 2.

Overall structural comparison of curved mPIEZO1 in the lipid bilayer (PDB: 7WLT), mPiezo1 in CHAPS (PDB: 6B3R) and mPiezo1 in Digitonin (PDB: 5Z10).

(2) Related to point 1), the 3.7 Å structure of the A1988V mutant presented by the authors showed a similar curvature as the WT but has a slower inactivating kinetics.

Based on the structural comparison between hPIEZO1 and its A1998V mutant, the retraction of pore lipids from the hydrophobic center pore in hPIEZO1-A1998V is mainly responsible for its slower inactivating kinetics.

(3) Related to point 1), the authors stated that human PIEZO1 might not share the same mechanism as mouse PIEZO1 due to its unique properties. For example, MDFIC only modifies the curvature of human PIEZO1, and lipid molecules were only observed in the pore of the human PIEZO1. Therefore, it may not be justified to draw any conclusions by comparing the structures of PIEZO1 from humans and mice.

Thanks for the constructive suggestion. To avoid this misleading, we have revised the manuscript.

(4) Related to point 1), it is well established that PIEZO1 opening is associated with a flattened structure. If the authors' proposal were true, in which a more flattened structure led to faster inactivation, we would have the following prediction: more opening is associated with faster inactivation. In this case, we would expect a pressure-dependent increase in the inactivation kinetics.

Could the authors provide such evidence, or provide other evidence along this direction?

We appreciate the reviewer’s comment. We are not claiming a relationship between the flattened structure and activation/inactivation. We only present the results of the structure of wild-type/mutant PIEZO1.

(5) In Figure S2, the authors showed representative experiments of the inactivation kinetics of PIEZO1 using whole-cell poking. However, poking experiments have high cell-to-cell variability.

The authors should also show statics of experiments obtained from multiple cells.

We have shown the statics of representative electrophysiology experiments obtained from multiple cells in Figure S2.

(6) In Figure 2 and Figure 5, when the authors show the pore diameter, it could be helpful to also show the side chain densities of the pore lining residues.

We appreciate the reviewer’s suggestion. The side chain of the pore lining restricted residues have been shown in Figure 2 and Figure 5 and the densities of pore domain have been shown in Figure S4 and S14. Interestingly, the pore lining restricted residues in mPIEZO1 and hPIEZO1 is highly conserved.

(7) The authors observed pore-plugging lipids in slow inactivating conditions such as channelopathy mutations or in complex with MDFIC. The authors propose that these lipid molecules stabilize a "deep resting state" of PIEZO1, making it harder to open and harder to inactivate once opened. This will lead to the prediction that the slow-inactivating conditions will lead to a higher activation threshold, such as the mid-point pressure in the activation curve. Is this true?

Yes, it is true. In Figure S2, the MDFIC-induced slow-inactivation conditions in hPIEZO1-MDFIC, hPIEZO1-A1988V-MDFIC, hPIEZO1-E756del-MDFIC and hPIEZO1-R2456H-MDFIC result in larger half-activation thresholds than hPIEZO1, hPIEZO1-A1988V, hPIEZO1-E756del and hPIEZO1-R2456H, respectively.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I document the major issues below:

(1) Mouse vs Human inactivation

Line 21- "than the slower inactivating curved mouse PIEZO1 (mPIEZO1)."

Where is the data in this paper or any other paper that human PIEZO1 inactivates faster than mouse PIEZO1? This is central to the way the authors present the paper. In fact, the tau quoted for the hPIEZO1 of ~10 ms is similar to that often measured for mPIEZO1. The reference in the discussion for mouse vs human inactivation times is a review of mechanotransduction. Either the authors need to directly compare the tau of mP1 vs hP1 or quote the relevant primary literature if it exists.

As measured in HEK-PIKO cells transfected with mPiezo1, the inactivation time of mPiezo1 is 13 ± 1 ms (PMID: 29261642) at -80 mV. 

The tau is also voltage-dependent. The tau is beyond 20 ms at -60 mV for mPIEZO1 (PMID:

20813920) and for hPIEZO1 is still around 10 ms.

(2) MDFIC-lipidation

Without seeing the PDB or EMDB I can't guarantee this but from Figure 6d it seems like the Sacylation in the distal C-terminus of MDFIC is not modelled as a covalent interaction, these lipids are covalently added to the Cys residues in S-acylation via zDHHC enzymes. This should be modelled correctly.

Thanks for this suggestion. As the lipid densities of the post-transcriptional modification of PIEZOs auxiliary subunit MDFIC are not confident, we only use the single-chain lipids to represent them.

And the lipidated MDFIC is proven by the MDFIC identification paper (PMID: 37590348).

(3) Pore lipids and inactivation

The lipids close to the pore are interesting and the density for a lipid is also seen in the mouse MDFIC-PIEZO1 complex from Zhou, Ma et al, 2023. However, there is no data provided by the authors that the lipid is functionally relevant to anything. There is not even a correlation with inactivation in Figure 7. P1+MDFIC inactivates slowest yet the lipids are present within the pore. Second, there is no evidence for what these structures are: closed, or inactivated? In fact, the Xiao lab is now interpreting the 7WLU structure as inactivated.

The evidence supporting the key role of pore lipids in hPIEZO1 activation is as follows. i. Compared with wild-type hPIEZO1, the hydrophobic acyl chain tails of the pore lipids retracted from the hydrophobic pore region in slower inactivating mutant hPIEZO1-A1988V (Fig. 7a-b). ii. Previous electrophysiological functional studies revealed that substituting this hydrophobic pore formed by I2447, V2450, and F2454 with a hydrophilic pore prolongs the inactivation time for both PIEZO1 and PIEZO2 channels (PMID: 30628892). iii. In the structure of the HX channelopathy mutant R2456H, the interaction between the hydrophilic phosphate group head of pore lipids and R2456 is disrupted, remodeling the blade and pore module and resulting in a significantly slow-inactivating rate. iv. The interaction between pore lipids and lipidated-MDFIC stabilizes the pore lipids to reseal the pore upon activation of the hPIEZO1-MDFIC complex. Overall, the pore lipid is involved in inactivation, and we have toned down the statement.

(4) Cytosolic plug

There is additional cytosolic density for the human PIEZO1 that the authors intimate could be from a different binding partner. IS it possible to refine this density? Is it from the PIEZO1-tag? At the very least a little more information about this density should be given if it is going to be mentioned like this.

Our purification result shows that the protein is tag-free. We are also curious about the extra cytosolic density, but we do not know what it is.

(5) Reduced sensitivity of PIEZO1 in the presence of MDFIC and its regulatory mechanism

This was reported in the first article however no data is presented by the authors to support MDFIC increasing the mechanical energy required to open PIEZO1. The sentence in the discussion; "MDFIC enables hPIEZO1 to respond to different forces by modifying the pore module through lipid interactions." is not supported by any functional data and seems to be an over-interpretation of the structures.

We appreciate this suggestion. The half-activation threshold of hPEIZO1 and hPEIZO1-MDFIC is measured to be 7 μm and 9 μm, respectively (Fig.S2). In addition, the mechanical currents amplitude of hPIEZO1-MDFIC is extremely small compared to that of WT reaching the nA level (Fig.S2). Therefore, the less mechanosensitive hPIEZO1-MDFIC may require more mechanical energy to open than PIEZO1 WT.

6) Both referencing of the PIEZO1 literature and prose could be improved.

Thanks for the suggestion. We have improved the referencing and prose.

Reviewer #2 (Recommendations for the authors):

(1) The authors speculate that the difference in curvature between human and mouse PIEZO1 results in its fast inactivation but do not provide experimental evidence to support this idea. This claim would have been bolstered by showing that the GOF human mutations have a more curved structure, but these proved too structurally unstable to be solved at high resolution. However, the authors state that the 3.7 angstrom map solved for hPIEZO1-A1988V does have an overall similar architecture as wild-type hPIEZO1; thus, contradicting their hypothesis.

We apologize for the misleading statement. In our revised manuscript, we do not claim a relationship between the flattened structure and activation/inactivation. We only present the results of the structure of wild-type/mutant PIEZO1.

The structure comparison between the A1988V mutant and WT shows a similar architecture but a different occupancy pattern of pore lipids. Therefore, we suggested that the A1988V mutant has slightly slower inactivation kinetics, mainly due to the exit of pore lipids from the pore.

(2) The authors show that interaction with MDFIC alters hPIEZO1 structure to be more curved and use this to support their idea that changing the curvature of the protein underlies the prolonged inactivation kinetics. It has been previously shown that MDFIC does not change the structure of mPIEZO1 but does alter its inactivation and gating kinetics. How does this discrepancy fit into the inactivation model proposed by the authors? Similarly, their claim that MDFIC slows hPIEZO1 inactivation and weakens mechanosensitivity just by affecting the pore module and changing blade curvature is made based on observation and no experimental data to test it.

We have revised the manuscript to avoid misleading the relationship between the curvature and the inaction kinetics of hPIEZO1. The evidence reported previously that substitution of the hydrophobic pore, formed by I2447, V2450, and F2454, with a hydrophilic pore prolongs the inactivation time for both PIEZO1 and PIEZO2 channels (PMID: 30628892). In addition, the severe HX channelopathy mutant R2456H, wherein the interaction between the hydrophilic phosphate group head and R2456 is disrupted, leads to remodeling of the blade and pore module. Indeed, our observation is limited and further experiments will be performed to support our model.

(3) How does their model fit in cell types that have PIEZO1 (or GOF mutant PIEZO1) but not MDFIC?

In cell types that have PIEZO1 or GOF mutant PIEZO1 but not MDFIC, PIEZO1 or GOF mutant PIEZO1 may have a faster inactivation rate than those that bind to MDFIC. It can be proved that overexpressed PIEZOs exhibit faster inactivation kinetics than those in some native cell types with MDFIC expression (PMID: 20813920, 30132757).

(4) Figure S2 is missing quantification of the electrophysiology data. The authors should show summary data in addition to their representative traces including the Imax for all conditions, tau for data shown in b, and sample size for all conditions, and related statistics. The text claims that MDFIC decreases mechanosensitivity (line 156) but there is no data to support this.

For the electrophysiological assay in Figure S2, we referred to previously reported mPIEZO1 mutants (PMID: 23487776, 28716860). We confirmed that the slower inactivation phenotypes of these mutations of hPIEZO1 are similar to those of mPIEZO1.

The half-activation threshold of hPEIZO1 and hPEIZO1-MDFIC is measured to be 7 μm and 9 μm, respectively. This tendency of increased half-activation threshold of hPIEZO1 upon binding with MDFIC is also shown in the electrophysiological result of hPIEZO1 channelopathy mutants.

(5) In line 144, the authors mention that they were able to validate the MDFIC density with multilipidated cysteines on the C-terminal amphipathic helix, but they do not show the density with fitted lipids. While individual densities for some of the lipids are shown in extended Figure 12, it would be helpful to include a figure where they show the map for MDFIC with fitted lipids in it.

Thanks for the valuable suggestion. As the lipid densities of the post-transcriptional modification of PIEZOs auxiliary subunit MDFIC are not confident, we only use the single-chain lipids to represent them. And the lipidated MDFIC is proven by the MDFIC identification paper.

(6) The authors show that R2456 interacts with a lipid at the pore module and hypothesize that this underlies the fast inactivation of hPIEZO1. While they did not obtain a high-resolution structure of this mutant, this hypothesis could be tested by substituting R for side chains with different charges and performing electrophysiology to determine the effects on inactivation.

Thanks for the constructive suggestion. We will perform the electrophysiology assay for R2456 mutants with different side chains.

7) Figure 4 shows overall structure of hPIEZO1 GOF mutations A1988V and E756del in complex with MDFIC. Other than showing an overall similar structure to wildtype hPIEZO1, the authors do not show how the human mutations A1988V alter the structure of the protein at the site of change. Understanding how these mutations affect the local architecture of the protein has important relevance for human physiology.

As the GOF channelopathy mutant hPIEZO1-A1988V is structurally unstable, the density at the site of A1988V is too weak to figure out the related interaction in the structure of the hPIEZO1-A1988V mutant. 

Minor comment:

In general, the manuscript will benefit from heavy copy editing. For example, the word cartoon is misspelled in many of the figure legends.

We apologize for the mistake. The manuscript has been checked and revised.

Reviewer #3 (Recommendations for the authors):

Some portions of this manuscript were not well written. For example, at the end of the 3rd paragraph in the introduction, the authors talked about HX mutations and their correlation with malaria infection and plasma iron. This is irrelevant information and will only distract the readers. It would be ideal if the authors could go through the entire manuscript and improve its clarity.

Thanks for the suggestion. We have revised the sentences about HX mutations as suggested and improved the entire manuscript.

Author Response

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

Reviewer #1 (Public Review):

The biogenesis of outer membrane proteins (OMPs) into the outer membranes of Gram-negative bacteria is still not fully understood, particularly substrate recognition and insertion by beta-assembly machinery (BAM). In the studies, the authors present their studies that in addition to recognition by the last strand of an OMP, sometimes referred to as the beta-signal, an additional signal upstream of the last strand is also important for OMP biogenesis.

Strengths:

1. Overall the manuscript is well organized and written, and addresses an important question in the field. The idea that BAM recognizes multiple signals on OMPs has been presented previously, however, it was not fully tested.

2. The authors here re-address this idea and propose that it is a more general mechanism used by BAM for OMP biogenesis.

3. The notion that additional signals assist in biogenesis is an important concept that indeed needs fully tested in OMP biogenesis.

4. A significant study was performed with extensive experiments reported in an attempt to address this important question in the field.

5. The identification of important crosslinks and regions of substrates and Bam proteins that interact during biogenesis is an important contribution that gives clues to the path substrates take en route to the membrane.

Weaknesses:

Major critiques (in no particular order):

1. The title indicates 'simultaneous recognition', however no experiments were presented that test the order of interactions during OMP biogenesis.

We have replaced the word “Simultaneous” with “Dual” so as not to reflect on the timing of the recognition events for the distinct C-terminal signal and -5 signal.

1. Aspects of the study focus on the peptides that appear to inhibit OmpC assembly, but should also include an analysis of the peptides that do not to determine this the motif(s) present still or not.

We thank the reviewer for this comment. Our study focuses on the peptides which exhibited an inhibitory effect in order to elucidate further interactions between the BAM complex and substrate proteins, especially in early stage of the assembly process. In the case of peptide 9, which contains all of our proposed elements but did not have an inhibitory effect, there is the presence of an arginine residue at the polar residue next to hydrophobic residue in position 0 (0 Φ). As seen in Fig S5, S6, and S7, there are no positively charged amino acids in the polar residue positions in the -5 or last strands. This might be the reason why peptide 9, as well as peptide 24, the β-signal derived from the mitochondrial OMP Tom40 and contains a lysine at the polar position, did not display an inhibitory effect. Incorporating the reviewer's suggestions might elucidate conditions that should not be added to the elements, but this is not the focus of this paper and was not discussed to avoid complicating the paper.

1. The β-signal is known to form a β-strand, therefore it is unclear why the authors did not choose to chop OmpC up according to its strands, rather than by a fixed peptide size. What was the rationale for how the peptide lengths were chosen since many of them partially overlap known strands, and only partially (2 residues) overlap each other? It may not be too surprising that most of the inhibitory peptides consist of full strands (#4, 10, 21, 23).

A simple scan of known β-strands would have been an alternative approach, however this comes with the bias of limiting the experiments to predicted substrate (strand) sequences, and it presupposes that the secondary structure element would be formed by this tightly truncated peptide.

Instead, we allowed for the possibility that OMPs meet the BAM complex in an unfolded or partially folded state, and that the secondary structure (β-strand) might only form via β-argumentation after the substrate is placed in the context of the lateral gate. We therefore used peptides that mapped right across the entirety of OmpC, with a two amino acid overlap.

To clarify this important point regarding the unbiased nature of our screen, we have revised the text:

(Lines 147-151) "We used peptides that mapped the entirety of OmpC, with a two amino acid overlap. This we considered preferable to peptides that were restricted by structural features, such as β-strands, in consideration that β-strand formation may or may not have occurred in early-stage interactions at the BAM complex."

1. It would be good to have an idea of the propensity of the chosen peptides to form β-stands and participate in β-augmentation. We know from previous studies with darobactin and other peptides that they can inhibit OMP assembly by competing with substrates.

We appreciate the reviewer's suggestion. However, we have not conducted biophysical characterizations of the peptides to calculate the propensity of each peptide to form β-stands and participate in β-augmentation. The sort of detailed biophysical analysis done for Darobactin (by the Maier and Hiller groups, The antibiotic darobactin mimics a β-strand to inhibit outer membrane insertase Nature 593:125-129) was a Nature publication based on this single peptide. A further biophysical analysis of all of the peptides presented here goes well beyond the scope of our study.

1. The recognition motifs that the authors present span up to 9 residues which would suggest a relatively large binding surface, however, the structures of these regions are not large enough to accommodate these large peptides.

The β-signal motif (ζxGxx[Ω/Φ]x[Ω/Φ]) is an 8-residue consensus, some of the inhibitory peptides include additional residues before and after the defined motif of 8 residues, and the lateral gate of BamA has been shown interact with a 7-residue span (eg. Doyle et al, 2022). Cross-linking presented in our study showed BamD residues R49 and G65 cross-linked to the positions 0 and 6 of the internal signal in OmpC (Fig. 6D).

We appreciate this point of clarification and have modified the text to acknowledge that in the final registering of the peptide with its binding protein, some parts of the peptide might sit beyond the bounds of the BamD receptor’s binding pocket and the BamA lateral gate:

(Lines 458-471) "The β-signal motif (ζxGxx[Ω/Φ]x[Ω/Φ]) is an eight-residue consensus, and internal signal motif is composed of a nine-residue consensus. Recent structures have shown the lateral gate of BamA interacts with a 7-residue span of substrate OMPs. Interestingly, inhibitory compounds, such as darobactin, mimic only three resides of the C-terminal side of β-signal motif. Cross-linking presented here in our study showed that BamD residues R49 and G65 cross-linked to the positions 0 and 6 of the internal signal in OmpC (Fig. 6D). Both signals are larger than the assembly machineries signal binding pocket, implying that the signal might sit beyond the bounds of the signal binding pocket in BamD and the lateral gate in BamA. These finding are consistent with similar observations in other signal sequence recognition events, such as the mitochondrial targeting presequence signal that is longer than the receptor groove formed by the Tom20, the subunit of the translocator of outer membrane (TOM) complex (Yamamoto et al., 2011). The presequence has been shown to bind to Tom20 in several different conformations within the receptor groove (Nyirenda et al., 2013)."

Moreover, the distance between amino acids of BamD which cross-linked to the internal signal, R49 and Y62, is approximately 25 Å (pdbID used 7TT3). The distance of the maximum amino acid length of the internal signal of OmpC, from F280 to Y288, is approximately 22 Å (pdbID used 2J1N). This would allow for the signal to fit within the confines of the TRP motif of BamD.

Author response image 1.

1. The authors highlight that the sequence motifs are common among the inhibiting peptides, but do not test if this is a necessary motif to mediate the interactions. It would have been good to see if a library of non-OMP related peptides that match this motif could also inhibit or not.

With respect, this additional work would not address any biological question relevant to the function of BamD. To randomize sequences and then classify those that do or don’t fit the motif would help in refining the parameters of the β-signal motif, but that was not our intent.

We have identified the peptides from within the total sequence of an OMP, shown which peptides inhibit in an assembly assay, and then observed that the inhibitory peptides conform to a previously published (β-signal) motif.

1. In the studies that disrupt the motifs by mutagenesis, an effect was observed and attributed to disruption of the interaction of the 'internal signal'. However, the literature is filled with point mutations in OMPs that disrupt biogenesis, particular those within the membrane region. F280, Y286, V359, and Y365 are all residues that are in the membrane region that point into the membrane. Therefore, more work is needed to confirm that these mutations are in parts of a recognition motif rather than on the residues that are disrupting stability/assembly into the membrane.

As the reviewer pointed out, the side chains of the amino acids constituting the signal elements we determined were all facing the lipid side, of which Y286 and Y365 were important for folding as well as to be recognized. However, F280A and V359A had no effect on folding, but only on assembly through the BAM complex. The fact that position 0 functions as a signal has been demonstrated by peptidomimetics (Fig. 1) and point mutant analysis (Fig. 2). We appreciate this clarification and have modified the text to acknowledge that the all of the signal element faces the lipid side, which contributes to their stability in the membrane finally, and before that the BAM complex actively recognizes them and determines their orientation:

(Lines 519-526) After OMP assembly, all elements of the internal signal are positioned such that they face into the lipid-phase of the membrane. This observation may be a coincidence, or may be utilized by the BAM complex to register and orientate the lipid facing amino acids in the assembling OMP away from the formative lumen of the OMP. Amino acids at position 6, such as Y286 in OmpC, are not only component of the internal signal for binding by the BAM complex, but also act in structural capacity to register the aromatic girdle for optimal stability of the OMP in the membrane.

1. The title of Figure 3 indicates that disrupting the internal signal motif disrupts OMP assembly, however, the point mutations did not seem to have any effect. Only when both 280 and 286 were mutated was an effect observed. And even then, the trimer appeared to form just fine, albeit at reduced levels, indicating assembly is just fine, rather the rate of biogenesis is being affected.

We appreciate this point and have revised the title of Figure 3 to be:

(Lines 1070-1071) "Modifications in the putative internal signal slow the rate of OMP assembly in vivo."

1. In Figure 4, the authors attempt to quantify their blots. However, this seems to be a difficult task given the lack of quality of the blots and the spread of the intended signals, particularly of the 'int' bands. However, the more disturbing trend is the obvious reduction in signal from the post-urea treatment, even for the WT samples. The authors are using urea washes to indicate removal of only stalled substrates. However a reduction of signal is also observed for the WT. The authors should quantify this blot as well, but it is clear visually that both WT and the mutant have obvious reductions in the observable signals. Further, this data seems to conflict with Fig 3D where no noticeable difference in OmpC assembly was observed between WT and Y286A, why is this the case?

We have addressed this point by adding a statistical analysis on Fig. 4A. As the reviewer points out, BN-PAGE band quantification is a difficult task given the broad spread of the bands on these gels. Statistical analysis showed that the increase in intermediates (int) was statistically significant for Y286A at all times until 80 min, when the intermediate form signals decrease.

(Lines 1093-1096) "Statistical significance was indicated by the following: N.S. (not significant), p<0.05; , p<0.005; *. Exact p values of intermediate formed by Wt vs Y286A at each timepoint were as follows; 20 minutes: p = 0.03077, 40 minutes: p = 0.02402, 60 minutes: p = 0.00181, 80 minutes: p = 0.0545."

Further regarding the Int. band, we correct the statement as follows.

(Lines 253-254) "Consistent with this, the assembly intermediate which was prominently observed at the OmpC(Y286A) can be extracted from the membranes with urea;"

OMP assembly in vivo has additional periplasmic chaperones and factors present in order to support the assembly process. Therefore, it is likely that some proteins were assembled properly in vivo compared to their in vitro counterparts. Such a decrease has been observed not only in E. coli but also in mitochondrial OMP import (Yamano et al., 2010).

1. The pull-down assays with BamA and BamD should include a no protein control at the least to confirm there is no non-specific binding to the resin. Also, no detergent was mentioned as part of the pull downs that contained BamA or OmpC, nor was it detailed if OmpC was urea solubilized.

We have performed pull down experiments with a no-protein (Ni-NTA only) control as noted (Author response image 1). The results showed that the amount of OmpC carrying through on beads only was significantly lower than the amount of OmpC bound in the presence of BamD or BamA. The added OmpC was not treated with urea, but was synthesized by in vitro translation; the in vitro translated OmpC is the standard substrate in the EMM assembly assay (Supp Fig. S1) where it is recognized by the BAM complex. Thus, we used it for pull-down as well and, to make this clearer, we have revised as follows:

Author response image 2.

Pull down assay of radio-labelled OmpC with indicated protein or Ni-NTA alone (Ni-NTA) . T; total, FT; Flow throw, W; wash, E; Elute.

(Lines 252-265) "Three subunits of the BAM complex have been previously shown to interact with the substrates: BamA, BamB, and BamD (Hagan et al., 2013; Harrison, 1996; Ieva et al., 2011). In vitro pull-down assay showed that while BamA and BamD can independently bind to the in vitro translated OmpC polypeptide (Fig .S9A), BamB did not (Fig. S9B)."

11.

• The neutron reflectometry experiments are not convincing primarily due to the lack controls to confirm a consistent uniform bilayer is being formed and even if so, uniform orientations of the BamA molecules across the surface.

• Further, no controls were performed with BamD alone, or with OmpC alone, and it is hard to understand how the method can discriminate between an actual BamA/BamD complex versus BamA and BamD individually being located at the membrane surface without forming an actual complex.

• Previous studies have reported difficulty in preparing a complex with BamA and BamD from purified components.

• Additionally, little signal differences were observed for the addition of OmpC. However, an elongated unfolded polypeptide that is nearly 400 residues long would be expected to produce a large distinct signal given that only the C-terminal portion is supposedly anchored to BAM, while the rest would be extended out above the surface.

• The depiction in Figure 5D is quite misleading when viewing the full structures on the same scales with one another.

We have addressed these five points individually as follows.

i. The uniform orientation of BamA on the surface is guaranteed by the fixation through a His-tag engineered into extracellular loop 6 of BamA and has been validated in previous studies as cited in the text. Moreover, to explain this, we reconstructed another theoretical model for BamA not oriented well in the system as below. However, we found that the solid lines (after fitting) didn’t align well with the experimental data. We therefore assumed that BamA has oriented well in the membrane bilayer.

Author response image 3.

Experimental (symbols) and fitted (curves) NR profiles of BamA not oriented well in the POPC bilayer in D2O (black), GMW (blue) and H2O (red) buffer.

ii. There would be no means by which to do a control with OmpC alone or BamD alone as neither protein binds to the lipid layer chip. OmpC is diluted from urea and then the unbound OmpC is washed from the chip before NR measurements. BamD does not have an acyl group to anchor it to the lipid layer, without BamA to anchor to, it too is washed from the chip before NR measurements. We have reconstructed another theoretical model for both of BamA + BamD embedding in the membrane bilayer, and the fits were shown below. Apparently, the fits didn’t align well with the experimental data, which discriminate the BamA/BamD individually being located at the membrane surface without forming an actual complex.

Author response image 4.

Experimental (symbols) and fitted (curves) NR profiles of BamA+D embedding together in the POPC bilayer in D2O (black), GMW (blue) and H2O (red) buffer.

iii. The previous studies that reported difficulty in preparing a complex with BamA and BamD from purified components were assays done in aqueous solution including detergent solubilized BamA, or with BamA POTRA domains only. Our assay is superior in that it reports the binding of BamD to a purified BamA that has been reconstituted in a lipid bilayer.

iv. The relatively small signal differences observed for the addition of OmpC are expected, since OmpC is an elongated, unfolded polypeptide of nearly 400 residues long which, in the context of this assay, can occupy a huge variation in the positions at which it will sit with only the C-terminal portion anchored to BAM, and the rest moving randomly about and extended from the surface.

v. We appreciate the point raised and have now added a note in the Figure legend that these are depictions of the results and not a scale drawing of the structures.

1. In the crosslinking studies, the authors show 17 crosslinking sites (43% of all tested) on BamD crosslinked with OmpC. Given that the authors are presenting specific interactions between the two proteins, this is worrisome as the crosslinks were found across the entire surface of BamD. How do the authors explain this? Are all these specific or non-specific?

The crosslinking experiment using purified BamD was an effective assay for comprehensive analysis of the interaction sites between BamD and the substrate. However, as the reviewer pointed out, cross-linking was observed even at the sites that, in the context of the BAM complex, interact with BamC as a protein-protein interaction and would not be available for substrate protein-protein interactions. To complement this, analysis and to address this issue, we also performed the experiment in Fig. 6C.

In Fig. 6C, the interaction of BamD with the substrate is examined in vivo, and the results demonstrate that if BPA is introduced into the site, we designated as the substrate recognition site, it is cross-linked to the substrate. On the other hand, position 114 was found to crosslink with the substrate in vitro crosslinking, but not in vivo. It should be noted that position 114 has also been confirmed to form cross-link products with BamC, we believe that BamD-substrate interactions in the native state have been investigated. To explain the above, we have added the following description to the Results section.

(Lines 319-321) "Structurally, these amino acids locate both the lumen side of funnel-like structure (e.g. 49 or 62) and outside of funnel-like structure such as BamC binding site (e.g. 114) (fig. S12C). (Lines 350-357) Positions 49, 53, 65, and 196 of BamD face the interior of the funnel-like structure of the periplasmic domain of the BAM complex, while position 114 is located outside of the funnel-like structure (Bakelar et al., 2016; Gu et al., 2016; Iadanza et al., 2016). We note that while position 114 was cross-linked with OmpC in vitro using purified BamD, that this was not seen with in vivo cross-linking. Instead, in the context of the BAM complex, position 114 of BamD binds to the BamC subunit and would not be available for substrate binding in vivo (Bakelar et al., 2016; Gu et al., 2016; Iadanza et al., 2016)."

1. The study in Figure 6 focuses on defined regions within the OmpC sequence, but a more broad range is necessary to demonstrate specificity to these regions vs binding to other regions of the sequence as well. If the authors wish to demonstrate a specific interaction to this motif, they need to show no binding to other regions.

The region of affinity for the BAM complex was determined by peptidomimetic analysis, and the signal region was further identified by mutational analysis of OmpC. Subsequently, the subunit that recognizes the signal region was identified as BamD. In other words, in the process leading up to Fig. 6, we were able to analyze in detail that other regions were not the target of the study. We have revised the text to make clear that we focus on the signal region including the internal signal, and have not also analyzed other parts of the signal region:

(Lines 329-332) "As our peptidomimetic screen identified conserved features in the internal signal, and cross-linking highlighted the N-terminal and C-terminal TPR motifs of BamD as regions of interaction with OmpC, we focused on amino acids specifically within the β-signals of OmpC and regions of BamD which interact with β-signal."

1. The levels of the crosslinks are barely detectable via western blot analysis. If the interactions between the two surfaces are required, why are the levels for most of the blots so low?

These are western blots of cross-linked products – the efficiency of cross-linking is far less than 100% of the interacting protein species present in a binding assay and this explains why the levels for the blots are ‘so low’. We have added a sentence to the revised manuscript to make this clear for readers who are not molecular biologists:

(Lines 345-348) "These western blots reveal cross-linked products representing the interacting protein species. Photo cross-linking of unnatural amino acid is not a 100% efficient process, so the level of cross-linked products is only a small proportion of the molecules interacting in the assays."

15.

• Figure 7 indicates that two regions of BamD promote OMP orientation and assembly, however, none of the experiments appears to measure OMP orientation?

• Also, one common observation from panel F was that not only was the trimer reduced, but also the monomer. But even then, still a percentage of the trimer is formed, not a complete loss.

(i) We appreciate this point and have revised the title of Figure 7 to be:

(Lines 1137-1138) "Key residues in two structurally distinct regions of BamD promote β-strand formation and OMP assembly."

(ii) In our description of Fig. 7F (Lines 356-360) we do not distinguish between the amount of monomer and trimer forms, since both are reflective of the overall assembly rate i.e. assembly efficiency. Rather, we state that:

"The EMM assembly assay showed that the internal signal binding site was as important as the β-signal binding site to the overall assembly rates observed for OmpC (Fig. 7F), OmpF (fig. S15D), and LamB (fig. S15E). These results suggest that recognition of both the C-terminal β-signal and the internal signal by BamD is important for efficient protein assembly."

16.

• The experiment in Fig 7B would be more conclusive if it was repeated with both the Y62A and R197A mutants and a double mutant. These controls would also help resolve any effect from crowding that may also promote the crosslinks.

• Further, the mutation of R197 is an odd choice given that this residue has been studied previously and was found to mediate a salt bridge with BamA. How was this resolved by the authors in choosing this site since it was not one of the original crosslinking sites?

As stated in the text, the purpose of the experiment in Figure 7B is to measure the impact of pre-forming a β-strand in the substrate (OmpC) before providing it to the receptor (BamD). We thank the reviewer for the comment on the R197 position of BamD. The C-terminal domain of BamD has been suggested to mediate the BamA-BamD interface, specifically BamD R197 amino acid creates a salt-bridge with BamA E373 (Ricci et al., 2012). It had been postulated that the formation of this salt-bridge is not strictly structural, with R197 highlighted as a key amino acid in BamD activity and this salt-bridge acts as a “check-point” in BAM complex activity (Ricci et al., 2012, Storek et al., 2023). Our results agree with this, showing that the C-terminus of BamD acts in substrate recognition and alignment of the β-signal (Fig. 6, Fig S12). We show that amino acids in the vicinity of R197 (N196, G200, D204) cross-linked well to substrate and mutations to the β-signal prevent this interaction (Fig S12B, D). For mutational analysis of BamD, we looked then at the conservation of the C-terminus of BamD and determined R197 was the most highly conserved amino acid (Fig 6C). In order to account for this, we have adjusted the manuscript:

(Lines 376-377) "R197 has previously been isolated as a suppressor mutation of a BamA temperature sensitive strain (Ricci et al., 2012)."

(Lines 495-496) "This adds an additional role of the C-terminus of BamD beyond a complex stability role (Ricci et al., 2012; Storek et al., 2023)."

1. As demonstrated by the authors in Fig 8, the mutations in BamD lead to reduction in OMP levels for more than just OmpC and issues with the membrane are clearly observable with Y62A, although not with R197A in the presence of VCN. The authors should also test with rifampicin which is smaller and would monitor even more subtle issues with the membrane. Oddly, no growth was observed for the Vec control in the lower concentration of VCN, but was near WT levels for 3 times VCN, how is this explained?

While it would be interesting to correlate the extent of differences to the molecular size of different antibiotics such as rifampicin, such correlations are not the intended aim of our study. Vancomycin (VCN) is a standard measure of outer membrane integrity in our field, hence its use in our tests for membrane integrity.

We apologize to the reviewer as Figure 8 D-G may have been misleading. Figure 8D,E are using bamD shut-down cells expressing plasmid-borne BamD mutants. Whereas Figure 8F, G are the same strain as used in Figure 3. We have adjusted the figure as well as the figure legend: (Lines 1165-1169) D, E E coli bamD depletion cells expressing mutations at residues, Y62A and R197A, in the β-signal recognition regions of BamD were grown with of VCN. F, G, E coli cells expressing mutations to OmpC internal signal, as shown in Fig 3, grown in the presence of VCN. Mutations to two key residues of the internal signal were sensitive to the presence of VCN.

1. While Fig 8I indeed shows diminished levels for FY as stated, little difference was observed for the trimer for the other mutants compared to WT, although differences were observed for the dimer. Interestingly, the VY mutant has nearly WT levels of dimer. What do the authors postulate is going on here with the dimer to trimer transition? How do the levels of monomer compare, which is not shown?

The BN-PAGE gel system cannot resolve protein species that migrate below ~50kDa and the monomer species of the OMPs is below this size. We can’t comment on effects on the monomer because it is not visualized. The non-cropped gel image is shown here. Recently, Hussain et al., has shown that in vitro proteo-liposome system OmpC assembly progresses from a “short-lived dimeric” form before the final process of trimerization (Hussain et al., 2021). However, their findings suggest that LPS plays the final role in stimulation of dimer-to-trimer, a step well past the recognition step of the β-signals. Mutations to the internal signal of OmpC results in the formation of an intermediate, the substrate stalled on the BAM complex. This stalling, presumably, causes a hinderance to the BAM complex resulting in reduced timer and loss of dimer OmpF signal in the EMM of cells expressing OmpC double mutant strain, FY. cannot resolve protein species that migrate below ~50kDa and the monomer species of the OMPs is below this size. We can’t comment on effects on the monomer because it is not visualized. The non-cropped gel image is shown here. We have noted this in the revised text:

Author response image 5.

Non-cropped gel of Fig. 8I. the asterisk indicates a band observed in the sample loading wells at the top of the gel.

(Lines 417-418) "The dimeric form of endogenous OmpF was prominently observed in both the OmpC(WT) as well as the OmpC(VY) double mutant cells."

1. In the discussion, the authors indicate they have '...defined an internal signal for OMP assembly', however, their study is limited and only investigates a specific region of OmpC. More is needed to definitively say this for even OmpC, and even more so to indicate this is a general feature for all OMPs.

We acknowledge the reviewer's comment on this point and have expanded the statement to make sure that the conclusion is justified with the specific evidence that is shown in the paper and the supplementary data. We now state:

(Lines 444-447) "This internal signal corresponds to the -5 strand in OmpC and is recognized by BamD. Sequence analysis shows that similar sequence signatures are present in other OMPs (Figs. S5, S6 and S7). These sequences were investigated in two further OMPs: OmpF and LamB (Fig. 2C and D)."

Note, we did not state that this is a general feature for all OMPs. That would not be a reasonable proposition.

20.

• In the proposed model in Fig 9, it is hard to conceive how 5 strands will form along BamD given the limited surface area and tight space beneath BAM.

• More concerning is that the two proposal interaction sites on BamD, Y62 and R197, are on opposite sides of the BamD structure, not along the same interface, which makes this model even more unlikely.

• As evidence against this model, in Figure 9E, the two indicates sites of BamD are not even in close proximity of the modeled substrate strands.

We can address the reviewer’s three concerns here:

i. The first point is that the region (formed by BamD engaged with POTRA domains 1-2 and 5 of BamA) is not sufficient to accommodate five β-strands. Structural analysis reveals that the interaction between the N-terminal side of BamD and POTRA1-2 is substantially changed the conformation by substrate binding, and that this surface is greatly extended. This surface does have enough space to accommodate five beta-strands, as now documented in Fig. 9D, 9E using the latest structures (7TT5 and 7TT2) as illustrations of this. The text now reads:

(Lines 506-515) "Spatially, this indicates the BamD can serve to organize two distinct parts of the nascent OMP substrate at the periplasmic face of the BAM complex, either prior to or in concert with, engagement to the lateral gate of BamA. Assessing this structurally showed the N-terminal region of BamD (interacting with the POTRA1-2 region of BamA) and the C-terminal region of BamD (interacting with POTRA5 proximal to the lateral gate of BamA) (Bakelar et al., 2016; Gu et al., 2016; Tomasek et al., 2020) has the N-terminal region of BamD changing conformation depending on the folding states of the last four β-strands of the substrate OMP, EspP (Doyle et al., 2022). The overall effect of this being a change in the dimensions of this cavity change, a change which is dependent on the folded state of the substrate engaged in it (Fig 9 B-E)."

ii. The second point raised regards the orientation of the substrate recognition residues of BamD. Both Y62A and R197 were located on the lumen side of the funnel in the EspP-BAM transport intermediate structure (PDBID;7TTC); Y62A is relatively located on the edge of BamD, but given that POTRA1-2 undergoes a conformational change and opens this region, as described above, both are located in locations where they could bind to substrates. This was explained in the following text in the results section of revised manuscript.

(Lines 377-379) "Each residue was located on the lumen side of the funnel-like structure in the EspP-BAM assembly intermediate structure (PDBID; 7TTC) (Doyle et al., 2022)."

**Reviewer #2 (Public Review):"

Previously, using bioinformatics study, authors have identified potential sequence motifs that are common to a large subset of beta-barrel outer membrane proteins in gram negative bacteria. Interestingly, in that study, some of those motifs are located in the internal strands of barrels (not near the termini), in addition to the well-known "beta-signal" motif in the C-terminal region.

Here, the authors carried out rigorous biochemical, biophysical, and genetic studies to prove that the newly identified internal motifs are critical to the assembly of outer membrane proteins and the interaction with the BAM complex. The author's approaches are rigorous and comprehensive, whose results reasonably well support the conclusions. While overall enthusiastic, I have some scientific concerns with the rationale of the neutron refractory study, and the distinction between "the intrinsic impairment of the barrel" vs "the impairment of interaction with BAM" that the internal signal may play a role in. I hope that the authors will be able to address this.

Strengths:

1. It is impressive that the authors took multi-faceted approaches using the assays on reconstituted, cell-based, and population-level (growth) systems.

2. Assessing the role of the internal motifs in the assembly of model OMPs in the absence and presence of BAM machinery was a nice approach for a precise definition of the role.

Weaknesses:

1. The result section employing the neutron refractory (NR) needs to be clarified and strengthened in the main text (from line 226). In the current form, the NR result seems not so convincing.

What is the rationale of the approach using NR?

We have now modified the text to make clear that:

(Lines 276-280) "The rationale to these experiments is that NR provides: (i) information on the distance of specified subunits of a protein complex away from the atomically flat gold surface to which the complex is attached, and (ii) allows the addition of samples between measurements, so that multi-step changes can be made to, for example, detect changes in domain conformation in response to the addition of a substrate."

What is the molecular event (readout) that the method detects?

We have now modified the text to make clear that:

(Lines 270-274) "While the biochemical assay demonstrated that the OmpC(Y286A) mutant forms a stalled intermediate with the BAM complex, in a state in which membrane insertion was not completed, biochemical assays such as this cannot elucidate where on BamA-BamD this OmpC(Y286A) substrate is stalled."

What are "R"-y axis and "Q"-x axis and their physical meanings (Fig. 5b)?

The neutron reflectivity, R, refers to the ratio of the incoming and exiting neutron beams and it is measured as a function of Momentum transfer Q, which is defined as Q=4π sinθ/λ, where θ is the angle of incident and λ is the neutron wavelength. R(Q)is approximately given byR(Q)=16π2/ Q2 |ρ(Q)|2, where R(Q) is the one-dimensional Fourier transform of ρ(z), the scattering length density (SLD) distribution normal to the surface. SLD is the sum of the coherent neutron scattering lengths of all atoms in the sample layer divided by the volume of the layer. Therefore, the intensity of the reflected beams is highly dependent on the thickness, densities and interface roughness of the samples. This was explained in the following text in the method section of revised manuscript.

(Lines 669-678) "Neutron reflectivity, denoted as R, is the ratio of the incoming to the exiting neutron beams. It’s calculated based on the Momentum transfer Q, which is defined by the formula Q=4π sinθ/λ, where θ represents the angle of incidence and λ stands for the neutron wavelength. The approximate value of R(Q) can be expressed as R(Q)=16π2/ Q2 |ρ(Q)|2, where R(Q) is the one-dimensional Fourier transform of ρ(z), which is the scattering length density (SLD) distribution perpendicular to the surface. SLD is calculated by dividing the sum of the coherent neutron scattering lengths of all atoms in a sample layer by the volume of that layer. Consequently, factors such as thickness, volume fraction, and interface roughness of the samples significantly influence the intensity of the reflected beams."

How are the "layers" defined from the plot (Fig. 5b)?

The “layers” in the plot (Fig. 5b) represent different regions of the sample being studied. In this study, we used a seven-layer model to fit the experimental data (chromium - gold - NTA - HIS8 - β-barrel - P3-5 - P1-2. This was explained in the following text in the figure legend of revised manuscript. (Lines 1115-1116) The experimental data was fitted using a seven-layer model: chromium - gold - NTA - His8 - β-barrel - P3-5 - P1-2.

What are the meanings of "thickness" and "roughness" (Fig. 5c)?

We used neutron reflectometry to determine the relative positions of BAM subunits in a membrane environment. The binding of certain subunits induced conformational changes in other parts of the complex. When a substrate membrane protein is added, the periplasmic POTRA domain of BamA extends further away from the membrane surface. This could result in an increase in thickness as observed in neutron reflectometry measurements.

As for roughness, it is related to the interface properties of the sample. In neutron reflectometry, the intensity of the reflected beams is highly dependent on the thickness, densities, and interface roughness of the samples. An increase in roughness could suggest changes in these properties, possibly due to protein-membrane interactions or structural changes within the membrane.

(Lines 1116-1120) "Table summarizes of the thickness, roughness and volume fraction data of each layer from the NR analysis. The thickness refers to the depth of layered structures being studied as measured in Å. The roughness refers to the irregularities in the surface of the layered structures being studied as measured in Å."

What does "SLD" stand for?

We apologize for not explaining abbreviation when the SLD first came out. We explained it in revised manuscript. (Line 298)

1. In the result section, "The internal signal is necessary for insertion step of assembly into OM" This section presents an important result that the internal beta-signal is critical to the intrinsic propensity of barrel formation, distinct from the recognition by BAM complex. However, this point is not elaborated in this section. For example, what is the role of these critical residues in the barrel structure formation? That is, are they involved in any special tertiary contacts in the structure or in membrane anchoring of the nascent polypeptide chains?

We appreciate the reviewer's comment on this point. Both position 0 and position 6 appear to be important amino acids for recognition by the BAM complex, since mutations introduced at these positions in peptide 18 prevent competitive inhibition activity.

In terms of the tertiary structure of OmpC, position 6 is an amino acid that contributes to the aromatic girdle, and since Y286A and Y365A affected OMP folding as measured in folding experiments, it is perhaps their position in the aromatic girdle that contributes to the efficiency of β-barrel folding in addition to its function as a recognition signal. We have added a sentence in the revised manuscript:

(Lines 233-236) "Position 6 is an amino acid that contributes to the aromatic girdle. Since Y286A and Y365A affected OMP folding as measured in folding experiments, their positioning into the aromatic girdle may contributes to the efficiency of β-barrel folding, in addition to contributing to the internal signal."

The mutations made at position 0 had no effect on folding, so this residue may function solely in the signal. Given the register of each β-strand in the final barrel, the position 0 residues have side-chains that face out into the lipid environment. From examination of the OmpC crystal structure, the residue at position 0 makes no special tertiary contacts with other, neighbouring residues.  

Reviewer #1 (Recommendations For The Authors):

Minor critiques (in no particular order):

1. Peptide 18 was identified based on its strong inhibition for EspP assembly but another peptide, peptide 23, also shows inhibition and has no particular consensus.

We would correct this point. Peptide 23 has a strong consensus to the canonical β-signal. We had explained the sequence consensus of β-signal in the Results section of the text. In the third paragraph, we have added a sentence indicating the relationship between peptide 18 and peptide 23.

(Lines 152-168) "Six peptides (4, 10, 17, 18, 21, and 23) were found to inhibit EspP assembly (Fig. 1A). Of these, peptide 23 corresponds to the canonical β-signal of OMPs: it is the final β-strand of OmpC and it contains the consensus motif of the β-signal (ζxGxx[Ω/Φ]x[Ω/Φ]). The inhibition seen with peptide 23 indicated that our peptidomimetics screening system using EspP can detect signals recognized by the BAM complex. In addition to inhibiting EspP assembly, five of the most potent peptides (4, 17, 18, 21, and 23) inhibited additional model OMPs; the porins OmpC and OmpF, the peptidoglycan-binding OmpA, and the maltoporin LamB (fig. S3). Comparing the sequences of these inhibitory peptides suggested the presence of a sub-motif from within the β-signal, namely [Ω/Φ]x[Ω/Φ] (Fig. 1B). The sequence codes refer to conserved residues such that: ζ, is any polar residue; G is a glycine residue; Ω is any aromatic residue; Φ is any hydrophobic residue and x is any residue (Hagan et al., 2015; Kutik et al., 2008). The non-inhibitory peptide 9 contained some elements of the β-signal but did not show inhibition of EspP assembly (Fig. 1A).

Peptide 18 also showed a strong sequence similarity to the consensus motif of the β-signal (Fig. 1B) and, like peptide 23, had a strong inhibitory action on EspP assembly (Fig. 1A). Variant peptides based on the peptide 18 sequence were constructed and tested in the EMM assembly assay (Fig. 1C)."

1. It is unclear why the authors immediately focused on BamD rather than BamB, given that both were mentioned to mediate interaction with substrate. Was BamB also tested?

We thank the reviewer for this comment. Following the reviewer's suggestion, we have now performed a pull-down experiment on BamB and added it to Fig. S9. We also modified the text of the results as follows.

(Lines 262-265) "Three subunits of the BAM complex have been previously shown to interact with the substrates: BamA, BamB, and BamD (Hagan et al., 2013; Harrison, 1996; Ieva et al., 2011). In vitro pull-down assay showed that while BamA and BamD can independently bind to the in vitro translated OmpC polypeptide (Fig .S9A), BamB did not (Fig. S9B)."

1. For the in vitro folding assays of the OmpC substrates, labeled and unlabeled, no mention of adding SurA or any other chaperone which is known to be important for mediating OMP biogenesis in vitro.

We appreciate the reviewer’s concerns on this point, however chaperones such as SurA are non-essential factors in the OMP assembly reaction mediated by the BAM complex: the surA gene is not essential and the assembly of OMPs can be measured in the absence of exogenously added SurA. It remains possible that addition of SurA to some of these assays could be useful in detailing aspects of chaperone function in the context of the BAM complex, but that was not the intent of this study.

1. For the supplementary document, it would be much easier for the reader to have the legends groups with the figures.

Following the reviewer's suggestion, we have placed the legends of Supplemental Figures together with each Figure.

1. Some of the figures and their captions are not grouped properly and are separated which makes it hard to interpret the figures efficiently.

We thank the reviewer for this comment, we have revised the manuscript and figures to properly group the figures and captions together on a single page.

1. The authors begin their 'Discussion' with a question (line 454), however, they don't appear to answer or even attempt to address it; suggest removing rhetorical questions.

As per the reviewers’ suggestion, we removed this question.

1. Line 464, 'unbiased' should be removed. This would imply that if not stated, experiments are 'negatively' biased.

We removed this word and revised the sentence as follows:

(Lines 431-433) "In our experimental approach to assess for inhibitory peptides, specific segments of the major porin substrate OmpC were shown to interact with the BAM complex as peptidomimetic inhibitors."

1. Lines 466-467; '...go well beyond expected outcomes.' What does this statement mean?

Our peptidomimetics led to unexpected results in elucidating the additional essential signal elements. The manuscript was revised as follows:

(Lines 433-435) "Results for this experimental approach went beyond expected outcomes by identifying the essential elements of the signal Φxxxxxx[Ω/Φ]x[Ω/Φ] in β-strands other than the C-terminal strand."

1. Line 478; '...rich information that must be oversimplified...'?

We appreciate the reviewer’s pointed out. For more clarity, the manuscript was revised as follows:

(Lines 450-453) "The abundance of information which arises from modeling approaches and from the multitude of candidate OMPs, is generally oversimplified when written as a primary structure description typical of the β-signal for bacterial OMPs (i.e. ζxGxx[Ω/Φ]x[Ω/Φ]) (Kutik et al., 2008)."

1. There are typos in the supplementary figures.

We have revised and corrected the Supplemental Figure legends.  

Reviewer #2 (Recommendations For The Authors):

1. In Supplementary Information, I recommend adding the figure legends directly to the corresponding figures. Currently, it is very inconvenient to go back and forth between legends and figures.

Following the reviewer's suggestion, we have placed the legends of Supplemental Figures together with each Figure.

1. Line 94 (p.3): "later"

Lateral?

Yes. We have corrected this.

1. Line 113 (p.3): The result section, "Peptidomimetics derived from E. coli OmpC inhibit OMP assembly" Rationale of the peptide inhibition assay is not clear. How can the peptide sequence that effectively inhibit the assembly interpreted as the b-assembly signal? By competitive binding to BAM or by something else? What is the authors' hypothesis in doing this assay?

In revision, we have added following sentence to explain the aim and design of the peptidomimetics:

(Lines 140-145) "The addition of peptides with BAM complex affinity, such as the OMP β-signal, are capable of exerting an inhibitory effect by competing for binding of substrate OMPs to the BAM complex (Hagan et al., 2015). Thus, the addition of peptides derived from the entirety of OMPs to the EMM assembly assay, which can evaluate assembly efficiency with high accuracy, expects to identify novel regions that have affinity for the BAM complex."

1. Line 113- (p.3) and Fig. S1: The result section, "Peptidomimetics derived from E. coli OmpC inhibit OMP assembly"

Some explanation seems to be needed why b-barrel domain of EspP appears even without ProK?

We appreciate the reviewer’s pointed out. We added following sentence to explain:

(Lines 128-137) "EspP, a model OMP substrate, belongs to autotransporter family of proteins. Autotransporters have two domains; (1) a β-barrel domain, assembled into the outer membrane via the BAM complex, and (2) a passenger domain, which traverses the outer membrane via the lumen of the β-barrel domain itself and is subsequently cleaved by the correctly assembled β-barrel domain (Celik et al., 2012). When EspP is correctly assembled into outer membrane, a visible decrease in the molecular mass of the protein is observed due to the self-proteolysis. Once the barrel domain is assembled into the membrane it becomes protease-resistant, with residual unassembled and passenger domains degraded (Leyton et al., 2014; Roman-Hernandez et al., 2014)."

1. Line 186 (p.6): "Y285"

Y285A?

We have corrected the error, it was Y285A.

1. Lines 245- (p. 7)/ Lines 330- (p. 10)

It needs to be clarified that the results described in these paragraphs were obtained from the assays with EMM.

We appreciate the reviewer’s concerns on these points. For the first half, the following text was added at the beginning of the applicable paragraph to indicate that all of Fig. 4 is the result of the EMM assembly assay.

(Line 241) "We further analyzed the role of internal β-signal by the EMM assembly assay. At the second half, we used purified BamD but not EMM. We described clearly with following sentence."

(Lines 316-318) "We purified 40 different BPA variants of BamD, and then irradiated UV after incubating with 35S-labelled OmpC."

Author response:

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

Reviewer #2 (Public Review):

The authors make a compelling case for the biological need to exquisitely control RecB levels, which they suggest is achieved by the pathway they have uncovered and described in this work. However, this conclusion is largely inferred as the authors only investigate the effect on cell survival in response to (high levels of) DNA damage and in response to two perturbations - genetic knock-out or over-expression, both of which are likely more dramatic than the range of expression levels observed in unstimulated and DNA damage conditions.

In the discussion of the updated version of the manuscript, we have clarified the limits of our interpretation of the role of the uncovered regulation.

Lines 411-417: “It is worth noting that the observed decrease in cell viability upon DNA damage was detected for relatively drastic perturbations such as recB deletion and RecBCD overexpression. Verifying these observations in the context of more subtle changes in RecB levels would be important for further investigation of the biological role of the uncovered regulation mechanism. However, the extremely low numbers of RecB proteins make altering its abundance in a refined, controlled, and homogeneous across cells manner extremely challenging and would require the development of novel synthetic biology tools.”

Reviewer #3 (Public Review):

The major weaknesses include a lack of mechanistic depth, and part of the conclusions are not fully supported by the data.

(1) Mechanistically, it is still unclear why upon DNA damage, translation level of recB mRNA increases, which makes the story less complete. The authors mention in the Discussion that a moderate (30%) decrease in Hfq protein was observed in previous study, which may explain the loss of translation repression on recB. However, given that this mRNA exists in very low copy number (a few per cell) and that Hfq copy number is on the order of a few hundred to a few thousand, it's unclear how 30% decrease in the protein level should resides a significant change in its regulation of recB mRNA.

We agree that the entire mechanistic pathway controlling recB expression may be not limited to just Hfq involvement. We have performed additional experiments, proposed by the reviewer, suggesting that a small RNA might be involved (see below, response to comments 3&4). However, we consider that the full characterisation of all players is beyond the scope of this manuscript. In addition to describing the new data (see below), we expanded the discussion to explain more precisely why changes in Hfq abundance upon DNA damage may impact RecB translation. 

Lines 384-391: “A modest decrease (~30%) in Hfq protein abundance has been seen in a proteomic study in E. coli upon DSB induction with ciprofloxacin (DOI: 10.1016/j.jprot.2018.03.002). While Hfq is a highly abundant protein, it has many mRNA and sRNA targets, some of which are also present in large amounts (DOI: 10.1046/j.1365-2958.2003.03734.x). As recently shown, the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes, where the targets with higher Hfq binding affinity have an advantage over the ones with less efficient binding (DOI: 10.1016/j.celrep.2020.02.016). In line with these findings, it is conceivable that even modest changes in Hfq availability could result in significant changes in gene expression, and this could explain the increased translational efficiency of RecB under DNA damage conditions. “

(2) Based on the experiment and the model, Hfq regulates translation of recB gene through binding to the RBS of the upstream ptrA gene through translation coupling. In this case, one would expect that the behavior of ptrA gene expression and its response to Hfq regulation would be quite similar to recB. Performing the same measurement on ptrA gene expression in the presence and absence of Hfq would strengthen the conclusion and model.

Indeed, based on our model, we expect PtrA expression to be regulated by Hfq in a similar manner to RecB. However, the product encoded by the ptrA gene, Protease III, (i) has been poorly characterised; (ii) unlike RecB, is located in the periplasm (DOI: 10.1128/jb.149.3.1027-1033.1982); and (iii) is not involved in any DNA repair pathway. Therefore, analysing PtrA expression would take us away from the key questions of our study.

(3) The authors agree that they cannot exclude the possibility of sRNA being involved in the translation regulation. However, this can be tested by performing the imaging experiments in the presence of Hfq proximal face mutations, which largely disrupt binding of sRNAs.

(4) The data on construct with a long region of Hfq binding site on recB mRNA deleted is less convincing. There is no control to show that removing this sequence region itself has no effect on translation, and the effect is solely due to the lack of Hfq binding. A better experiment would be using a Hfq distal face mutant that is deficient in binding to the ARN motifs.

We performed the requested experiments. We included this data in the manuscript in the supplementary figure (Figure S11), and our interpretation in the discussion.

Lines 354-378: “While a few recent studies have shown evidence for direct gene regulation by Hfq in a sRNA-independent manner (DOI: 10.1101/gad.302547.117; DOI: 10.1111/mmi.14799; DOI: 10.1371/journal.pgen.1004440; DOI: 10.1111/mmi.12961; DOI: 10.1038/emboj.2013.205), we attempted to investigate whether a small RNA could be involved in the Hfq-mediated regulation of RecB expression. We tested Hfq mutants containing point mutations in the proximal and distal sides of the protein, which were shown to disrupt either binding with sRNAs or with ARN motifs of mRNA targets, respectively [DOI: 10.1016/j.jmb.2013.01.006, DOI: 10.3389/fcimb.2023.1282258]. Hfq mutated in either proximal (K56A) or distal (Y25D) faces were expressed from a plasmid in a ∆hfq background. In both cases, Hfq expression was confirmed with qPCR and did not affect recB mRNA levels (Supplementary Figure S11b). When the proximal Hfq binding side (K56A) was disrupted, RecB protein concentration was nearly similar to that obtained in a ∆hfq mutant (Supplementary Figure S11a, top panel). This observation suggests that the repression of RecB translation requires the proximal side of Hfq, and that a small RNA is likely to be involved as small RNAs (Class I and Class II) were shown to predominantly interact with the proximal face of Hfq [DOI: 10.15252/embj.201591569]. When we expressed Hfq mutated in the distal face (Y25D) which is deficient in binding to mRNAs, less efficient repression of RecB translation was detected (Supplementary Figure S11a, bottom panel). This suggests that RecB mRNA interacts with Hfq at this position. We did not observe full de-repression to the ∆hfq level, which might be explained by residual capacity of Hfq to bind its recB mRNA target in the point mutant (Y25D) (either via the distal face with less affinity or via the lateral rim Hfq interface).”

Taken together, these results suggest that Hfq binds to recB mRNA and that a small RNA might contribute to the regulation although this sRNA has not been identified.

(5) Ln 249-251: The authors claim that the stability of recB mRNA is not changed in ∆hfq simply based on the steady-state mRNA level. To claim so, the lifetime needs to be measured in the absence of Hfq.

We measured recB lifetime in the absence of Hfq in a time-course experiment where transcription initiation was inhibited with rifampicin and mRNA abundance was quantified with RT-qPCR. The results confirmed that recB mRNA lifetime in hfq mutants is similar to the one in the wild type (Figure S7d, referred to the line 263 of the manuscript).

(6) What's the labeling efficiency of Halo-tag? If not 100% labeled, is it considered in the protein number quantification? Is the protein copy number quantification through imaging calibrated by an independent method? Does Halo tag affect the protein translation or degradation?

Our previous study (DOI: 10.1038/s41598-019-44278-0) described a detailed characterization of the HaloTag labelling technique for quantifying low-copy proteins in single E. coli cells using RecB as a test case. 

In that study, we showed complete quantitative agreement of RecB quantification between two fully independent methods: HaloTag-based labelling with cell fixation and RecB-sfGFP combined with a microfluidic device that lowers protein diffusion in the bacterial cytoplasm. This second method had previously been validated for protein quantification (DOI: 10.1038/ncomms11641) and provides detection of 80-90% of the labelled protein. Additionally, in our protocol, immediate chemical fixation of cells after the labelling and quick washing steps ensure that new, unlabelled RecB proteins are not produced. We, therefore, conclude that our approach to RecB detection is highly reliable and sufficient for comparing RecB production in different conditions and mutants.

The RecB-HaloTag construct has been designed for minimal impact on RecB production and function. The HaloTag is translationally fused to RecB in a loop positioned after the serine present at position 47 where it is unlikely to interfere with (i) the formation of RecBCD complex (based on RecBCD structure, DOI: 10.1038/nature02988), (ii) the initiation of translation (as it is far away from the 5’UTR and the beginning of the open reading frame) and (iii) conventional C-terminalassociated mechanisms of protein degradation (DOI: 10.15252/msb.20199208). In our manuscript, we showed that the RecB-HaloTag degradation rate is similar to the dilution rate due to bacterial growth. This is in line with a recent study on unlabelled proteins, which shows that RecB’s lifetime is set by the cellular growth rate (DOI: 10.1101/2022.08.01.502339).

Furthermore, we have demonstrated (DOI: 10.1038/s41598-019-44278-0) that (i) bacterial growth is not affected by replacing the native RecB with RecB-HaloTag, (ii) RecB-HaloTag is fully functional upon DNA damage, and (iii) no proteolytic processing of the RecB-HaloTag is detected by Western blot. 

These results suggest that RecB expression and functionality are unlikely to be affected by the translational HaloTag insertion at Ser-47 in RecB.

In the revised version of the manuscript, we have added information about the construct and discuss the reliability of the quantification.

Lines 141-152: “To determine whether the mRNA fluctuations we observed are transmitted to the protein level, we quantified RecB protein abundance with singlemolecule accuracy in fixed individual cells using the Halo self-labelling tag (Fig. 2A&B).

The HaloTag is translationally fused to RecB in a loop after Ser47(DOI: 10.1038/s41598-019-44278-0) where it is unlikely to interfere with the formation of RecBCD complex (DOI: 10.1038/nature02988), the initiation of translation and conventional C-terminal-associated mechanisms of protein degradation (DOI: 10.15252/msb.20199208). Consistent with minimal impact on RecB production and function, bacterial growth was not affected by replacing the native RecB with RecBHaloTag, the fusion was fully functional upon DNA damage and no proteolytic processing of the construct was detected (DOI: 10.1038/s41598-019-44278-0). To ensure reliable quantification in bacteria with HaloTag labelling, the technique was previously verified with an independent imaging method and resulted in > 80% labelling efficiency (DOI: 10.1038/s41598-019-44278-0, DOI: 10.1038/ncomms11641). In order to minimize the number of newly produced unlabelled RecB proteins, labelling and quick washing steps were followed by immediate chemical fixation of cells.”

Lines 164-168: “Comparison to the population growth rate [in these conditions (0.017 1/min)] suggests that RecB protein is stable and effectively removed only as a result of dilution and molecule partitioning between daughter cells. This result is consistent with a recent high-throughput study on protein turnover rates in E. coli, where the lifetime of RecB proteins was shown to be set by the doubling time (DOI: 10.1038/s41467-024-49920-8).”

(7) Upper panel of Fig S8a is redundant as in Fig 5B. Seems that Fig S8d is not described in the text.

We have now stated in the legend of Fig S8a that the data in the upper panel were taken from Fig 5B to visually facilitate the comparison with the results given in the lower panel. We also noticed that we did not specify that in the upper panel in Fig S9a (the data in the upper panel of Fig S9a was taken from Fig 5C for the same reason). We added this clarification to the legend of the Fig S9 as well.

We referred to the Fig S8d in the main text. 

Lines 283-284: “We confirmed the functionality of the Hfq protein expressed from the pQE-Hfq plasmid in our experimental conditions (Fig. S8d).”

Reviewer #1 (Recommendations For The Authors):

(1) Experimental regime to measure protein and mRNA levels.

(a) Authors expose cells to ciprofloxacin for 2 hrs. They provide a justification via a mathematical model. However, in the absence of a measurement of protein and mRNA across time, it is unclear whether this single time point is sufficient to make the conclusion on RecB induction under double-strand break.

In our experiments, we only aimed to compare recB mRNA and RecB protein levels in two steady-state conditions: no DNA damage and DNA damage caused by sublethal levels of ciprofloxacin. We did not aim to look at RecB dynamic regulation from nondamaged to damaged conditions – this would indeed require additional measurements at different time points. We revised this part of the results to ensure that our conclusions are stated as steady-state measurements and not as dynamic changes.

Line 203-205: “We used mathematical modelling to verify that two hours of antibiotic exposure was sufficient to detect changes in mRNA and protein levels and for RecB mRNA and protein levels to reach a new steady state in the presence of DNA damage.”

(b) Authors use cell area to account for the elongation under damage conditions. However, it is unclear whether the number of copies of the recB gene are similar across these elongated cells. Hence, authors should report mRNA and protein levels with respect to the number of gene copies of RecB or chromosome number as well.

Based on the experiments in DNA damaging conditions, our main conclusion is that the average translational efficiency of RecB is increased in perturbed conditions. We believe that this conclusion is well supported by our measurements and that it does not require information about the copy number of the recB gene but only the concentration of mRNA and protein. We did observe lower recB mRNA concentration upon DNA damage in comparison to the untreated conditions, which may be due to a lower concentration of genomic DNA in elongated cells upon DNA damage, as we mention in lines (221-223).

Our calculation of translation efficiency could be affected by variations of mRNA concentration across cells in the dataset. For example, longer cells that are potentially more affected by DNA damage could have lower concentrations of mRNA. We verified that this is not the case, as recB mRNA concentration is constant across cell size distribution (see the figure below or Figure S5a from Supplementary Information).

Therefore, we do not think that the measurements of recB gene copy would change our conclusions. We agree that measuring recB gene copies could help to investigate the reason behind the lower recB mRNA concentration under the perturbed conditions as this could be due to lower DNA content or due to shortage of resources (such as RNA polymerases). However, this is a side observation we made rather than a critical result, whose investigation is beyond the scope of this manuscript.

Author response image 1.

(2) RecB as a proxy for RecBCD. Authors suggest that RecB levels are regulated by hfq. However, how does this regulatory circuit affect the levels of RecC and RecD? Ratio of the three proteins has been shown to be important for the function of the complex.

A full discussion of RecBCD complex formation regulation would require a complete quantitative model based on precise information on the dynamic of the complex formation, which is currently lacking. 

We can however offer the following (speculative) suggestions assuming that all three subunits are present in similar abundance in native conditions (DOI: 10.1038/s41598019-44278-0 for RecB and RecC). As the complex is formed in 1:1:1 ratio (DOI: 10.1038/nature02988), we propose that the regulation mechanism of RecB expression affects complex formation in the following way. If the RecB abundance becomes lower than the level of RecC and RecD subunits, the complex formation would be limited by the number of available RecB subunits and hence the number of functional RecBCDs will be decreased. On the contrary, if the number of RecB is higher than the baseline, then, especially in the context of low numbers, we would expect that the probability of forming a complex RecBC (and then RecBCD) will be increased. Based on this simple explanation, we might speculate that regulation of RecB expression may be sufficient to regulate RecB levels and RecBCD complex formation. However, we feel that this argument is too speculative to be added to the manuscript. 

(3) Role of Hfq in RecB regulation. While authors show the role of hfq in recB translation regulation in non-damage conditions, it is unclear as to how this regulation occurs under damage conditions.

(a) Have the author carried out recB mRNA and protein measurement in hfqdeleted cells under ciprofloxacin treatment?

We attempted to perform experiments in hfq mutants under ciprofloxacin treatment. However, the cells exhibited a very strong and pleiotropic phenotype: they had large size variability and shape changes and were also frequently lysing. Therefore, we did not proceed with mRNA and protein quantification because the data would not have been reliable. 

(b) How do the authors propose that Hfq regulation is alleviated under conditions of DNA damage, when RecB translation efficiency increases?

We propose that Hfq could be involved in a more global response to DNA damage as follows. 

Based on a proteomic study where Hfq protein abundance has been found to decrease (~ 30%) upon DSB induction with ciprofloxacin (DOI: 10.1016/j.jprot.2018.03.002), we suggest that this could explain the increased translational efficiency of RecB. While Hfq is a highly abundant protein, it has many targets (mRNA and sRNA), some of which are also highly abundant. Therefore the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes (DOI: 10.1046/j.13652958.2003.03734.x), where the targets with higher Hfq binding affinity have an advantage over the ones with less efficient binding. We reason that upon DNA damage, a moderate decrease in the Hfq protein abundance (30%) can lead to a similar competition among Hfq targets where high-affinity targets outcompete low-affinity ones as well as low-abundant ones (such as recB mRNAs). Thus, the regulation of lowabundant targets of Hfq by moderate perturbations of Hfq protein level is a potential explanation for the change in RecB translation that we have observed. Potential reasons behind the changes of Hfq levels upon DNA damage would be interesting to explore, however this would require a completely different approach and is beyond the scope of this manuscript.

We have modified the text of the discussion to explain our reasoning:

Lines 384-391: “A modest decrease (~30%) in Hfq protein abundance has been seen in a proteomic study in E. coli upon DSB induction with ciprofloxacin (DOI: 10.1016/j.jprot.2018.03.002). While Hfq is a highly abundant protein, it has many mRNA and sRNA targets, some of which are also present in large amounts (DOI: 10.1046/j.1365-2958.2003.03734.x). As recently shown, the competition among the targets over Hfq proteins results in unequal (across various targets) outcomes, where the targets with higher Hfq binding affinity have an advantage over the ones with less efficient binding (DOI: 10.1016/j.celrep.2020.02.016). In line with these findings, it is conceivable that even modest changes in Hfq availability could result in significant changes in gene expression, and this could explain the increased translational efficiency of RecB under DNA damage conditions.”

(c) Is there any growth phenotype associated with recB mutant where hfq binding is disrupted in damage and non-damage conditions? Does this mutation affect cell viability when over-expressed or under conditions of ciprofloxacin exposure?

We checked the phenotype and did not detect any difference in growth or cell viability affecting the recB-5 UTR* mutants either in normal conditions or upon exposure to ciprofloxacin. However, this is expected because the repair capacity is associated with RecB protein abundance and in this mutant, while translational efficiency of recB mRNA increases, the level of RecB proteins remains similar to the wild-type (Figure 5E).

Minor points:

(1) Introduction - authors should also discuss the role of RecFOR at sites of fork stalling, a likely predominant pathway for break generated at such sites.

The manuscript focuses on the repair of DNA double-strand breaks (DSBs). RecFOR plays a very important role in the repair of stalled forks because of single-strand gaps but is not involved in the repair of DSBs (DOI: 10.1038/35003501). We have modified the beginning of the introduction to mention the role of RecFOR. 

Lines 35-39: “For instance, replication forks often encounter obstacles leading to fork reversal, accumulation of gaps that are repaired by the RecFOR pathway (DOI: 10.1038/35003501) or breakage which has been shown to result in spontaneous DSBs in 18% of wild-type Escherichia coli cells in each generation (DOI: 10.1371/journal.pgen.1007256), underscoring the crucial need to repair these breaks to ensure faithful DNA replication.”

(2) Methods: The authors refer to previous papers for the method used for single RNA molecule detection. More information needs to be provided in the present manuscript to explain how single molecule detection was achieved.

We added additional information in the method section on the fitting procedure allowing quantifying the number of mRNAs per detected focus.

Lines 515-530: “Based on the peak height and spot intensity, computed from the fitting output, the specific signal was separated from false positive spots (Fig. S1a). To identify the number of co-localized mRNAs, the integrated spot intensity profile was analyzed as previously described (DOI: 10.1038/nprot.2013.066). Assuming that (i) probe hybridization is a probabilistic process, (ii) binding each RNA FISH probe happens independently, and (iii) in the majority of cases, due to low-abundance, there is one mRNA per spot, it is expected that the integrated intensities of FISH probes bound to one mRNA are Gaussian distributed. In the case of two co-localized mRNAs, there are two independent binding processes and, therefore, a wider Gaussian distribution with twice higher mean and twice larger variance is expected. In fact, the integrated spot intensity profile had a main mode corresponding to a single mRNA per focus, and a second one representing a population of spots with two co-localized mRNAs (Fig. S1b). Based on this model, the integrated spot intensity histograms were fitted to the sum of two Gaussian distributions (see equation below where a, b, c, and d are the fitting parameters), corresponding to one and two mRNA molecules per focus. An intensity equivalent corresponding to the integrated intensity of FISH probes in average bound to one mRNA was computed as a result of multiple-Gaussian fitting procedure (Fig. S1b), and all identified spots were normalized by the one-mRNA equivalent.

“

Reviewer #2 (Recommendations For The Authors):

Overall the work is carefully executed and highly compelling, providing strong support for the conclusions put forth by the authors.

One point: the potential biological consequences of the post-transcriptional mechanism uncovered in the work would be enhanced if the authors could 1) tune RecB protein levels and 2) directly monitor the role that RecB plays in generating single-standed DNA at DSBs.

We agree that testing viability of cells in case of tunable changes in RecB levels would be important to further investigate the biological role of the uncovered regulation mechanism. However, this is a very challenging experiment as it is technically difficult to alter the low number of RecB proteins in a controlled and homogeneous across-cell manner, and it would require the development of precisely tunable and very lowabundant synthetic designs. 

We did monitor real-time RecB dynamics by tracking single molecules in live E. coli cells in a different study (DOI: 10.1101/2023.12.22.573010) that is currently under revision. There, reduced motility of RecB proteins was observed upon DSB induction indicating that RecB is recruited to DNA to start the repair process.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

To gain further insight into the dynamics of microglial aging in the hippocampus, the authors used a bioinformatics method known as "pseudotime" or "trajectory inference" to understand how cells may progress through different functional states, as defined by cellular transcriptome (15,16). These bioinformatics approaches can reveal key patterns in scRNAseq / snRNAseq datasets and, in the present study, the authors conclude that a "stress response" module characterized by expression of TGFb1 represents a key "checkpoint" in microglial aging in midlife, after which the cells can move along distinct transcriptional trajectories as aging progresses. This is an intriguing possibility. However, pseudotime analyses need to be validated via additional bioinformatics as well as follow-up experiments. Indeed, Heumos et al, in their Nature Genetics "Expert Guidelines" Review, emphasize that "inferred trajectories might not necessarily have biological meaning." They recommend that "when the expected topology is unknown, trajectories and downstream hypotheses should be confirmed by multiple trajectory inference methods using different underlying assumptions."(15) Numerous algorithms are available for trajectory inference (e.g. Monocle, PAGA, Slingshot, RaceID/StemID, among many others) and their performance and suitability depends on the individual dataset and nature of the trajectories that are to be inferred. It is recommended to use dynGuidelines(16) for the selection of optimal pseudotime analysis methods. In the present manuscript, the authors do not provide any justification for their use of Monocle 3 over other trajectory inference approaches, nor do they employ a secondary trajectory inference method to confirm observations made with Monocle 3. Finally, follow-up validation experiments that the authors carry out have their own limitations and caveats (see below). Hence, while the microglial aging trajectories identified by this study are intriguing, they remain hypothetical trajectories that need to be proven with additional follow-up experiments.

We thank the reviewer for their suggestion. We have utilized the dynGuidelines kindly provided by the reviewer to utilize an additional trajectory inference tool to analyze our data. We selected Scorpius based on the structure of our data. The tool has provided additional support that microglia progress from a homeostatic state (Cx3cr1, Mef2c) to the induction of stress genes (Hspa1, Atf3) at an intermediate point during aging progression. Furthermore, we observe a concordant increase in ribosomal protein genes at a time point in the pseudotime analysis immediately prior to activation of inflammation-related genes (Il1b, Cst7). These additional analyses support the main findings of our original pseudotime analysis and have been added to the manuscript as Figure S3C,D. Additionally, in the statistical test that uncovers differentially expressed genes along the pseudotime trajectory in this analyses, we find that Tgfb1 is one of the genes that is differentially expressed with peak expression at an intermediate timepoint along the pseudotime trajectory. Furthermore, we have done some preliminary trajectory analysis with slingshot (Street et al, BMC Genomics, PMID: 29914354) that found a similar trajectory with analogous gene expression patterns and dynamic expression of Tgfb1.

To follow up on the idea that TGFb1 signaling in microglia plays a key role in determining microglial aging trajectories, the authors use RNAscope to show that TGFb1 levels in microglia peak in middle age. They also treat primary LPS-activated microglia with TGFb1 and show that this restores expression of microglial homeostatic gene expression and dampens expression of stress response and, potentially, inflammatory genes. Finally, they utilize transgenic approaches to delete TGFb1 from microglia around 8-10mo of age and scRNAseq to show that homeostatic signatures are lost and inflammatory signatures are gained. Hence, findings in this study support the idea that TGFb1 can strongly regulate microglial phenotype. Loss of TGFb1 signaling to microglia in adulthood has already been shown to cause decreased microglial morphological complexity and upregulation of genes typically associated with microglial responses to CNS insults(17-19). TGFb1 signaling to microglia has also been implicated in microglial responses to disease and manipulations to increase this signaling can improve disease progression in some cases(19). In this light, the findings in the present study are largely confirmatory of previous findings in the literature. They also fall short of unequivocally demonstrating that TGFb1 signaling acts as a "checkpoint" for determining subsequent microglial aging trajectory. To show this clearly, one would need to perturb TGFb1 signaling around 12mo of age and carry out sequencing (bulkRNAseq or scRNAseq) of microglia at 18mo and 24mo. Such experiments could directly demonstrate whether the whole microglial population has been diverted to the TGFb1-low aging trajectory (that progresses through a translational burst state to an inflammation state as proposed). Future development of tools to tag TGFb1 high or low microglia could also enable fate tracing type experiments to directly show whether the TGFb1 state in middle age predicts cell state at later phases of aging.

We apologize for the use of the term “checkpoint” when referring to the role of Tgfb1 in microglial aging. Instead, our model posits that Tgfb1 expression increases in response to the early insults of the aging process in an attempt to return microglia to homeostasis. Therefore, this would predict that increasing TGFB1 levels after an insult would decrease activation and age-related progression of microglia, which we demonstrate in vitro (Figure 3). Alternatively, the loss of TGFB1 should prevent microglia from returning to a homeostatic state after an age-related stressor, and thus increase the number of microglia in activated states. We observe this increase in activated microglia in our middle-aged microglia-specific Tgfb1 knockout mouse model. Furthermore, the haploinsufficiency of Tgfb1 at this age indicates that TGFB1 signaling in microglia is sensitive to relative levels of Tgfb1. The transient increase in Tgfb1 expression further suggests that the threshold for TGFB1 signaling is dynamic. Finally, RNA-Seq analysis of both in vitro TGFB1 supplemented microglia and in vivo Tgfb1 depleted microglia highlight that TGFB1 alters the aging microglia transcriptome. Combined, these results provide evidence that Tgfb1 modulates advancement of microglia through an aging continuum.

The present study would also like to draw links between features of microglial aging in the hippocampus and a decline in hippocampal-dependent cognition during aging. To this end, they carry out behavioral testing in 8-10mo old mice that have undergone microglial-specific TGFb1 deletion and find deficits in novel object recognition and contextual fear conditioning. While this provides compelling evidence that TGFb1 signaling in microglia can impact hippocampus-dependent cognition in midlife, it does not demonstrate that this signaling accelerates or modulates cognitive decline (see below). Age-associated cognitive decline refers to cognitive deficits that emerge as a result of the normative brain aging process (20-21). For a cognitive deficit to be considered age-associated cognitive decline, it must be shown that the cognitive operation under study was intact at some point earlier in the adult lifespan. This requires longitudinal study designs that determine whether a manipulation impacts the relationship between brain status and cognition as animals age (22-24). Alternatively, cross-sectional studies with adequate sample sizes can be used to sample the variability in cognitive outcomes at different points of the adult lifespan (22-24) and show that this is altered by a particular manipulation. For this specific study, one would ideally demonstrate that hippocampal-based learning/memory was intact at some point in the lifespan of mice with microglial TGFb1 KO but that this manipulation accelerated or exacerbated the emergence of deficits in hippocampal-dependent learning/memory during aging. In the absence of these types of data, the authors should tone down their claims that they have identified a cellular and molecular mechanism that contributes to cognitive decline.

We agree with the reviewer that to adequately demonstrate an age-dependent effect of microglia-derived TGFB1 on cognition it is necessary to perturb microglial TGFB1 at young and mature ages and assess the age-dependent effect on cognition. To address this, we have now performed a complementary behavioral study utilizing the Tmem119-CreER mouse model to drive the microglia-specific excision of Tgfb1 in two separate cohorts of mice – one young (2-3 months) and one in mature mice (7-8 months) – followed by cognitive testing. Using the novel object recognition test, we find that young mice of all genotypes (WT, Tgfb1 Het and Tgfb1 cKO ) retain the ability to recognize the novel object (as determined by having a significant preference in exploring the novel object). Alternatively, only the WT mature mice demonstrate a preference for the novel object, while the Tgfb1 Het and Tgfb1 cKO show no preference for the novel object. These behavioral data demonstrate an age-dependent necessity for microglia-specific TGFB1 in in maintain proper hippocampal-dependent memory and is now included in the manuscript as revised Figure 4I-J. We have also included additional behavioral tests (Y-Maze and open field) that did not show any difference between the genotypes as Figure S6D-G. Unfortunately, we were unable to perform the fear conditioning testing, as our apparatus broke during this time. Together, these results reveal that there is an age-dependent necessity for microglia-derived TGFB1 for hippocampal-dependent cognitive function.

A final point of clarification for the reader pertains to the mining of previously generated data sets within this study. The language in the results section, methods, and figure legends causes confusion about which experiments were actually carried out in this study versus previous studies. Some of the language makes it sound as though parabiosis experiments and experiments using mouse models of Alzheimer's Disease were carried out in this study. However, parabiosis and AD mouse model experiments were executed in previous studies (25,26), and in the present study, RNAseq datasets were accessed for targeted data mining. It is fantastic to see further mining of datasets that already exist in the field. However, descriptions in the results and methods sections need to make it crystal clear that this is what was done.

The reviewer makes an excellent point. While we referenced the public dataset in the original manuscript, the citation style of superscripted numbers diminishes our ability to adequately reference the datasets. Therefore, we have added the names of the first authors (Palovics for the parabiosis dataset and Sala Frigerio for the Alzheimer’s Disease dataset) to all the instances in the results and figure legends when we refer to these datasets.

Additional recommendations:

Major comments.

(1) There is some ambiguity surrounding how to interpret the microglial TGFb1 knockout that seems incompatible with viewing this molecule as a "checkpoint" in microglial aging. TGFb1 is believed to be primarily produced by microglia. Secreted TGFb1 is then detected by microglial TGFbR2. Are the microglia that have high levels of TGFb1 in middle age signaling to themselves (autocrine signaling)? Or contributing to a local milieu that impacts multiple neighbor microglia (paracrine signaling)? The authors could presumably look in their own dataset to evaluate microglial capacity to detect TGFb1 via its receptors.

We thank the reviewer for this insightful suggestion. We have undertaken analysis of our dataset to assess whether Tgfb1 acts through autocrine or paracrine signaling. To do so, we reanalyzed our microglia aging scRNA-Seq dataset leveraging the variation in microglia Tgfb1 expression to probe the relative activity of TGFB1. Specifically, we partitioned microglia into quartiles based on their Tgfb1 expression, and subsequently investigated the expression of TGFB signaling effectors and targets. High expression of downstream TGFB signaling pathway components in microglia with high Tgfb1 expression would point to autocrine mechanisms while, alternatively, high expression of downstream TGFB signaling pathway components in microglia with low Tgfb1 expression would point to paracrine mechanisms. We observed highest expression of TGFB signaling pathway components and targets in microglia with the highest expression of Tgfb1. These data suggest that Tgfb1 acts through an autocrine mechanism. These results have been added to our manuscript as Figure S4E-G. Additionally, while our manuscript was under review, a paper by Bedolla et al (Nature Communications 2024; PMID: 38906887) was published that investigated the role of Tgfb1 in adult microglia. This paper utilized orthogonal techniques – sparse microglia-specific Tgfb1 knockout and IHC - to also suggest that microglia utilize autocrine Tgfb1 signaling. Together, these complementary data provide strong evidence that Tgfb1 acts through an autocrine mechanism in adult microglia.

(2) Conclusions of the study rest on the assumption that microglial inflammatory responses are a central driver of cognitive decline. They assume that manipulations that increase microglial progression into an inflammatory state will negatively impact cognitive function. Although there are certainly a lot of data in the field that inflammatory factors can impact synaptic function, additional experiments would be required to unequivocally demonstrate that a "TGFb1 dependent" progression of microglia to an inflammatory state underlies any observed changes in cognition. For example, in the context of microglial TGFb1 deletion, can NSAIDs or blockers of soluble TNFa (e.g. XENP345), or blockers of SPP1, etc. rescue behavior? Can microglial depletion in this context rescue behavior? Assuming behavior was carried out in the same microglial TGFb1 KO mice that were used for microglial scRNAseq, they could also carry out linear regression-type analyses to link microglial inflammatory status to the behavioral performance of individual mice. In the absence of additional evidence of this sort, the authors should tone down claims about mechanistic relationships between microglial state and cognitive performance.

We thank the reviewer for realizing that the link between cognition and inflammation in our paper is speculative. Therefore, we have taken the reviewer’s advice and toned down the claims linking inflammation to cognition in our manuscript. Instead, we connect the disruption in cognition to what is observed in our data, a loss of microglia homeostasis and a shift in the microglia aging trajectories.

Additional Recommendations:

Minor comments:

(1) Ideally at some point in the results or discussion, the authors should acknowledge that the hippocampus has highly distinct sub-regions and that microglia show different functions and properties across these sub-regions (e.g. microglia in hilus and subgranular zone vs microglia in stratum radiatum, vs microglia immediately adjacent to or embedded within stratum pyrimidale). Do expression levels of TGFb1 and microglial aging trajectories vary across sub-regions? To what extent can this account for heterogeneity of aging trajectories observed in microglial aging within the hippocampus?

We are interested in how microglia heterogeneity during aging is influenced by the specific functions, and thus microenvironments within the hippocampus. Therefore, we have expanded our IHC analysis of microglia to determine how the microenvironment influences microglia phenotypes by looking at several different regions of the hippocampus. We have included this regional analysis as Figure S2 in the manuscript. This analysis has revealed region-specific effects on microglia activation during aging.

(2) For immunohistochemistry data, it is not particularly convincing to see one example of one cell from each condition. Generally, an accepted approach in the field is to present lower magnification images accompanied by zoom panels for several cells from each field of view. This reassures the reader that specific cells haven't simply been "cherry-picked" to support a particular conclusion.

To allay the concerns of the reviewer that cells haven’t been “cherry-picked”, we have provided low magnification images for the aging CD68 and NF_κB stains in Supplemental Figure S2.

(3) In immunohistochemistry data, have measures been taken to ensure that observed signals are not simply autofluorescence that becomes prominent in tissues with aging? (i.e. use of trueblack or photoquenching of tissue prior to staining) See PMID 37923732

We agree that autofluorescence, at least partially due to the accumulation of lipofuscin, becomes prominent in certain regions and cells of the hippocampus during aging. This most prominently occurs in the microglia of the hilus. This autofluorescence has a particular subcellular distribution, as it is localized to lyso-endosomal bodies. The microglia activation marker CD68 is also localized to lysosomes. A previous publication by Burns et al (eLife; PMID: 32579115) identified autofluorescent microglia (AF+) with unique molecular profiles that accumulate with age. They posited that these AF+ microglia resembled other microglia subsets that have pronounced storage compartments, such as the pro-inflammatory lipid droplet-containing microglia that accumulate with age reported by Marschallinger et al (Nature; PMID: 31959936). As such, autofluorescence present in microglia potentially represents distinctive and functional states of microglia. Our CD68 immunostaining accumulates with age, which could overlap with autofluorescent storage bodies. Thus, we performed a complementary CD68 immunostaining in an independent cohort of young (3 months) and aged (24 months) mice with autofluorescence quencher TrueBlack, and found that the staining pattern and accumulation of CD68 microglia with age persisted as previously observed after use of this quencher (see Authpr response image 1). Images are IBA1 (cyan) and CD68 (yellow) with the molecular layer (ML), granule cell (GC), and hilus illustrated and corresponding quantification provided (Two-way ANOVA with Sidak’s multiple comparisons test; ***P<0.001; ****P<0.0001).

We would like to note that the subcellular localization of the other immunostainings included in the manuscript was distinct from CD68, and not likely to be associated with the autofluorescent storage bodies. Additionally, our RNAScope staining for Tgfb1 did not show an accumulation with age, but rather a transient increase at 12 months of age, which indicates that the interpretation of the RNAScope stain for Tgfb1 was not unduly influenced by autofluorescence.

Author response image 1.

(4) Ideally, more care is needed with the language used to describe microglial state during aging. The terms "dystrophic," "dysfunctional," and "inflammatory" all carry their own implications and assumptions. Many changes exhibited by microglia during aging can initially be adaptive or protective, particularly during middle age. Without additional experiments to show that specific microglial attributes during aging are actively detrimental to the tissue and additional experiments to show that microglia have ceased to be capable of engaging in many of their normal actions to support tissue homeostasis, the authors should exercise caution in using terms like dysfunctional.

We appreciate the reviewers’ suggestion. To allay the concerns of the reviewer about the multiple implications of terms such as “dysfunctional” and “inflammatory”, we have tried to replace them throughout the text with more specific terms.

Reviewer #2:

That said, given what we recently learned about microglia isolation for RNA-seq analysis, there is a danger that some of the observations are a result of not age, but cell stress from sample preparation (enzymatic digestion 10min at 37C; e.g. PMID: 35260865). Changes in cell state distribution along aging were made based on scRNA-seq and were not corroborated by any other method, such as imaging of cluster-specific marker expression in microglia at different ages. This analysis would allow confirming the scRNA-seq data and would also give us an idea of where the subsets are present within the hippocampus, and whether there is any interesting distribution of cell states (e.g. some are present closer to stem cells?). Since TGFb is thought to be crucial to microglia biology, it would be valuable to include more analysis of the mice with microglia-specific Tgfb deletion e.g. what was the efficiency of recombination in microglia? Did their numbers change after induction of Tgfb deletion in Cx3cr1-creERT2::Tgfb-flox mice.

We thank the reviewer for their comment regarding potential ex vivo transcriptional alterations with the approaches used in our study. We performed our aging microglia scRNA-Seq characterization prior to the release of Marsh et al (Nature Neuroscience; PMID: 35260865), which revealed the potential transcriptional artefacts induced by isolation. That being said, we took great care to minimize the amount of time samples were subjected to enzymatic digestion (15 minutes) and kept cells at 4C during the remainder of the isolation. Furthermore, we performed all isolations simultaneously, so that transcriptional changes induced by the isolation would be present across all ages and should not be observed during our analysis unless indicative of a true age-related change. Additionally, we have corroborated changes in cell state distribution across ages using several markers (Tgfb1 and KLF2 for the intermediate stress state, S6 for the translation state, and NFKB and CD68 for activation states). In the revised manuscript, we have added additional hippocampal subregion analysis of several IHC immunostains to provide spatial insights into the microglia aging process (Figure S2). This analysis reveals unique spatial dynamics of microglia aging. For example, as the reviewer foresaw, we found that the granule cell layer (the location of adult hippocampal neurogenesis) had a more pronounced age-associated progression of microglial activation than several other regions. A subset of regions had minimal levels of activation during aging, such as the molecular layer and the stratum radiatum of the CA1 (inner CA1in the manuscript) – regions enriched in synaptic terminals. Furthermore, this analysis highlights the susceptibility of microglia aging to microenvironmental influences.

Regarding the temporally controlled microglia-specific genetic KO mouse model used in our original submission, the Cx3cr1-CreER allele selected (B6.129P2(Cg)-Cx3cr1tm2.1(cre/ERT2)Litt/WganJ) has been reported to have very high recombination efficiency (~94% in Parkhurst et al (Cell; PMID: 24360280)), and we used a tamoxifen induction protocol very similar to Faust et al. (Cell Reports; PMID: 37635351) that achieved ~98% recombination (they injected 100mg/kg for 5 days, while we injected 90mg/kg for 5 days). We analyzed our scRNA-Seq data for the expression of Tgfb1 and found that the knockout mice had a 67% reduction in cells expressing higher levels of Tgfb1 (see panel A in Author response image 2). This is likely a large underestimate of the recombination efficiency, as exon 3 is floxed and residual nonfunctional transcripts could be present, given nonsense-mediated decay is not realized in a number of knockout lines (Lindner et al, Methods, PMID: 33838271). We likely achieved a much higher excision efficiency. We would like to highlight that our data indicating increased microglia activation after tamoxifen treatment (Figure S5A) and the involvement of autonomous signaling (Figure S4E-G) are consistent with recently published work by Bedolla et al, (Nature Communications; PMID: 38906887). Additionally, as part of the revision process, we have now corroborated our behavioral data using and independent temporally controlled microglia-specific KO mouse model - Tmem119-CreER::Tgfb1 knockout mice (Figure 4I-K). We performed qPCR on sorted microglia to determine RNA levels in wildtype and knockout mice. Relative levels of Tgfb1 and exon 3 of Tgfb1 (the floxed exon) on technical replicates of 3 pooled samples indicated overall loss of Tgfb1 expression, as well as undetectable levels of exon 3 as normalized to Actb (see panel B in Author response image 2).

Author response image 2.

With respect to the effects of aging and Tgfb1 on microglia density, we find a slight region-specific increase in microglia density with age (see Author response image 3). The density of Iba1 cells across hippocampal regions was analyzed at 3 and 24 months of age (see panel A in Author response image 3) and along an aging continuum at 3, 6, 12, 18, and 24 months (see panel B in Author response image 3). These data are also included in the revised manuscript (Figure S2D-F).

Author response image 3.

Deletion of Tgfb1 also had region-specific effects on microglia. While there was no difference in microglia density between wildtype and heterozygous microglia, there was a significant increase in microglia density in the hilus and molecular layers in knockout mice (see Author response image 4) and included in the revised manuscript (Figure S5A). These data indicate that there are subtle region-specific increases in microglia density with age, as well as following the deletion of Tgfb1 from microglia of mature mice.

Author response image 4.

Additional Recommendations:

(1) The problem of possible digestion artifacts in scRNA-seq should be at least addressed in the discussion as a caveat in data interpretation. Staining for unique cluster markers in undigested tissue would solve the problem. It can be done with microscopy or using flow cytometry, but for this microglia, isolation should be done with no enzymes or with Actinomycin (PMID: 35260865).

The ex vivo activation signature uncovered by Marsh et al. (Nature Neuroscience; PMID: 35260865) arises from the digestion methods used to isolate microglia. We took the utmost care in processing our microglia identically within experiments, which should minimize the amount of uneven ex vivo activation of microglia. This is borne out by the structures of our single-cell sequencing data. Unlike Marsh et al_. where they observe unique cluster after addition of their inhibitors, we do not see any clusters unique to a single condition, suggesting that any influence of _ex vivo activation was evenly distributed.

Importantly, as suggested by the review, we have we have complemented our scRNA-Seq analysis by corroborating several markers for various stages of microglia aging progression using RNAScope and IHC in intact tissue. Specifically, the transient age-dependent increase in Tgfb1 high microglia was confirmed using RNAScope (Figure 3B), the age-related increase in ribosomal high microglia was confirmed using S6 immunostaining (Figure 3I), and the increase of various markers of age-associated activation (C1q, CD68 and NFkB) was confirmed using immunostaining (Figure 1F and Figure S2D-I). Additionally, we have also performed immunostainings for KLF2 and confirmed peak microglia expression at 18 months of age with lower levels at 24 months of age (Figure 2H).

(2) The figures of GO and violin plots are not easy to follow sometimes... what are the data points in the violin plots, maybe worth showing them as points? For the GO, e.g. in 3D, 3J, including a short description of the figure could help, e.g. in Figure 1. it was clear.

We chose not to include the datapoints in the violin plots for aesthetic purposes. Each violin plot would have had hundreds of points that would have made the plots very busy and hidden the structure of the distribution. In Author response image 5 we show the violin plot in Figure 2M with (panel A) and without (panel B) individual points. In a small format, the points overlap and become jumbled together. Therefore, we chose to present the violin plots without points for clarity on the data structure. As for the gene ontology plots in Figure 3, we have updated the descriptions in both the text and figure legends to provide clarification on what they represent.

Author response image 5.

(3) I'm very curious to see the mechanism of action of "aged" microglia in the TGFb-depletion model. Is it creating hostile conditions for stem cells, or we have increased synapse loss? Something else?

We thank the reviewer for their insightful questions. We would like to note that during the revision process of our manuscript, a complementary study was published reporting that the loss of microglia-derived Tgfb1 leads to an aberrant increase in the density of dendritic spines in the CA1 region of the hippocampus (Bedolla et al, Nature Communications, PMID: 38906887). The data from Bedolla et al, shows sparsely labeled neurons in the CA1 with a mGreenLantern expressing virus in mice the had Tgfb1 deleted from microglia using the Cx3cr1-CreERT driver (Figure 7U,V). Additionally, McNamara et al (Nature; PMID: 36517604) demonstrated that microglia-derived Tgfb1 signaling regulates myelin integrity during development and several studies have revealed links between Tgfb1 signaling and altered neurogenesis (e.g., He et al, Nature, PMID: 24859199 and Dias et al, Neuron, PMID: 25467979). Together, this growing body of work indicates that microglia-derived TGFB1 regulates myelination, neurogenesis and synaptic plasticity, which have all been shown to play a role in cognition.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

Specific comments to improve the quality of the work:

(1) The choice of subunits to tag are really not ideal. In the available structures of the human proteasome, The C-terminus of Rpn3/PSMD3 points directly toward the ATPase pore and is likely to disrupt the structure and/or dynamics of the proteasome during proteolysis (see comments regarding controls for functionality below). Similarly, the C-terminal tail of Rpt1/PSMC2 has a key role in the opening of the 20S core particle gate for substrate translocation and processing (see 2018 Nature Communications, 9:1360 and 2018 Cell Reports 24:1301-1315), and Alpha3/PSMA4 can be substituted by a second copy of Alpha4/PSMA7 in some conditions (although tagging Alpha3/PSMA4 would admittedly provide a picture of the canonical proteasome interactome while actively excluding the interactome of the non-canonical proteasomes that form via replacement of Alpha3/PSMA4). Comparison of these cell lines with lines harboring tags on subunits that are commonly used for tagging in the field because of a lack of impacts, such as the N-terminus of Rpn1/PSMD2, the C-terminus of Rpn11/PSMD14, and the C-terminus of Beta4/PSMB2 would help instill confidence that the interactome reported largely arises from mature, functional proteasomes rather than subcomplexes, defective proteasomes, or other species that may occur due to tagging at these positions.

We thank the reviewer for pointing this out. The original purpose of our strategy was to establish proximity labeling of proteasomes to enable applications both in cell culture and in vivo. The choice of PSMA4 and PSMC2 was dictated by previous successful tagging with GFP in mammalian cells (Salomons et al., Exp Cell Res 2010)(Bingol and Schuman, Nature 2006). However, the choice of C-terminal PSMC2 might have been not optimal. HEK293 cells overexpressing PSMC2-BirA show slower growth and the BioID data retrieve higher enrichment of assembly factors suggesting slower assembly of this fusion protein in proteasome. Although we did not observe a negative impact on overall proteasome activity and PSMC2-BirA was (at least in part) incorporated into fully assembled proteasomes as indicated by enrichment of 20S proteins.We apologize for not making it clear that we labeled the N-terminus of PSMD3/Rpn3 and not the C-terminus (Figure 1a and S1a). Therefore, we included in Figure S1a of the revised manuscript structures of the proteasome where the tagged subunit termini are highlighted: C-terminus for PSMA4 and PSMC2 and N-terminus for PSMD3. Additionally, we would like to point out that, differently from PSMC2-BirA, cells expressing BirA-PSMD3 did not show slower growth, and BioID data showed a more homogenous enrichment of both 19S and 20S proteins, as compared to PSMC2-BirA (Figure 1D and 1E). However, the overall level of enrichment of proteasome subunits was not comparable to PSMA4-BirA and, therefore, we opted for focusing the rest of the manuscript on this construct.

In support of this point, the data provided in Figure 1E in which the change in the abundances of each proteasome subunit in the tagged line vs. the BirA control line demonstrates substantial enrichment of the subcomplexes of the proteasome that are tagged in each case; this effect may represent the known feedback-mediated upregulation of new proteasome subunit synthesis that occurs when proteasomal proteolysis is impaired, or alternatively, the accumulation of subcomplexes containing the tagged subunit that cannot readily incorporate into mature proteasomes. Acknowledging this limitation in the text would be valuable to readers who are less familiar with the proteasome.

We would like to clarify that the data shown in Figure 1E do not represent whole proteome data, but rather log2 fold changes vs. BirA* control calculated on streptavidin enrichment samples. The differences in the enrichment of the various subcomplexes between cell lines derives from the fact that the effect size of the enrichment depends on both protein abundance in the isolated complexes, but also on the efficiency of biotinylation. The latter will be higher for proteins located in closer proximity to the bait. A similar observation was pointed out in a recent publication (PMID:36410438) that compared BioID and Co-IP for the same bait. When a component of the nuclear pore complex (Nup158) was analyzed by BioID only the more proximal proteins were enriched as compared to the whole complex in Co-IP data (Author response image 1):

Author response image 1.

Proteins identified in the NUP158 BioID or pulldown experiments are filled in red or light red for significance intervals A or B, respectively. The bait protein NUP158 is filled in yellow. Proteins enriched in the pulldown falling outside the SigA/B cutoff are filled in gray. NPC, nuclear pore complex. SigA, significant class A; SigB, significant class B. Reproduced from Figure 6 of PMID: 36410438.

However, we would like to point out that despite quantitative differences between different proteasome subunits, both 19S and 20S proteins were found to be strongly enriched (typically >2 fold) in all the constructs compared to BirA* control line (Figure 1E). This indicates that at least a fraction of all the tagged subunits are incorporated into fully assembled proteasomes.

Regarding the upregulation of proteasome subunits as a consequence of proteasome dysfunction, we did not find evidence of this, at least in the case of PSMA4. The immunoblot shown in Figure 2A and its quantification in S3A indicate no increased abundance of endogenous PSMA4 upon tetracycline induction of PSMA4-BirA*.

(2) The use of myc as a substrate of the proteasome for demonstration that proteolysis is unaffected is perhaps not ideal. Myc is known to be degraded via both ubiquitin-dependent and ubiquitin-independent mechanisms, such that disruption of one means of degradation (e.g., ubiquitin-dependent degradation) via a given tag could potentially be compensated by another. A good example of this is that the C-terminal tagging of PSMC2/Rpt1 is likely to disrupt interaction between the core particle and the regulatory particle (as suggested in Fig. 1D); this may free up the core particle for ubiquitin-independent degradation of myc.

Aside from using specific reporters for ubiquitin-dependent vs. independent degradation or a larger panel of known substrates, analysis of the abundance of K48-ubiquitinated proteins in the control vs. tag lines would provide additional evidence as to whether or not proteolysis is generally perturbed in the tag lines.

We thank the reviewer for this suggestion. We have included an immunoblot analysis showing that the levels of K48 ubiquitylation (Figure S3d) are not affected by the expression of tagged PSMA4.

(3) On pg. 8 near the bottom, the authors accidentally refer to ARMC6 as ARMC1 in one instance.

We have corrected the mistake.

(4) On pg. 10, the authors explain that they analyzed the interactome for all major mouse organs except the brain; although they explain in the discussion section why the brain was excluded, including this explanation on pg. 10 here instead of in the discussion might be a better place to discuss this.

We moved the explanation from the discussion to the results part.

Reviewer #2 (Recommendations For The Authors):

(1) Perhaps the authors can quantify the fraction of unassembled PSMA4-BirA* from the SEC experiment (Fig. 2b) to give the readers a feeling for how large a problem this could be.

The percentages based on Area Under the Curve calculations have been added to Figure S3b.

(2) Do the authors observe any difference in the enrichment scores between proteins that are known to interact with the proteasome vs proteins that the authors can justify as "interactors of interactors" vs the completely new potential interactors? This could be an interesting way to show that the potential new interactors are not simply because of poor false positive rate calibration, but that they behave in the same way as the other populations.

We thank the reviewer for this suggestion. We analyzed the enrichment scores for 20S proteasome subunits, known PIPs, first neighbors and the remaining enriched proteins. The remaining proteins (potential new interactors) have very similar scores as the first neighbors of known interactors. This plot has been added to Figure S3g.

(3) Did the authors try to train a logistic model for the miniTurbo experiments, like it was done for the BirA* experiments? Perhaps combining the results of both experiments would yield higher confidence on the proteasome interactors.

Following the reviewers suggestion, we applied the classifier on the dataset of the comparison between miniTurbo and PSMA-miniTurbo. We found a clear separation between the FPR and the TPR with 136 protein groups enriched in PSMA-miniTurbo. We have added the classifier and corresponding ROC curve to Figure S4f and S4g.

75 protein groups were found to be enriched for both PSMA4-BirA* and PSMA4-miniTurbo (Author response image 2), including the proteasome core particles, regulatory particles, known interactors and potential new interactors. As we focused more on the identification of substrates with PSMA4-miniTurbo, we did not pursue these overlapping protein groups further, but rather used the comparison to the mouse model to identify potential new interactors.

Author response image 2.

Overlap between ProteasomeID enriched proteins (fpr<0.05) between PSMA4-BirA* and PSMA4-miniTurbo.

(4) Perhaps this is already known, but did the authors check if MG132 affect proteasome assembly? The authors could for example repeat their SEC experiments in the presence of MG132.

We thank the reviewer for the suggestion, however to our knowledge there are no reports that MG132 has an effect on the assembly of the proteasome. MG132 is one of the most used proteasome inhibitors in basic research and as such has been extensively characterized in the last 3 decades. The small peptide aldehyde acts as a substrate analogue and binds directly to the active site of the protease PSMB5/β5. We therefore think it is unlikely that MG132 is interfering with the assembly of the proteasome.

(5) Minor comment: at the bottom of page 8, the authors probably mean ARMC6 and not ARMC1.

We have corrected the mistake.

(6) It would be interesting to expand the analysis of the already acquired in vivo data to try to identify tissue-specific proteasome interactors. Can the authors draw a four-way Venn diagram with the interactors of each tissue?

We thank the reviewer for this suggestion. We have generated an UpSet plot showing the overlap of ProteasomeID enriched proteins in the four tissues that gave us meaningful results (Author response image 3). In order to investigate whether the observed differences in ProteasomeID enriched proteins could be meaningful in terms of proteasome biology, we have highlighted proteins belonging to the UPS that show tissue specific enrichments. We found proteasome activators such as PSME1/PA28alpha and PSME2/PA28beta to enrich preferentially in kidney and liver, respectively, as well as multiple deubiquitinases to enrich preferentially in the heart. These differences might be related to the specific cellular composition of the different tissues, e.g., number of immune cells present, or the tissue-specific interaction of proteasomes with enzymes involved in the ubiquitin cycle. Given the rather preliminary nature of these findings, we have opted for not including this figure in the main manuscript, but rather include it only in this rebuttal letter.

Author response image 3.

Upset plot showing overlap between ProteasomeID enriched proteins in different mouse organs.

Reviewer #3 (Recommendations For The Authors):

(1) In the first paragraph of the Introduction, the authors link cellular senescence caused by partial proteasome inhibition with the efficacy of proteasome inhibitors in cancer therapy. Although this is an interesting hypothesis, I am not aware of any direct evidence for this; rather, I believe the efficacy of bortezomib/carfilzomib in haematological malignancies is most commonly attributed to these cells having adapted to high levels of proteotoxic stress (e.g., chronic unfolded protein response activation). I would suggest rephrasing this sentence.

We thank the reviewer for the comment and have amended the introduction.

(2) For the initial validation experiments (e.g., Fig. 1B), have the authors checked what level of Streptavidin signal is obtained with "+ bio, - tet" ? Although I accept that the induction of PSMA4-BirA* upon doxycycline addition is clear from the anti-Flag blots, it would still be informative to ascertain what level of background labelling is obtained without induction (but in the presence of exogenous biotin).

We tested four different conditions +/- tet and +/- biotin (24h) in PSMA4-BirA* cell lines (Author response image 4). As expected, biotinylation was most pronounced when tet and biotin were added. When biotin was omitted, streptavidin signal was the lowest regardless of the addition of tet. Compared to the -biotin conditions, a slight increase of streptavidin signal could be observed when biotin was added but tet was not added. This could be either due to the promoter leaking (PMID: 12869186) or traces of tetracycline in the FBS we used, as we did not specifically use tet-free FBS for our experiments.

Author response image 4.

Streptavidin-HRP immunoblot following induction of BirA fusion proteins with tetracycline (+tet) and supplementation of biotin (+bio). For the sample used as expression control tetracycline was omitted (-tet). To test background biotinylation, biotin supplementation was omitted (-bio). Immunoblot against BirA and PSMA was used to verify induction of fusion proteins, while GAPDH was used as loading control.

(3) For the proteasome structure models in Fig. 1D, a scale bar would be useful to inform the reader of the expected 10 nm labelling radius (as the authors have done later, in Fig. 2D).

We have added 10 nm scale bars to Figure 1d.

(4) In the "Identification of proteasome substrates by ProteasomeID" Results subsection, I believe there is a typo where the authors refer to ARMC1 instead of ARMC6.

We have corrected the mistake.

(5) I think Fig. S5 was one of the most compelling in the manuscript. Given the interest in confirming on-target efficacy of targeted degradation modalities, as well as identifying potential off-target effects early-on in development, I would consider promoting this out of the supplement.

We thank the reviewer for the comment and share the excitement about using ProteasomeID for targeted degradation screening. We have moved the data on PROTACs (Figure S5) into a new main Figure 5.

In addition, in relation to the comment of this reviewer regarding the detection of endogenous substrates, we have now included validation for one more hit emerging from our analysis (TIGD5) and included the results in Figure 4f, 4g and S4j.

Author response:

The following is the authors’ response to the original reviews

We thank the reviewers for their careful and positive assessment of our manuscript. Maybe our findings are best summarized in the model below, showing that KDM5 inhibition/loss mediates a viral mimicry and DNA damage response through the generation of R-loops in genomic repeats. This is a different mechanism from the more well studied double-stranded RNA-induced “viral mimicry” response. Our studies also suggest that KDM5 inhibition may have a larger therapeutic window than STING agonists, since KDM5 inhibition seemingly does not induce “viral mimicry” in normal breast epithelial cells. 

Author response image 1.

Model of viral mimicry activation. De-repression of repetitive elements may trigger dsRNA formation, which activates the RIG-1/MDA5 pathway, as well as PKR. Alternatively, derepression of these elements may induce transcription replication conflicts (TRCs), resulting in R-loop formation. R-loops can lead to DNA damage, and/or activate the cGAS/STING pathway. Both the MAVS pathway and the cGAS/STING pathway converge to activate type I interferon (IFN) responses, resulting in decreased cell fitness and/or increased immunogenicity.

We do agree with the assessment that the study would be strengthened by in vivo studies. However, there are 4 different isoforms of KDM5 (3 in females), and existing KDM5specific inhibitors do not have adequate PK/PD properties for in vivo studies. We would also like to note that most mouse studies have not been proven to accurately predict immunotherapy responses in patients. Future studies in ex vivo tumor models would strengthen the clinical relevance of these studies. In the interim, we have added some normal macrophage studies in Figure S5 and an example of studies in normal T-cells below. Such studies will also be important to ensure that future KDM5 inhibitors do not have adverse effects on the immune system. Here, we observe that KDM5 inhibition appears to have neutral or slightly reduced T cell viability with KDM5 inhibition (Author response image 2a). However, KDM5 inhibition also results in increased CD107a expression in T-cells, indicative of a more cytotoxic phenotype (Author response image 2b). These studies suggest that KDM5 inhibitors do not have significant adverse effects on T cells or macrophages (figure S5) in the normal immune environment.

Author response image 2.

KDM5 inhibition does not have significant adverse effects on T-cells. a) Fold change proliferation of T-cells from 2 different human donors (left and right panels on graph) activated with 0.25ug/ml CD3 and treated with the indicated concentrations of C48 or a positive control (CBLB) compared to vehicle controls. b. FACS plots and histograms of CD107a surface expression (x-axis) versus forward scatter (FSC, y-axis) of T-cells from 2 different humans donors activated with 0.25ug/ml or 0.5mug/ml CD3 and treated with the indicated concentrations of C48.

Specific comments and answers to Reviewer #1:

We have added some additional analysis of data from other breast cancer cell lines to strengthen our points (Figure S2f, Figure S3e, Figure S4g-h, k.) We have also uploaded all the data to Geo with the following accession numbers :

GSE296387: H3K4me3 CUT-and-Tag data

GSE296584: S9.6 CUT-and-Tag data

GSE296974: RNA-sequencing data

Responses to Reviewer #1 (Recommendations for the authors):

(1) We have not conducted genomic studies comparing KDM5 expression to retroelement activation status in the tumor data sets but recognize that this is important for future studies. Again, there are several KDM5 isoforms and looking at repeat expression in these larger data sets is complex. We have added some data correlating KDM5 expression with ISG signatures in Figure S3j-l as well as in the graph below (Author response image 3). The correlation with ISG and AP signatures is modest, but strongest for KDM5B and C in breast cancer data sets, consistent with our disruption data for these 2 isoforms. As mentioned above, we do agree that future studies of KDM5s along with a broader analysis of other epigenetic modifying enzymes over repeats in various cancer types will shed light on the role of histone modifying enzymes in suppressing “viral mimicry” in tumors.

Author response image 3.

Correlation between gene expression and IFN gene set GSVA scores in breast cancer cell lines. a) Pearson correlation score between gene expression and IFN signature (ISG) gene set variation analysis (GSVA) scores in breast cancer cell lines as reported in DepMap. Higher ranks indicate an inverse correlation between expression of the individual gene and the expression of the ISG gene set. Correlation ranks for KDM5A, B and C are highlighted. b) as in a), but comparing gene expression to antigen presentation (AP) GSVA scores.

(2) We apologize for the mislabeling in figure 2B – has been corrected in the revised version.

(3) We agree that blocking the cGAS/STING pathway, only partially rescues the ISREGFP and HLA-A, B, C phenotype in HCC1428 cells. We have added data (Figure S2f) showing that this rescue is stronger in MCF7 cells. It is possible that the MDA5/MAVS pathway may also contribute to activation of the Type I interferon response. However, we have data that MAVS plays a minor (if any) role in this context, as MAVS KO minimally decreases C48-induced ISRE-GFP activity and HLA-A, B, C surface expression in HCC1428 cells (added Figure S2g).

Furthermore, there is no significant increase in dsRNA observed (using J2 antibody as a readout in immunofluorescence experiments) with C48 treatment as compared to 5’-azacytidine treatment or ADAR K/O (data not included). However, we have not performed MAVS/PKR K/O experiments to completely rule out the involvement of the dsRNA sensing pathways.

(4) These experiments were performed in the operetta imaging system, rather than confocal imaging, and therefore we do not have such images. Quantification of RNaseH1-GFP in the whole cell is reported in the figure, as RNaseH1-GFP signal is increased in both the nucleus and the cytoplasm with C48 treatment. This is not unexpected, as our data suggest that R-loop formation occurs in repetitive regions of the genome that are de-repressed by KDM5 inhibition in the nucleus, and the RNA/DNA hybrids, generated from R-loops, may activate cGAS/STING pathway in the cytoplasm.

(5) Disruption of siXPF and siXPG is relatively toxic in itself. Complete knockouts in breast cancer cells were not viable and we partially knocked down XPF using siRNA instead. We do agree that these kinds of rescue studies need to be expanded upon in future studies, but they served as further proof of the conclusions presented here.

(6) We have provided all the data in Geo and alternative representations can be made.

(7) Unfortunately, CUT-and-Tag experiments were not performed in cells expressing siXPF and therefore we cannot provide this data. However, XPF has been previously shown to be responsible for excising R-loops from the genome, rendering them detectable by cGAS/STING in the cytoplasm (Crossley et al, 2022, referenced in the current MS). Therefore, while we demonstrate that XPF knockdown attenuates type I IFN pathway activation upon KDM5 inhibition, it may not necessarily reduce R-loop formation in retroelements; it may just prevent their excision and downstream cGAS/STING activation. We do agree that CUT-and-Tag experiments in cells treated with siXPF versus siControl will have to be performed in the future to test this hypothesis.

Responses to Reviewer #2 (Recommendations for the authors):

(1) We have modified the text as well as the figure legend to state that this is a simplistic representation of the pathway in normal cells. As stated in the introduction, these pathways can be modified in tumors. The data presented suggest that the dsRNA pathway can be activated in all breast cancer cell lines tested, whereas more variation is observed in the activation of the STING pathway.  

(2) The ADAR guides target ADAR 110 and p150 but not ADAR2. This has been clarified in the text.  

(3) The guides have been renamed in the figure as the reviewer suggests.  

(4) It has been shown by others that KDM5 can occupy the STING promoter (https://pubmed.ncbi.nlm.nih.gov/30080846/); which supports the reviewer’s suggestion that STING upregulation in HMECs may be due to increased H3K4me3 at the STING gene. However, we argue that STING upregulation is not sufficient to activate “viral mimicry” due to the absence of “tumor-specific R-loops” (due to an increase in TRC in tumor cells) in normal cells. It is interesting to note that the S9.6 signal in subtelomeric regions is increased in HMECS similar to what is observed in tumor cells. However, the S9.6 signal over other repeats is not (Author response image 4), suggesting that C48-induced increases over non-telomeric repeats are tumor specific. This suggests that the tumor-specific increases in R-loop formation, which lead to “viral mimicry” activation, are not driven by those formed in subtelomeric regions. Future studies will have to expand on these findings.

Author response image 4.

Percent of S9.6 reads that align to repetitive genome in HMEC cells. (a) % of total aligned S9.6 reads that map to subtelomeric region in HMEC cells treated with DMSO or 2.5 μM C48. (b) % of total aligned S9.6 reads that map to repetitive elements in general in HMEC cells treated as in a).

(5) Clarity on R-loop quantification has been added to the figure legend as well as in the Materials and Methods section. Mean fluorescence intensity in the whole cell (this includes both nuclear and cytoplasmic signals) was quantified together and normalized to the number of DAPI-stained nuclei per well. As mentioned above all quantified in the Operetta imaging system.

(6) We have added some data that shows that increases in H3K4me3 is observed in and around ISGs upon KDM5 inhibition (Figure S4f). However, without time course experiments it is difficult to assess whether these are direct effects of the KDM5 inhibitor or indirect effects from activation of Type I IFN (similarly to what has previously been reported with 5’-azacytidine induction of “viral mimicry”, https://pubmed.ncbi.nlm.nih.gov/26317465/).

(7) We have previously included data showing that S9.6 reads in repeats that do not display C48-mediated increases in H3K4me3 also do not increase with C48 treatment (this is now Figure S4o). In addition, we have added some data showing that repeats with increased H3K4me3 and repeats with increased transcription upon C48 treatment also have increased S9.6 reads. Repeats that display both increases in H3K4me3 and mRNA expression have even greater increases in S9.6 signal compared to repeats that have increases in either one (Figure S4m-n). Taken together, this data suggest that KDM5 inhibition increases H3K4me3 in repeats, thereby allowing for their transcription, which can increase the probability of Transcription replication conflicts (TRC) and R-loop formation at such loci.

(8) As mentioned earlier in this response, while we observe increased S9.6 reads in subtelomeric regions of HCC1428 cells upon KDM5 inhibition, we also observe this in normal HMEC cells. Since KDM5 inhibition does not induce viral mimicry in HMEC cells, this suggests that R-loops formed in subtelomeric regions do not dictate the response observed with C48 treatment in breast cancer cells.

We hope that these answers to the reviewers comments as well as the additional data provided strengthens our findings.

Author Response

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

First, the authors would like to thank the reviewers and editors for their thoughtful comments. The comments were used to guide our revision, which is substantially improved over our initial submission. We have addressed all comments in our responses below, through a combination of clarification, new analyses and new experimental data.

Reviewer #1 (Public Review):

In this manuscript, the authors identified and characterized the five C-terminus repeats and a 14aa acidic tail of the mouse Dux protein. They found that repeat 3&5, but not other repeats, contribute to transcriptional activation when combined with the 14aa tail. Importantly, they were able to narrow done to a 6 aa region that can distinguish "active" repeats from "inactive" repeats. Using proximal labeling proteomics, the authors identified candidate proteins that are implicated in Dux-mediated gene activation. They were able to showcase that the C-terminal repeat 3 binds to some proteins, including Smarcc1, a component of SWI/SNF (BAF) complex. In addition, by overexpressing different Dux variants, the authors characterized how repeats in different combinations, with or without the 14aa tail, contribute to Dux binding, H3K9ac, chromatin accessibility, and transcription. In general, the data is of high quality and convincing. The identification of the functionally important two C-terminal repeats and the 6 aa tail is enlightening. The work shined light on the mechanism of DUX function.

A few major comments that the authors may want to address to further improve the work:

We thank the reviewer for their efforts and constructive comments, which have guided our revisions.

1) The summary table for the Dux domain construct characteristics in Fig. 6a could be more accurate. For example, C3+14 clearly showed moderate weaker Dux binding and H3K9ac enrichment in Fig 3c and 3e. However, this is not illustrated in Fig. 6a. The authors may consider applying statistical tests to more precisely determine how the different Dux constructs contribute to DNA binding (Fig. 3c), H3K9ac enrichment (Fig. 3e), Smarcc1 binding (Fig. 5e), and ATAC-seq signal (Fig. 5f).

We thank the reviewer for this comment, and agree that there were some modest differences in construct characteristics that were not captured in the Summary Table (6a). To better reflect the differences between constructs, we added additional dynamic range to our depiction/scoring, and believe that the new scoring system provides sufficient qualitative range to capture the difference without imposing a statistical approach.

2) Another concern is that exogenous overexpressed Dux was used throughout the experiments. The authors may consider validating some of the protein-protein interactions using spontaneous or induced 2CLCs (where Dux is expressed).

We agree that it would be helpful to determine endogenous DUX interaction with our BioID candidates. Here, we attempted co-IPs for endogenous DUX protein with the DUX antibody and were unsuccessful, which indicated that the DUX antibody is useful for detection but not efficient in the primary IP. This is why we utilized the mCherry tag for DUX IP experiments, which worked exceptionally well.

3) It could be technically challenging, but the authors may consider to validate Dux and Smarcc1 interaction in a biologically more relevant context such as mouse 2-cell embryos where both proteins are expressed. Whether Smarcc1 binding will be dramatically reduced at 4-cell embryos due to loss of Dux expression?

While we agree that it would be interesting to validate the in vivo interaction of DUX and SMARCC1 in the early embryo, it is not technically feasible for us to conduct the experiment, as the IP would require thousands of two-cell embryos, and we have the issue of poor co-IP quality with the DUX antibody.

Reviewer #2 (Public Review):

In this manuscript, Smith et al. delineated novel mechanistic insights into the structure-function relationships of the C-terminal repeat domains within the mouse DUX protein. Specifically, they identified and characterised the transcriptionally active repeat domains, and narrowed down to a critical 6aa region that is required for interacting with key transcription and chromatin regulators. The authors further showed how the DUX active repeats collaborate with the C-terminal acidic tail to facilitate chromatin opening and transcriptional activation at DUX genomic targets.

Although this study attempts to provide mechanistic insights into how DUX4 works, the authors will need to perform a number of additional experiments and controls to bolster their claims, as well as provide detailed analyses and clarifications.

We thank this reviewer for their constructive comments, and have conducted several new analyses, additional experiments and clarifications – which have strengthened the manuscript in several locations. Highlights include a statistical approach to the similarity of mouse repeats to themselves and to orthologs (Figure S1d) and clarified interpretations, a wider dynamic range to better reflect changes in DUX construct behaviors (Figure 6a), and additional data on construct behavior, including ‘inactive’ constructs (e.g C1+14aa in Figure 1a,d, new ATAC-seq in Figure S1g), and active constructs such as C3+C5+14aa and C3+C514aa (in Figure S1b).

Reviewer #3 (Public Review):

Dux (or DUX4 in human) is a master transcription factor regulating early embryonic gene activation and has garnered much attention also for its involvement in reprogramming pluripotent embryonic stem cells to totipotent "2C-like" cells. The presented work starts with the recognition that DUX contains five conserved c. 100-amino acid carboxy-terminal repeats (called C1-C5) in the murine protein but not in that of other mammals (e.g. human DUX4). Using state-of-the-art techniques and cell models (BioID, Cut&Tag; rescue experiments and functional reporter assays in ESCs), the authors dissect the activity of each repeat, concluding that repeats C3 and C5 possess the strongest transactivation potential in synergy with a short C-terminal 14 AA acidic motif. In agreement with these findings, the authors find that full-length and active (C3) repeat containing Dux leads to increased chromatin accessibility and active histone mark (H3K9Ac) signals at genomic Dux binding sites. A further significant conclusion of this mutational analysis is the proposal that the weakly activating repeats C2 and C4 may function as attenuators of C3+C5-driven activity.

By next pulling down and identifying proteins bound to Dux (or its repeat-deleted derivatives) using BioID-LC/MS/MS, the authors find a significant number of interactors, notably chromatin remodellers (SMARCC1), a histone chaperone (CHAF1A/p150) and transcription factors previously (ZSCAN4D) implicated in embryonic gene activation.

The experiments are of high quality, with appropriate controls, thus providing a rich compendium of Dux interactors for future study. Indeed, a number of these (SMARCC1, SMCHD1, ZSCAN4) make biological sense, both for embryonic genome activation and for FSHD (SMCHD1).

A critical question raised by this study, however, concerns the function of the Dux repeats, apparently unique to mice. While it is possible, as the authors propose, that the weak activating C1, C2 C4 repeats may exert an attenuating function on activation (and thus may have been selected for under an "adaptationist" paradigm), it is also possible that they are simply the result of Jacobian evolutionary bricolage (tinkering) that happens to work in mice. The finding that Dux itself is not essential, in fact appears to be redundant (or cooperates with) the OBOX4 factor, in addition to the absence of these repeats in the DUX protein of all other mammals (as pointed out by the authors), might indeed argue for the second, perhaps less attractive possibility.

In summary, while the present work provides a valuable resource for future study of Dux and its interactors, it fails, however, to tell a compelling story that could link the obtained data together.

We appreciated the reviewer’s views regarding the high quality of the work and our generation of an important dataset of DUX interactors. We also appreciate the comments provided to improve the work, and have performed and included in the revised version a set of clarifications, additional analyses and additional experiments that have served to reinforce our main points and provide additional mechanistic links. We also agree that more remains to be done to understand the function and evolution of repeats C1, C2 and C4.

Reviewer #1 (Recommendations For The Authors):

1) For immuno-blots, authors may indicate the expected bands to help readers better understand the results.

Agreed, and we have included the predicted molecular weight of proteins in the Figure Legends. We note that our work shows that the C-terminal domains confer anomalous migration in SDS-PAGE.

2) Fig. 5b, a blot missing for the mCherry group?

Figure 5b is a volcano blot, so we believe the reviewer is referring to Figure 5d, which is a coimmunoprecipitation experiment between SMARCC1 and mCherry-tagged DUX constructs. However, we are unsure of the comment as an anti mCherry sample is present in that panel.

3) Line 99-100, Fig. S1d, it seems that repeat2, but not repeat3, is more similar to human DUX4 C-terminal region.

This comment and one by another reviewer have prompted us to re-examine the similarities of the DUX repeats, and we have new analyses (Figure S1d) and an alternative framing in the manuscript as a result. We have expanded on this in our response to Reviewer #2, point #1 – and direct the reviewer there for our expanded treatment.

4) There are a few references are misplaced. For example, line 48, the studies that reported the role of Dux in inducing 2CLCs should be from Hendrickson et al., 2017, De Iaco et al., 2017, and Whiddon et al., 2017. The authors may want to double check all references.

Thanks for pointing these out. These issues have been corrected in the manuscript.

5) In the materials & methods section, a few potential errors are noticed. For example, concentrations of PD0325901 and CHIR99021 in mESC medium appear ~1000-fold higher than standards.

Thanks – corrected.

Reviewer #2 (Recommendations For The Authors):

Major Points

1) Line 99 - The authors claimed that the "human DUX4 C-terminal region is most similar to the 3rd repeat of mouse DUX", but based on Supp. Fig. 1d, the human DUX4 C-term should be most similar to the 2nd repeat of mouse DUX. If this is indeed the case, it will undermine the rest of this study, since the authors claim that the 3rd repeat is transcriptionally active, whereas the 2nd repeat is transcriptionally inactive, and the bulk of this study largely focused on how the active repeats, not the inactive repeats, are critical in recruiting key transcriptional and chromatin regulators to induce the embryonic gene expression program.

We thank the reviewer for their comments here. Since submission,and as mentioned above for reviewer #1 we have revisited the issue of similarity of the DUX4 C-terminal region to the mouse C-terminal repeats, with a BLAST-based approach that is more rigorous and informed by statistics – which is in Author response table 1 and now in the manuscript as Figure S1d, and has affected our interpretation. Our prior work involved a simple % identity comparison table and we now appreciate that some of the similarity analyses did not meet statistical significance, and therefore we are unable to draw certain conclusions. We make the appropriate modifications in the text. For example, we no longer state that the DUX4 C-terminus appears to be most similar to mouse repeats 3 and 5. This does not affect the main conclusions of the paper regarding interactions of the C-terminus with chromatin-related proteins, only our speculation on which repeat might have represented the original single repeat in the mouse – an issue we think of some interest, but did not rise to the level of mentioning in the original or current abstract.

Author response table 1.

Parameters: PAM250 matrix. Gap costs of existence: 15 and extension: 3. Numbers represent e-value of each pairwise comparison

*No significant similarities found (>0.05).

2) In Supp Fig 1d, it seems that the rat DUX4 C-terminal region is most similar to the 4th repeat of mouse DUX, which according to the author is supposedly transcriptionally inactive. This weakens the authors justification that the 3rd or 5th repeat is likely the "parental repeat for the other four", and further echoes my concern in point 1 where the human DUX4 C-term is most similar to the 2nd (inactive) repeat of mouse DUX.

The reviewer’s point is well taken and is addressed in point #1 above.

3) In Fig. 1d, the authors showed that DUX4-containing C3 and C5, but lacking acidic tail, can promote MERVL::GFP expression, albeit to a slightly lower extent compared to FL. However, in Fig. 2b, C3 or C5 alone (lacking acidic tail) completely failed to promote MERVL::GFP expression. However, in the presence of the acidic tail, both versions were able to promote MERVL::GFP expression, similar to that of FL. The latter would suggest that it is the acidic tail that is crucial for MERVL::GFP expression, and this does not quite agree with Fig 1b, where C12345 (lacking acidic tail) was able to promote MERVL::GFP expression. Although C12345 did not activate MERVL to a similar level as FL, it is clearly proficient, compared to C3 or C5 alone (lacking acidic tail) where there is no increase in MERVL at all. Additional constructs will be helpful to clarify these points. For example, 'C3+C5 minus acidic tail' and 'HD1+HD2+acidic tail only' constructs.

We agree that constructs such as those mentioned would add to the work. First, we have done the additional construct HD1+HD2+14aa tail, which is presented as ΔC12345+14aa in Figure 2a and in S2a. Additionally, we performed experiments on the requested C3+C5+14aa and C3+C5Δ14aa (see samples 6 and 7 in Author response image 1, which are now included in Supplemental Figure 2b). The results reinforce our hypothesis of an additive effect toward DUX target gene activation by increasing C-terminal repeats and including the 14aa tail.

Author response image 1.

4) Related to the above, the flow cytometry data for the MERVL::GFP reporter as presented in Figures 1 and 2, as well as in Supp. Fig. 2, show a considerably large difference in the %GFP|mCherry for the FL construct, ranging from ~6-26%. This makes it difficult to convince the reader which of the different DUX domain constructs cannot or can partially induce GFP|mCherry signal when compared to FL, and hence it is tough to definitively ascertain the exact contribution of each of the 5 C-terminal repeats with high confidence, as it appears that there exists a significant amount of variability in this MERVL::GFP reporter system. The authors need to address this issue since this is their primary method to elucidate the transcriptional activity of each of the mouse DUX repeat domains.

We note that with the Dux-/- cell lines we used throughout the timeline of the study, the percent of %GFP|mCherry expression progressively and slowly decreased – possibly due to slow/modest epigenetic silencing of the reporter. However, we always used the full-length DUX construct to establish the dynamic range. We emphasize that the relative differences between constructs over multiple cell line replicates remained relatively consistent. However, we elected to show absolute values in each experiment, rather than simply normalizing the full-length to 100% and showing relative.

5) Lines 140-142 - The authors claimed that the functional difference between the transcriptionally active and inactive repeats could be narrowed down to a "6aa region which is conserved between repeats C3 and C5, but not conserved in C1, C2 and C4". Assuming the 6aa sequence is DPLELF, why does C1C3a elicit almost twice the intensity of GFP|mCherry signal compared to C3C1c, despite both constructs having the exact same 6aa sequence?

Indeed, C1C3a and C3C1c both containing the ‘active’ DPL sequence but having different relative levels of %GFP|mCherry. This is consistent with these sequences having a positive role in DUX target gene regulation – but likely in combination with other other regions which potentiate its affect, possibly through interacting proteins or post-translational modifications.

Why does DPLEPL (the intermediate C3C1b construct) induce a similar extent of GFP|mCherry signal as the FL construct, even though the former includes 3aa from a transcriptionally inactive repeat? In contrast, GSLELF (the other intermediate C1C3b construct) that also includes 3aa from a transcriptionally inactive repeat is almost completely deficient in inducing any GFP|mCherry signal. Why is that so? Is DPL the most crucial sequence? It will be important to mutate these 3 (or the above 6) residues on FL DUX4 to examine if its transcriptional activity is abolished.

These are interesting points. DPL does appear to be the most important region in the mouse DUX repeats. However, DPL is not shared in the C-terminus of human DUX4. Notably, the DUX4 C-terminus is sufficient to activate the mouse MERVL::GFP reporter when cloned to mouse homeodomains (see Author response image 2, second sample) and other DUX target genes (initially published in Whiddon et al. 2017). One clear possibility is that the DPL region is helping to coordinate the additive effects of multiple DUX repeats, which only exist in the mouse protein.

Author response image 2.

6) Line 154 - The intermediate DUX domain construct C1C3b occupied a different position on the PCA plot from the C1C3c construct that does not contain any of the critical 6aa sequence, as shown in Fig. 2e. However, both these constructs appear to be similarly deficient in inducing any GFP|mCherry signal, as seen in Fig. 2c. Why is that so?

The PCA plot assesses the impact on the whole transcriptome and not just the MERVL::GFP reporter, suggesting the 3aa region has transcriptional effects on the genome beyond what is detected in the MERVL::GFP reporter.

7) To strengthen the claim that "Chromatin alterations at DUX bindings sites require a transcriptionally active DUX repeat", the authors should also perform CUT&Tag for constructs containing transcriptionally inactive DUX repeats (e.g. C1+14aa), and show that such constructs fail to occupy DUX binding sites, as well as are deficient in H3K9ac accumulation.

This is a good comment. We elected to control this with constructs containing or lacking an active repeat. Although we have not pursued this by CUT&TAG, we have examined the impact of DUX constructs with inactive repeats (including the requested C1+14aa, new Figure S1g) by ATAC-seq (see #12, ATAC-seq section, below), and observe no chromatin opening, suggesting that the lack of transcriptional activity is rooted in the inability to open chromatin.

8) It would be good if the authors could also include CUT&Tag data for some of the C1C3 chimeric constructs that were used in Fig. 2, since the authors argued that the minimal 6aa region is sufficient to activate many of the DUX target genes. This would also strengthen the authors’ case that the transcriptionally active, not inactive, repeats are critical for binding at DUX binding sites and ensuring H3K9ac occupancy.

We agree that these would be helpful, and have examined the inactive repeats in transcription and ATAC-seq formats during revision (new data in Figures 1d and S1g), but not yet the CUT&TAG format.

9) Line 213 - "SMARCA4" should have been "SMARCA5"? Based on Fig. 4d, SMARCA5 is picked up in the BirA*-DUX interactome, not SMARCA4.

Thanks – corrected.

10) Lines 250-252 - The authors compared the active BirA-C3 against the inactive BirA-C1 to elucidate the interactome of the transcriptionally active C3 repeat, as illustrated in Fig. 5c. They found 12 proteins more enriched in C1 and 154 proteins in C3. This information should be presented clearly as a separate tab in Supp Table 2. What are the proteins common to both constructs, i.e. enriched to a similar extent? Do they include chromatin remodellers too? Although the authors sought to identify differential interactors between the 2 constructs, it is also meaningful to perform 2 separate comparisons - active BirA-C3 against BirA alone control, and inactive BirA-C1 against BirA alone control - like in Fig. 4d, so as to more accurately define whether the active C3 repeat, and not the inactive C1 repeat, interacts with proteins involved in chromatin remodeling.

We thank the reviewer for this comment, and we have modified the manuscript by adding a second sheet in Supplementary Table 2 including the results for enriched proteins in BirA-C1 vs. C3. Additionally, due to limitations of annotation between BirA alone and BirA*-C3 being sequenced in different mass spectrometry experiments, it is difficult to quantitatively compare the two datasets with pairwise comparisons.

11) Fig 5d: The authors mentioned in the legend that endogenous IP was performed for SMARCC1. However, in line 266, they stated Flag-tagged SMARCC1. Is SMARCC1 overexpressed? The reciprocal IP should also be presented. More importantly, C1 constructs (e.g. C1+14aa and C1Δ14aa) should also be included.

To clarify, Figure 4e used exogenously overexpressed FLAG-SMARCC1 in HEK-293T cells to confirm the results of the full-length DUX BioID experiment. Figure 5d was performed with overexpressed DUX construct, but involved endogenous SMARCC1 in mESCs. This has now been made clearer in the revised manuscript.

12) For both the SMARCC1 CUT&Tag and ATAC-seq experiments shown in Figures 5e and 5f respectively, the authors need to include DUX derivatives that contain transcriptionally inactive repeats with and without the 14aa acidic tail, i.e. C1+14aa and C1Δ14aa, and show that these constructs prevent the binding/recruitment of SMARCC1 to DUX genomic targets, and correspondingly display a decrease in chromatin accessibility. Only then can they assert the requirement of the transcriptionally active repeat domains for proper DUX protein interaction, occupancy and target activation.

We agree that examination of an inactive repeat in certain approaches would improve the manuscript. Importantly, we have now included C1+14 in our ATAC-seq experiments, and in Author response image 3 two individual replicates, which constitute a new Figure S1g. Compared to the transcriptionally active DUX constructs, which see opening at DUX binding sites, we do not see chromatin opening at DUX binding sites with transcriptionally inactive C1+14.

Author response image 3.

13) To prove that DUX-interactors are important for embryonic gene expression, it will be important to perform loss of function studies. For instance, will the knockdown/knockout of SMARCC1 in cells expressing the active DUX repeat(s) lead to a loss of DUX target gene occupancy and activation?

We agree that it would be interesting to better understand SMARCC1 cooperation with DUX function in the embryo, but we believe this is beyond the scope of this paper.

Minor Points

1) Lines 124-126 - What is the reason/rationale for why the authors used one linker (GGGGS2) for constructs with a single internal deletion, but 2 different linkers (GGGGS2 and GAGAS2) for constructs with 2 internal deletions?

With Gibson cloning, there are homology overhang arms for each PCR amplicon that are required to be specific for each overlap. Additionally, each PCR amplicon needs to be specific enough from one another so that all inserts (up to 5 in this manuscript) are included and oriented in the right order. The linker sequences were included in the homology arm overlaps, so the nucleotide sequences for each linker needed to be specific enough to include all inserts. This is a general rule to Gibson cloning. Additionally, both GGGGS2 and GAGAS2 are common linker sequences used in molecular biology and the amino acids structures are similar to one another, suggesting there is no functional difference between linkers.

2) Line 704 - 705: In the figure legend, the authors stated that 'Constructs with a single black line have the linker GGGGS2 and constructs with two black lines have linkers with GGGGS2 and GAGAS2, respectively.'. This was not obvious in the figures.

Constructs used for flow and genomics experiments that are depicted in Figure 2, Supplementary Figure 2, Figure 3, Figure 4, and Figure 5 have depicted black lines where deletions are present. Where these deletions are present, there are linkers in order to preserve spacing and mobility for the protein.

3) Line 160 - Clusters #1 and #2 are likely written in the wrong order. It should have been "activating the majority of DUX targets in cluster #2, not cluster #1" and "failed to activate those in cluster #1, not cluster #2", based on the RNA-seq heatmap in Fig. 2f.

We thank the reviewer for this comment, and the error has been corrected in the manuscript.

4) Line 188 - Delete the word "of" in the following sentence fragment: "DUX binding sites correlating with the of transcriptional".

Thanks – corrected.

5) Line 191 - Delete the word "aids" in the following sentence fragment: "important for conferring H3K9ac aids at bound".

Thanks – corrected.

6) Line 711 - "C1-C3 a,b,d" should be "C1-C3 a,b,c".

Thanks – corrected.

7) Lines 711-712 - The colors "pink to blue" and "blue to pink" are likely written in the wrong order. Based on Fig. 2c, the blue to pink bar graphs should represent C1-C3 a,b,c in that order, and likewise the pink to blue bar graphs should represent C3-C1 a,b,c in that order.

Thanks – corrected.

8) There is an overload of data presented in Fig. 2c, such that it is difficult to follow which part of the figure represents each data segment as written in the figure legend. It is recommended that the data presented here is split into 2 sub-figures.

Figure 2c has a supporting figure in Supplementary Figure 2b. While there is both a graphical depiction of the constructions and the data both in the main panel of Figure 2C, we have depicted it as so to be as clear as possible for the reader to interpret the complexity and presentence of amino acids in each of the constructs.

9) Line 717 - "following" is misspelt.

Thanks – corrected.

10) Lines 720-721 - "(Top)" and "(Bottom)" should be replaced with "(Left)" and "(Right)", as the 2 bar graphs presented in Fig. 2d are placed side by side to each other, not on the top and bottom.

Thanks – corrected.

11) Lines 725 and 839 - "Principle" is misspelt. It should be "Principal".

Thanks – corrected.

12) In Figures 3d and 3e, the sample labeled "C3+14_1" should be re-labeled to "C3+14", in accordance with the other sub-figures. Additionally, for the sake of consistency, "aa" should be appended to the relevant constructs, e.g. "C3+14aa" and "C3Δ14aa".

Thanks – corrected.

13) Line 773 - Were the DUX domain constructs over-expressed for 12hr (as written in the figure legend) or 18hr (as labeled in Fig. 5d)?

Thanks – corrected.

14) Related to minor point 19 above, is there a reason/rationale for why some of the experiments used 12hr over-expression of DUX domain constructs (e.g. for CUT&TAG in Fig. 3), whereas in other experiments 18hr over-expression was chosen instead (e.g. flow cytometry for MERVL::GFP reporter in Figures 1 and 2, and co-IP validations of BirA*-DUX interactions in Fig. 4)?

Thanks for the opportunity to explain. In this work, experiments that reported on proteins that are translated following DUX gene activation (e.g. MERVL:GFP via flow) were done at 18hr to allow for enough time for transcription and translation of GFP (or other DUX target genes). For experiments that report on the impact of DUX on chromatin and transcription, such as RNA-seq, CUT&Tag, and ATAC-seq, we induced DUX domain constructs for 12 hours.

15) Line 804 - "ΔHDs" is missing between "C2345+14aa" and "ΔHD1".

Thanks – corrected.

16) In Fig. 5c, "Chromatin remodelers" is misspelt.

Thanks – corrected.

17) There is no reference in the manuscript to the proposed model that is presented in Fig. 6b.

Thanks – corrected.

Reviewer #3 (Recommendations For The Authors):

Given the uncertainty of the function of the Dux peptide repeats in mice, could it not also be possible that the underlying repeated nature of the (coding) DNA? That is, could these DNA repeats exert a regulatory function on Dux transcription itself (also given the dire consequences of misregulated DUX4 expression as seen in FSHD, for example).

Yes, it remains possible that the internal coding repeats within Dux are playing a role in locus regulation, and might be interesting to examine. However, we consider this question as being outside the scope of the current paper.

Finally, it would be interesting to know whether these repeats are, in fact, present in all mouse species. Already no longer present in rat, do they exist, or not, in more "distant" mice, e.g. M. caroli?

Determining whether all mouse strains contain C-terminal repeats in DUX is a question we also considered. However, Dux and its orthologs are present in long and very complex repeat arrays that are not present in the sequencing data or annotation in other mouse strains. Therefore, we are not unable to answer this question from existing sequencing data. Answering would require a considerable genome sequencing and bioinformatics effort, or alternatively a considerable effort aimed at cloning ortholog cDNAs from 2-cell embryos.

Minor points:

line 169: here it seems, in fact, that the 'inactive' C2, C4 repeats are more similar to each other (my calculation: 91 and 96% identity at the protein and DNA level, respectively) than the active C3 and C5 repeats (82 and 89% identity, resp.), the outlier being C1.

Thanks for this comment, which was mentioned by other reviewers as well and has been addressed through new statistical analyses and interpretation (see new Figure S1d).

line 191: I'm not sure this sentence parses correctly ("...14AA tail is important for conferring H3K9Ac aids at bound sites...")

We thank the reviewer for this comment, and we have corrected the sentence in the manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study focuses on characterizing a previously identified gene, encoding the secreted protein Ppe1, that may play a role in rice infection by the blast fungus Magnaporthe oryzae. Magnaporthe oryzae is a hemibiotrophic fungus that infects living host cells before causing disease. Infection begins with the development of a specialized infection cell, the appressorium, on the host leaf surface. The appressorium generates enormous internal turgor that acts on a thin penetration peg at the appressorial base, forcing it through the leaf cuticle. Once through this barrier, the peg elaborates into bulbous invasive hyphae that colonizes the first infected cell before moving to neighboring cells via plasmodesmata. During this initial biotrophic growth stage, invasive hyphae invaginate the host plasma membrane, which surrounds growing hyphae as the extra-invasive hyphae membrane (EIHM). To avoid detection, the fungus secretes apoplastic effectors into the EIHM matrix via the conventional ER-Golgi secretion pathway. The fungus also forms a plant-derived structure called the biotrophic interfacial complex (BIC) that receives cytoplasmic effectors through an unconventional secretion route before they are delivered into the host cell. Together, these secreted effector proteins act to evade or suppress host innate immune responses. Here the authors contribute to our understanding of M. oryzae infection biology by showing how Ppe1, which localizes to both the appressorial penetration peg and to the appressorial-like transpressoria associated with invasive hyphal movements into adjacent cells, maximizes host cell penetration and disease development and is thus a novel contributor to rice blast disease.

We sincerely appreciate the reviewer’s thoughtful evaluation of our work. We are grateful for your recognition of Ppe1 as a novel contributor to M. oryzae infection biology and your insightful summary of its spatio-temporal localization and functional importance in host penetration. We also appreciate devoting your time to provide us with constructive feedback, which greatly strengthens our manuscript.

Strengths:

A major goal of M. oryzae research is to understand how the fungus causes disease, either by determining the physiological underpinnings of the fungal infection cycle or by identifying effectors and their host targets. Such new knowledge may point the way to novel mitigation strategies. Here, the authors make an interesting discovery that bridges both fungal physiology and effector biology research by showing how a secreted protein Ppe1, initially considered an effector with potential host targets, associates with its own penetration peg (and transpressoria) to facilitate host invasion. In a previous study, the authors had identified a small family of small secreted proteins that may function as effectors. Here they suggest Ppe1 (and, later in the manuscript, Ppe2/3/5) localizes outside the penetration peg when appressoria develops on surfaces that permit penetration, but not on artificial hard surfaces that prevent peg penetration. Deleting the PPE1 gene reduced (although did not abolish) penetration, and a fraction of those that penetrated developed invasive hyphae that were reduced in growth compared to WT. Using fluorescent markers, the authors show that Ppe1 forms a ring underneath appressoria, likely where the peg emerges, which remained after invasive hyphae had developed. The ring structure is smaller than the width of the appressorium and also lies within the septin ring known to form during peg development. This so-called penetration ring also formed at the transpressorial penetration point as invasive hyphae moved to adjacent cells. This structure is novel, and required for optimum penetration during infection. Furthermore, Ppe1, which carries a functional signal peptide, may form on the periphery of the peg, together suggesting it is secreted and associated with the peg to facilitate penetration. Staining with aniline blue also suggests Ppe1 is outside the peg. Together, the strength of the work lies in identifying a novel appressorial penetration ring structure required for full virulence.

We are deeply grateful to the reviewer for the clear understanding and insightful evaluation of our work. Your recognition of the novel contribution and scientific merit of our study is both encouraging and motivating. We sincerely appreciate the time, expertise and constructive feedback dedicated to reviewing our manuscript, as the comments have been instrumental in enhancing the quality of this work.

Weaknesses:

The main weakness of the paper is that, although Ppe1 is associated with the peg and optimizes penetration, the function of Ppe1 is not known. The work starts off considering Ppe1 a secreted effector, then a facilitator of penetration by associating with the peg, but what role it plays here is only often speculated about. For example, the authors consider at various times that it may have a structural role, a signaling role orchestrating invasive hyphae development, or a tethering role between the peg and the invaginated host plasma membrane (called throughout the host cytoplasmic membrane, a novel term that is not explained). However, more effort should be expended to determine which of these alternative roles is the most likely. Otherwise, as it stands, the paper describes an interesting phenomenon (the appressorial ring) but provides no understanding of its function.

We sincerely appreciate the reviewer’s comments. We have revised "host cytoplasmic membrane" to "host plasma membrane" throughout the manuscript for consistency. To further investigate the role of the Ppe1 in the interaction between M. oryzae and rice, we overexpressed PPE1 in rice ZH11. A pCXUN-SP-GFP-Ppe1 vector containing a signal peptide and an N-terminal GFP tag was constructed (pCXUN-SP-GFP-Ppe1), and 35 GFP-PPE1-OX plants (T0) were subsequently obtained through Agrobacterium-mediated rice transformation. Subsequently, PCR and qRT-PCR validation were performed on the T0 transgenic plants. The PCR results showed that the inserted plasmid could be amplified from the genomic DNA extracted from the leaves of all the resulting T0 plants (Author response image 1A). qRT-PCR results indicated that most T0 transgenic plants could transcriptionally express PPE1 (Author response image 1B). T0 plants with higher expression levels were selected for western blot analysis, which confirmed the presence of GFP-Ppe1 bands of the expected size (Author response image 1C). To further explore the targets of Ppe1 in rice, the leaf sheaths of T0 plants were inoculated with M. oryzae strain Guy11. Total proteins were extracted at 24 hours post-inoculation (hpi) and subjected to immunoprecipitation using GFP magnetic beads. Silver staining revealed more interacting protein bands in T0 plants compared to ZH11 and GFP-OX controls (Author response image 1D). These samples were then analyzed by mass spectrometry in which 331 rice proteins that potentially interact with Ppe1 were identified (Author response image 1E). Subsequently, yeast two-hybrid assays were performed on 13 putative interacting proteins with higher coverage, but no interaction was detected between Ppe1 and these proteins (Author response image 1F-G). Considering that the identification and functional validation of interacting proteins is a labor-intensive and time-consuming endeavor, we will focus our future efforts on in-depth studies of Ppe1's function in rice.

Author response image 1.

Screening of Ppe1 candidate targets in rice. (A) The determination of GFP-PPE1 construct in transgenic rice. (B) The expression of PPE1 transgenic rice (T0) was verified by qRT-PCR. (C) Western blot analysis of Ppe1 expression in transgenic rice. (D) Rapid silver staining for detection of the purified proteins captured by the GFP-beads. (E) Venn diagram comparing the number of proteins captured in the different samples. (F) Identity of the potential targets of Ppe1 in rice. (G) Yeast two-hybrid assay showing negative interaction of Ppe1 with rice candidate proteins.

The inability to nail down the function of Ppe1 likely stems from two underlying assumptions with weak support. Firstly, the authors assume that Ppe1 is secreted and associated with the peg to form a penetration ring between the plant cell wall and cytoplasm membrane. However, the authors do not demonstrate it is secreted (for instance by blocking Ppe1 secretion and its association with the peg using brefeldin A).

To investigate the secretion pathway of Ppe1 in M. oryzae, we determined the inhibitory effects of Brefeldin A (BFA) on conventional ER-to-Golgi secretion in fungi as suggested by the reviewer. We inoculated rice leaf sheaths with conidia suspensions from the Ppe1-mCherry and PBV591 strains (containing a Pwl2-mCherry-NLS and Bas4-GFP co-expressing constructs) and treated them with BFA. We found that, even after exposure to BFA for 5 to 11 hours, the Ppe1-mCherry still formed its characteristic ring conformation (Author response image 2). Similarly, in the BFA-treated samples, the cytoplasmic effector Pwl2-mCherry accumulated at the BIC, while the apoplastic effector Bas4-GFP was retained in the invasive hyphae (Author response image 2). These results indicate that Ppe1 is not secreted through the conventional ER-Golgi secretion pathway.

Author response image 2.

The secretion of Ppe1 is not affected by BFA treatment. (A) and (B) The Ppe1-mCherry fluorescent signal was still observed both in the presence and absence of BFA. (C) Following BFA treatment, the secretion of the apoplastic effector Bas4-GFP was blocked while that of the cytoplasmic effector Pwl2-mCherry was not affected. The rice leaf sheath tissue was inoculated with 50 μg/mL BFA (0.1% DMSO) at 17 hpi. Images were captured at 22 hpi for A and 28 hpi for B and C. Scale bars = 10 µm.

Also, they do not sufficiently show that Ppe1 localizes on the periphery of the peg. This is because confocal microscopy is not powerful enough to see the peg. The association they are seeing (for example in Figure 4) shows localization to the bottom of the appressorium and around the primary hyphae, but the peg cannot be seen. Here, the authors will need to use SEM, perhaps in conjunction with gold labeling of Ppe1, to show it is associating with the peg and, indeed, is external to the peg (rather than internal, as a structural role in peg rigidity might predict). It would also be interesting to repeat the microscopy in Figure 4C but at much earlier time points, just as the peg is penetrating but before invasive hyphae have developed - Where is Ppe1 then? Finally, the authors speculate, but do not show, that Ppe1 anchors penetration pegs on the plant cytoplasm membrane. Doing so may require FM4-64 staining, as used in Figure 2 of Kankanala et al, 2007 (DOI: 10.1105/tpc.106.046300), to show connections between Ppe1 and host membranes. Note that the authors also do not show that the penetration ring is a platform for effector delivery, as speculated in the Discussion.

We sincerely appreciate the reviewer's valuable suggestion regarding SEM with immunogold labeling to precisely visualize Ppe1's association with penetration peg. While we fully acknowledge this would be an excellent approach, after consulting several experts in the field, we realized that the specialized equipment and technical expertise required for fungal immunogold-SEM are currently unavailable to us. We sincerely hope that the reviewer will understand this technical limitation.

To further strengthen our evidence for the role of Ppe1's in anchoring penetration peg to the plant plasma membrane, we provided new co-localization images of Ppe1 and penetration peg (Fig. S7). At 16 hours post-inoculation (hpi), when the penetration peg was just forming and prior to the development of invasive hyphae, the Ppe1-mCherry fluorescence forms a tight ring-like structure closely associated with the base of the appressorium. As at 23 hpi, the circular Ppe1-mCherry signal was still detectable beneath the appressorium, and around the penetration peg which differentiated into the primary invasive hyphae. Furthermore, we obtained 3D images of the strain expressing both Ppe1-mCherry and Lifeact-GFP during primary invasive hyphal development. The results revealed that Ppe1 forms a ring-like structure that remains anchored to the penetration peg during fungal invasion (Fig. S6).

We also conducted FM4-64 staining experiment as recommended by the reviewer. Although the experiment provided valuable insights, we found that the resolution was insufficient to precisely delineate the spatial relationship between Ppe1 and host membranes at the penetration peg (Author response image 3). To optimize this colocalization, we tested the localization between Ppe1-mCherry ring and rice plasma membrane marker GFP-OsPIP2 (Fig. S8). These new results provide compelling complementary evidence supporting our conclusion that Ppe1 functions extracellularly at the host-pathogen interface. We hope these additional data will help address the reviewer's concerns regarding Ppe1's localization.

Author response image 3.

FM4-64-stained rice leaf sheath inoculated with M. oryzae strain expressing Ppe1-GFP. Ppe1-GFP ring was positioned above the primary invasive hyphae. Scale bar = 5 µm.

Secondly, the authors assume Ppe1 is required for host infection due to its association with the peg. However, its role in infection is minor. The majority of appressoria produced by the mutant strain penetrate host cells and elaborate invasive hyphae, and lesion sizes are only marginally reduced compared to WT (in fact, the lesion density of the 70-15 WT strain itself seems reduced compared to what would be expected from this strain). The authors did not analyze the lesions for spores to confirm that the mutant strains were non-pathogenic (non-pathogenic mutants sometimes form small pinprick-like lesions that do not sporulate). Thus, the pathogenicity phenotype of the knockout mutant is weak, which could contribute to the inability to accurately define the molecular and cellular function of Ppe1.

We appreciate the reviewer’s comments. To ensure the reliability of our findings, we conducted spray inoculation experiments with multiple independent repeats. Our results consistently demonstrated that deletion of the PPE1 gene significantly attenuates the virulence of M. oryzae. Further analysis of lesion development and sporulation in the Δ_ppe1_ mutant revealed that it retains the ability to produce conidia. To validate these observations, we generated a PPE1 knockout in the wild-type reference strain Guy11. Similarly, we observed a significant decrease in the pathogenicity of the Δ_ppe1_ mutants generated from the wild-type Guy11 strain compared to Guy11 in the spray assay (Fig S2). These results collectively indicate the importance of Ppe1 in the pathogenicity of M. oryzae to rice.

In summary, it is important that the role of Ppe1 in infection be determined.

Reviewer #2 (Public review):

The article focuses on the study of Magnaporthe oryzae, the fungal pathogen responsible for rice blast disease, which poses a significant threat to global food security. The research delves into the infection mechanisms of the pathogen, particularly the role of penetration pegs and the formation of a penetration ring in the invasion process. The study highlights the persistent localization of Ppe1 and its homologs to the penetration ring, suggesting its function as a structural feature that facilitates the transition of penetration pegs into invasive hyphae. The article provides a thorough examination of the infection process of M. oryzae, from the attachment of conidia to the development of appressoria and the formation of invasive hyphae. The discovery of the penetration ring as a structural element that aids in the invasion process is a significant contribution to the understanding of plant-pathogen interactions. The experimental methods are well-documented, allowing for reproducibility and validation of the results.

We sincerely appreciate the thoughtful and insightful evaluation of our work. Thank you for recognizing the significance of our findings regarding the penetration ring and the functional role of Ppe1 during host invasion.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Line 48: "after appressorium- or transpressorium-mediated penetration of plant cell wall" - transpressoria do not penetrate the plant cell wall.

Thank you for your valuable suggestion. For improved clarity, we have rephrased the sentence as follows: In this study, we showed that a penetration ring is formed by penetration pegs after appressorium-mediated penetration of plant cell wall.

Line 143: "approximately 25% of the 143 appressoria formed by the Δppe1 mutant had no penetration peg" - It is not possible to see the penetration peg by confocal microscopy.

Thank you for your valuable suggestion. We have revised the sentence as follows: In contrast, approximately 25% of the appressoria formed by the Δ_ppe1_ mutant had no penetration.

Line 159: "inner cycle" -should be inner circle?

We gratefully acknowledge the reviewer's careful reading. The typographical error has been corrected throughout the revised manuscript.

Line 255: "These results indicate that initiation of penetration peg formation is necessary for the formation of the penetration ring." Actually, more precisely, they indicate that penetration is necessary.

We appreciate this suggestion and have revised the text to be more concise: These results indicate that penetration is necessary for the formation of the penetration ring.

Line 282: "unlike subcellular localizations of other effectors"- is this an effector if no plant targets are known?

We appreciate this suggestion and have revised the text as follows: unlike subcellular localizations of Bas4, Slp1, Pwl2, and AvrPiz-t.

Line 299: "it may function as a novel physical structure for anchoring penetration pegs on the surface of plant cytoplasm membrane after cell wall penetration" - an interaction with the plant plasma membrane was not shown and this is speculative.

We have provided new evidence to show the spatial positioning of Ppe1-mCherry ring with the rice plasma membrane (see figure S8)

Line 301: "It is also possible that this penetration ring functions as a collar or landmark that is associated with the differentiation of penetration pegs (on the surface of cytoplasm membrane) into primary invasive hyphae enveloped in the EIHM cytoplasm membrane (Figure 7)." The alternative conclusions for Ppe1 function, either interacting with host membranes or acting as a developmental landmark, need to be resolved here.

We appreciate this suggestion and have revised the text as follows: It is also possible that this penetration ring functions as a collar that is associated with the differentiation of penetration pegs into primary invasive hyphae enveloped in the EIHM (Figure 7).

Line 317: "is likely a structural feature or component for signaling the transition of penetration pegs to invasive hyphae",- if the authors think Ppe1 has these roles, why do they refer to Ppe1 as an effector?

Many thanks for these comments. We have revised this and refer to Ppe1 as a secreted protein throughout the revised manuscript.

Line 337: "After the penetration of plant cell wall, the penetration ring may not only function as a physical structure but also serve as an initial effector secretion site for the release of specific effectors to overcome plant immunity in early infection stages"- which is it? Also, no evidence is provided to suggest it is a platform for effector secretion.

We sincerely appreciate your valuable suggestion. We have revised this sentence as follows: After the penetration of plant cell wall, the penetration ring may not only function as a physical structure but also serve as a secretion site for the release of specific proteins to overcome plant immunity during the early infection stages.

Reviewer #2 (Recommendations for the authors):

(1) While the study suggests the penetration ring as a structural feature, it remains unclear whether it also serves as a secretion site for effectors. Further exploration of this aspect would strengthen the conclusions.

We thank the reviewer for this useful suggestion. In this study, we demonstrated that Ppe1 proteins form a distinct penetration ring structure at the site where the penetration peg contacts the plant plasma membrane prior to differentiation into primary invasive hyphae (Figs. 2 and 7). Thus, we reasoned that penetration ring may function as a novel physical structure. Notably, additional Ppe family members (Ppe2, Ppe3, and Ppe5) were also found to localize to this penetration ring (Fig. 6B), suggesting that it also serves as a secretion site for releasing proteins. To test whether Ppe1 and Ppe2 label to the same site, we analyzed the colocalization between Ppe1-GFP and Ppe2-mCherry. The results showed that Ppe1-GFP and Ppe2-mCherry are well colocalized (Author response image 4). This study primarily focuses on the discovery and characterization of the penetration ring. The potential role of this structure in effector translocation will be investigated in future studies.

Author response image 4.

Ppe1 co-localizes with Ppe2 at the penetration ring in M. oryzae. Line graphs were generated at the directions pointed by the white arrows. Scale bar = 2μm.

(2) The article could benefit from a discussion on the broader implications of these findings for developing resistant crop varieties or new fungicidal strategies.

We have incorporated this discussion as suggested (lines 358-360).

(3) What is the significance of the formation of the penetration ring in the pathogenicity of the rice blast fungus? Or, how does it assist the fungus in its infection process?

Our findings have several significant implications. First, we believe that the discovery of the penetration ring as a novel physical structure associated with the differentiation of invasive hyphae represents a breakthrough in plant-pathogen interactions that will be of interest to fungal biologists, pathologists and plant biologists. Secondly, our study presents new role of the peg as a specialized platform for secretory protein deployment, in addition to its commonly known role as a physical penetration tool for the pathogen. Thirdly, we identify Ppe1 as a potential molecular target for controlling the devastating rice blast disease, as Ppe homologs are absent in plants and mammals. We have incorporated this discussion in the revised manuscript (lines 354-362).

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

In this study, the authors aim to understand why decision formation during behavioural tasks is distributed across multiple brain areas. They hypothesize that multiple areas are used in order to implement an information bottleneck (IB). Using neural activity recorded from monkey DLPFC and PMd performing a 2-AFC task, they show that DLPFC represents various task variables (decision, color, target configuration), while downstream PMd primarily represents decision information. Since decision information is the only information needed to make a decision, the authors point out that PMd has a minimal sufficient representation (as expected from an IB). They then train 3-area RNNs on the same task and show that activity in the first and third areas resemble the neural representations of DLPFC and PMd, respectively. In order to propose a mechanism, they analyse the RNN and find that area 3 ends up with primarily decision information because feedforward connections between areas primarily propagate decision information.

The paper addresses a deep, normative question, namely why task information is distributed across several areas.

Overall, it reads well and the analysis is well done and mostly correct (see below for some comments). My major problem with the paper is that I do not see that it actually provides an answer to the question posed (why is information distributed across areas?). I find that the core problem is that the information bottleneck method, which is evoked throughout the paper, is simply a generic compression method.

Being a generic compressor, the IB does not make any statements about how a particular compression should be distributed across brain areas - see major points (1) and (2).

If I ignore the reference to the information bottleneck and the question of why pieces of information are distributed, I still see a more mechanistic study that proposes a neural mechanism of how decisions are formed, in the tradition of RNN-modelling of neural activity as in Mante et al 2013. Seen through this more limited sense, the present study succeeds at pointing out a good model-data match, and I could support a publication along those lines. I point out some suggestions for improvement below.

We thank the reviewer for their comments, feedback and suggestions. We are glad to hear you support the good model-data match for this manuscript.  With your helpful comments, we have clarified the connections to the information bottleneck principle and also contrasted it against the information maximization principle (the InfoMax principle), an alternative hypothesis. We elaborate on these issues in response to your points below, particularly major points (1) and (2). We also address all your other comments below.

Major points

(1) It seems to me that the author's use of the IB is based on the reasoning that deep neural networks form decisions by passing task information through a series of transformations/layers/areas and that these deep nets have been shown to implement an IB. Furthermore, these transformations are also loosely motivated by the data processing inequality.

On Major Point 1 and these following subpoints, we first want to make a high-level statement before delving into a detailed response to your points as it relates to the information bottleneck (IB). We hope this high-level statement will provide helpful context for the rest of our point-by-point responses. 

We want to be clear that we draw on the information bottleneck (IB) principle as a general principle to explain why cortical representations differ by brain area. The IB principle, as applied to cortex, is only stating that a minimal sufficient representation to perform the task is formed in cortex, not how it is formed. The alternative hypothesis to the IB is that brain areas do not form minimal sufficient representations. For example, the InfoMax principle states that each brain area stores information about all inputs (even if they’re not necessary to perform the task). InfoMax isn’t unreasonable: it’s possible that storing as much information about the inputs, even in downstream areas, can support flexible computation and InfoMax also supports redundancy in cortical areas. Indeed, many studies claim that action choice related signals are in many cortical areas, which may reflect evidence of an InfoMax principle in action for areas upstream of PMd.

While we observe an IB in deep neural networks and cortex in our perceptual decision-making task, we stress that its emergence across multiple areas is an empirical result. At the same time, multiple areas producing an IB makes intuitive sense: due to the data processing inequality, successive transformations typically decrease the information in a representation (especially when, e.g., in neural networks, every activation passes through the Relu function, which is not bijective). Multiple areas are therefore a sufficient and even ‘natural’ way to implement an IB, but multiple areas are not necessary for an IB. That we observe an IB in deep neural networks and cortex emerge through multi-area computation is empirical, and, contrasting InfoMax, we believe it is an important result of this paper. 

Nevertheless, your incisive comments have helped us to update the manuscript that when we talk about the IB, we should be clear that the alternative hypothesis is non-minimal representations, a prominent example of which is the InfoMax principle. We have now significantly revised our introduction to avoid this confusion. We hope this provides helpful context for our point-by-point replies, below.

However, assuming as a given that deep neural networks implement an IB does not mean that an IB can only be implemented through a deep neural network. In fact, IBs could be performed with a single transformation just as well. More formally, a task associates stimuli (X) with required responses (Y), and the IB principle states that X should be mapped to a representation Z, such that I(X;Z) is minimal and I(Y,Z) is maximal. Importantly, the form of the map Z=f(X) is not constrained by the IB. In other words, the IB does not impose that there needs to be a series of transformations. I therefore do not see how the IB by itself makes any statement about the distribution of information across various brain areas.

We agree with you that an IB can be implemented in a single transformation. We wish to be clear that we do not intend to argue necessity: that multiple areas are the only way to form minimal sufficient representations. Rather, multiple areas are sufficient to induce minimal sufficient representations, and moreover, they are a natural and reasonably simple way to do so. By ‘natural,’ we mean that minimal sufficient representations empirically arise in systems with multiple areas (more than 2), including deep neural networks and the cortex at least for our task and simulations. For example, we did not see minimal sufficient representations in 1- or 2-area RNNs, but we did see them emerge in RNNs with 3 areas or more. One potential reason for this result is that sequential transformations through multiple areas can never increase information about the input; it can only maintain or reduce information due to the data processing inequality.

Our finding that multiple areas facilitate IBs in the brain is therefore an empirical result: like in deep neural networks, we observe the brain has minimal sufficient representations that emerge in output areas (PMd), even as an area upstream (DLPFC) is not minimal. While the IB makes a statement that this minimal sufficient representation emerges, to your point, the fact that it emerges over multiple areas is not a part of the IB – as you have pointed out, the IB doesn’t state where or how the information is discarded, only that it is discarded. Our RNN modeling later proposes one potential mechanism for how it is discarded. We updated the manuscript introduction to make these points:

“An empirical observation from Machine Learning is that deep neural networks tend to form minimal sufficient representations in the last layers. Although multi-layer computation is not necessary for an IB, they provide a sufficient and even “natural” way to form an IB. A representation z = f(x) cannot contain more information than the input x itself due to the data processing inequality[19]. Thus, adding additional layers typically results in representations that contain less information about the input.”

And later in the introduction:

“Consistent with these predictions of the IB principle, we found that DLPFC has information about the color, target configuration, and direction. In contrast, PMd had a minimal sufficient representation of the direction choice. Our recordings therefore identified a cortical IB. However, we emphasize the IB does not tell us where or how the minimal sufficient representation is formed. Instead, only our empirical results implicate DLPFC-PMd in an IB computation. Further, to propose a mechanism for how this IB is formed, we trained a multi-area RNN to perform this task. We found that the RNN faithfully reproduced DLPFC and PMd activity, enabling us to propose a mechanism for how cortex uses multiple areas to compute a minimal sufficient representation.”

In the context of our work, we want to be clear the IB makes these predictions:

Prediction 1: There exists a downstream area of cortex that has a minimal and sufficient representation to perform a task (i.e.,. I(X;Z) is minimal while preserving task information so that I(Z;Y) is approximately equal to  I(X;Y)). We identify PMd as an area with a minimal sufficient representation in our perceptual-decision-making task. 

Prediction 2 (corollary if Prediction 1 is true): There exists an upstream brain area that contains more input information than the minimal sufficient area. We identify DLPFC as an upstream area relative to PMd, which indeed has more input information than downstream PMd in our perceptual decision-making task. 

Note: as you raise in other points, it could have been possible that the IB is implemented early on, e.g., in either the parietal cortex (dorsal stream) or inferotemporal cortex (ventral stream), so that DLPFC and PMd both contained minimal sufficient representations. The fact that it doesn’t is entirely an empirical result from our data. If DLPFC had minimal sufficient representations for the perceptual decision making task, we would have needed to record in other regions to identify brain areas that are consistent with Prediction 2. But, empirically, we found that DLPFC has more input information relative to PMd, and therefore the DLPFC-PMd connection is implicated in the IB process.

What is the alternative hypothesis to the IB? We want to emphasize: it isn’t single-area computation. It’s that the cortex does not form minimal sufficient representations. For example, an alternative hypothesis (“InfoMax”) would be for all engaged brain areas to form representations that retain all input information. One reason this could be beneficial is because each brain area could support a variety of downstream tasks. In this scenario, PMd would not be minimal, invalidating Prediction 1. However, this is not supported by our empirical observations of the representations in PMd, which has a minimal sufficient representation of the task. We updated our introduction to make this clear:

“But cortex may not necessarily implement an IB. The alternative hypothesis to IB is that the cortex does not form minimal sufficient representations. One manifestation of this alternative hypothesis is the “InfoMax” principle, where downstream representations are not minimal but rather contain maximal input information22. This means information about task inputs not required to perform the task are present in downstream output areas. Two potential benefits of an InfoMax principle are (1) to increase redundancy in cortical areas and thereby provide fault tolerance, and (2) for each area to support a wide variety of tasks and thereby improve the ability of brain areas to guide many different behaviors. In contrast to InfoMax, the IB principle makes two testable predictions about cortical representations. Prediction 1: there exists a downstream area of cortex that has a minimal and sufficient representation to perform a task (i.e., I(X; Z) is minimal while preserving task information so that I(Z; Y) ≈ I(X; Y)). Prediction 2 (corollary if Prediction 1 is true): there exists an upstream area of cortex that has more task information than the minimal sufficient area.”

Your review helped us realize we should have been clearer in explaining that these are the key predictions of the IB principle tested in our paper. We also realized we should be much clearer that these predictions aren’t trivial or expected, and there is an alternative hypothesis. We have re-written the introduction of our paper to highlight that the key prediction of the IB is minimal sufficient representations for the task, in contrast to the alternative hypothesis of InfoMax.

A related problem is that the authors really only evoke the IB to explain the representation in PMd: Fig 2 shows that PMd is almost only showing decision information, and thus one can call this a minimal sufficient representation of the decision (although ignoring substantial condition independent activity).

However, there is no IB prediction about what the representation of DLPFC should look like.

Consequently, there is no IB prediction about how information should be distributed across DLPFC and PMd.

We agree: the IB doesn’t tell us how information is distributed, only that there is a transformation that eventually makes PMd minimal. The fact that we find input information in DLPFC reflects that this computation occurs across areas, and is an empirical characterization of this IB in that DLPFC has direction, color and context information while PMd has primarily direction information. To be clear: only our empirical recordings verified that the DLPFC-PMd circuit is involved in the IB. As described above, if not, we would have recorded even further upstream to identify an inter-areal connection implicated in the IB.

We updated the text to clearly state that the IB predicts that an upstream area’s activity should contain more information about the task inputs. We now explicitly describe this in the introduction, copy and pasted again here for convenience.

“In contrast to InfoMax, the IB principle makes two testable predictions about cortical representations. Prediction 1: there exists a downstream area of cortex that has a minimal and sufficient representation to perform a task (i.e., I(X; Z) is minimal while preserving task information so that I(Z; Y) ≈ I(X; Y)). Prediction 2 (corollary if Prediction 1 is true): there exists an upstream area of cortex that has more task information than the minimal sufficient area.

Consistent with the predictions of the IB principle, we found that DLPFC has information about the color, target configuration, and direction. In contrast, PMd had a minimal sufficient representation of the direction choice. Our recordings therefore identified a cortical IB. However, we emphasize the IB does not tell us where or how the minimal sufficient representation is formed. Instead, only our empirical results implicate DLPFC-PMd in an IB computation Further, to propose a mechanism for how this IB is formed, we trained a multi-area RNN to perform this task.”  

The only way we knew DLPFC was not minimal was through our experiments. Please also note that the IB principle does not describe how information could be lost between areas or layers, whereas our RNN simulations show that this may occur through preferential propagation of task-relevant information with respect to the inter-area connections.  

(2) Now the authors could change their argument and state that what is really needed is an IB with the additional assumption that transformations go through a feedforward network. However, even in this case, I am not sure I understand the need for distributing information in this task. In fact, in both the data and the network model, there is a nice linear readout of the decision information in dPFC (data) or area 1 (network model). Accordingly, the decision readout could occur at this stage already, and there is absolutely no need to tag on another area (PMd, area 2+3).

Similarly, I noticed that the authors consider 2,3, and 4-area models, but they do not consider a 1-area model. It is not clear why the 1-area model is not considered. Given that e.g. Mante et al, 2013, manage to fit a 1-area model to a task of similar complexity, I would a priori assume that a 1-area RNN would do just as well in solving this task.

While decision information could indeed be read out in Area 1 in our multi-area model, we were interested in understanding how the network converged to a PMd-like representation (minimal sufficient) for solving this task. Empirically, we only observed a match between our model representations and animal cortical representations during this task when considering multiple areas. Given that we empirically observed that our downstream area had a minimal sufficient representation, our multi-area model allowed how this minimal sufficient representation emerged (through preferential propagation of task-relevant information).

We also analyzed single-area networks in our initial manuscript, though we could have highlighted these analyses more clearly to be sure they were not overlooked. We are clearer in this revision that we did consider a 1-area network (results in our Fig 5). While a single-area RNN can indeed solve this task, the single area model had all task information present in the representation, and did not match the representations in DLPFC or PMd. It would therefore not allow us to understand how the network converged to a PMd-like representation (minimal sufficient) for solving this task. We updated the schematic in Fig 5 to add in the single-area network (which may have caused the confusion).

We have added an additional paragraph commenting on this in the discussion. We also added an additional supplementary figure with the PCs of the single area RNN (Fig S15). We highlight that single area RNNs do not resemble PMd activity because they contain strong color and context information. 

In the discussion:

“We also found it was possible to solve this task with single area RNNs, although they did not resemble PMd (Figure S15) since it did not form a minimal sufficient representation. Rather, for our RNN simulations, we found that the following components were sufficient to induce minimal sufficient representations: (1) RNNs with at least 3 areas, following Dale’s law (independent of the ratio of feedforward to feedback connections).”

I think there are two more general problems with the author's approach. First, transformations or hierarchical representations are usually evoked to get information into the right format in a pure feedforward network. An RNN can be seen as an infinitely deep feedforward network, so even a single RNN has, at least in theory, and in contrast to feedforward layers, the power to do arbitrarily complex transformations. Second, the information coming into the network here (color + target) is a classical xor-task. While this task cannot be solved by a perceptron (=single neuron), it also is not that complex either, at least compared to, e.g., the task of distinguishing cats from dogs based on an incoming image in pixel format.

An RNN can be viewed as an infinitely deep feedforward network in time. However, we wish to clarify two things. First, our task runs for a fixed amount of time, and therefore this RNN in practice is not infinitely deep in time. Second, if it were to perform an IB operation in time, we would expect to see color discriminability decrease as a function of time. Indeed, we considered this as a mechanism (recurrent attenuation, Figure 4a), but as we show in Supplementary Figure S9, we do not observe it to be the case that discriminability decreases through time. This is equivalent to a dynamical mechanism that removes color through successive transformations in time, which our analyses reject (Fig 4). We therefore rule out that an IB is implemented through time via an RNN’s recurrent computation (viewed as feedforward in time). Rather, as we show, the IB comes primarily through inter-areal connections between RNN areas. We clarified that our dynamical hypothesis is equivalent to rejecting the feedforward-in-time filtering hypothesis in the Results: 

“We first tested the hypothesis that the RNN IB is implemented primarily by recurrent dynamics (left side of Fig. 4a). These recurrent dynamics can be equivalently interpreted as the RNN implementing a feedforward neural network in time.”  

The reviewer is correct that the task is a classical XOR task and not as complex as e.g., computer vision classification. That said, our related work has looked at IBs for computer vision tasks and found them in deep feedforward networks (Kleinman et al., ICLR 2021). Even though the task is relatively straightforward, we believe it is appropriate for our conclusions because it does not have a trivial minimal sufficient representation: a minimal sufficient representation for XOR must contain only target, but not color or target configuration information. This can only be solved via a nonlinear computation. In this manner, we favor this task because it is relatively simple, and the minimal sufficient representations are interpretable, while at the same time not being so trivially simple (the minimal sufficient representations require nonlinearity to compute).  

Finally, we want to note that this decision-making task is a logical and straightforward way to add complexity to classical animal decision-making tasks, where stimulus evidence and the behavioral report are frequently correlated. In tasks such as these, it may be challenging to untangle stimulus and behavioral variables, making it impossible to determine if an area like premotor cortex represents only behavior rather than stimulus. However, our task decorrelates both the stimulus and the behaviors. 

(3) I am convinced of the author's argument that the RNN reproduces key features of the neural data. However, there are some points where the analysis should be improved.

(a) It seems that dPCA was applied without regularization. Since dPCA can overfit the data, proper regularization is important, so that one can judge, e.g., whether the components of Fig.2g,h are significant, or whether the differences between DLPFC and PMd are significant.

We note that the dPCA codebase optimizes the regularization hyperparameter through cross-validation and requires single-trial firing rates for all neurons, i.e., data matrices of the form (n_Neurons x Color x Choice x Time x n_Trials), which are unavailable for our data. We recognized that you are fundamentally asking whether differences are significant or not. We therefore believe it is possible to address this through a statistical test, described further below. 

In order to test whether the differences of variance explained by task variables between DLPFC and PMd are significant, we performed a shuffle test. For this test, we randomly sampled 500 units from the DLPFC dataset and 500 units from the PMd dataset. We then used dPCA to measure the variance explained by target configuration, color choice, and reach direction (e.g., Var^True_DLPFC,Color, Var^True_PMd,Color).

To test if this variance was significant, we performed the following shuffle test. We combined the PMd and DLPFC dataset into a pool of 1000 units and then randomly selected 500 units from this pool to create a surrogate PMd dataset and used the remaining 500 units as a surrogate DLPFC dataset. We then again performed dPCA on these surrogate datasets and estimated the variance for the various task variables (e.g., Var_{ShuffledDLPFC,Color}  ,Var_{ShuffledPMd,Color}).

We repeated this process for 100 times and estimated a sampling distribution for the true difference in variance between DLPFC and PMd for various task variables (e.g., Var^True_DLPFC,Color - Var^True_PMd,Color). At the same time, we estimated the distribution of the variance difference between surrogate PMd and DLPFC dataset for various task variables (e.g., Var_{ShuffleDLPFC,Color} - Var_{ShufflePMd,Color}). 

We defined a p-value as the number of shuffles in which the difference in variance was higher than the median of the true difference and divided it by 100. Note, for resampling and shuffle tests with n shuffles/bootstraps, the lowest theoretical p-value is given as 2/n, even in the case that no shuffle was higher than the median of the true distribution. Thus, the differences were statistically significant (p < 0.02) for color and target configuration but not for direction (p=0.72). These results are reported in Figure S6 and show both the true sampling distribution and the shuffled sampling distributions.

(b) I would have assumed that the analyses performed on the neural data were identical to the ones performed on the RNN data. However, it looked to me like that was not the case. For instance, dPCA of the neural data is done by restretching randomly timed trials to a median trial. It seemed that this restretching was not performed on the RNN. Maybe that is just an oversight, but it should be clarified. Moreover, the decoding analyses used SVC for the neural data, but a neural-net-based approach for the RNN data. Why the differences?

Thanks for bringing up these points. We want to clarify that we did include SVM decoding for the multi-area network in the appendix (Fig. S4), and the conclusions are the same. Moreover, in previous work, we also found that training with a linear decoder led to analogous conclusions (Fig. 11 of Kleinman et al, NeurIPS 2021).  As we had a larger amount of trials for the RNN than the monkey, we wanted to allow a more expressive decoder for the RNN, though this choice does not affect our conclusions. We clarified the text to reflect that we did use an SVM decoder.

“We also found analogous conclusions when using an SVM decoder (Fig. S4).”

dPCA analysis requires trials of equal length. For the RNN, this is straightforward to generate because we can set the delay lengths to be equal during inference (although the RNN was trained on various length trials and can perform various length trials). Animals must have varying delay periods, or else they will learn the timing of the task and anticipate epoch changes. Because animal trial lengths were therefore different, their trials had to be restretched. We clarified this in the Methods.

“For analyses of the RNN, we fixed the timing of trials, obviating the need to to restretch trial lengths. Note that while at inference, we generated RNN trials with equal length, the RNN was trained with varying delay periods.” 

(4) The RNN seems to fit the data quite nicely, so that is interesting. At the same time, the fit seems somewhat serendipitous, or at least, I did not get a good sense of what was needed to make the RNN fit the data. The authors did go to great lengths to fit various network models and turn several knobs on the fit. However, at least to me, there are a few (obvious) knobs that were not tested.

First, as already mentioned above, why not try to fit a single-area model? I would expect that a single area model could also learn the task - after all, that is what Mante et al did in their 2013 paper and the author's task does not seem any more complex than the task by Mante and colleagues.

Thank you for bringing up this point. As mentioned in response to your prior point, we did analyze a single-area RNN (Fig. 5d). We updated the schematic to clarify that we analyzed a single area network. Moreover, we also added a supplementary figure to qualitatively visualize the PCs of the single area network (Fig. S15). While a single area network can solve the task, it does not allow us to study how representations change across areas, nor did it empirically resemble our neural recordings. Single-area networks contain significant color, context, and direction information. They therefore do not form minimal representations and do not resemble PMd activity.

Second, I noticed that the networks fitted are always feedforward-dominated. What happens when feedforward and feedback connections are on an equal footing? Do we still find that only the decision information propagates to the next area? Quite generally, when it comes to attenuating information that is fed into the network (e.g. color), then that is much easier done through feedforward connections (where it can be done in a single pass, through proper alignment or misalignment of the feedforward synapses) than through recurrent connections (where you need to actively cancel the incoming information). So it seems to me that the reason the attenuation occurs in the inter-area connections could simply be because the odds are a priori stacked against recurrent connections. In the real brain, of course, there is no clear evidence that feedforward connections dominate over feedback connections anatomically.

We want to clarify that we did pick feedforward and feedback connections based on the following macaque atlas, reference 27 in our manuscript: 

Markov, N. T., Ercsey-Ravasz, M. M., Ribeiro Gomes, A. R., Lamy, C., Magrou, L., Vezoli, J., Misery, P., Falchier, A., Quilodran, R., Gariel, M. A., Sallet, J., Gamanut, R., Huissoud, C., Clavagnier, S., Giroud, P., Sappey-Marinier, D., Barone, P., Dehay, C., Toroczkai, Z., … Kennedy, H. (2014). A weighted and directed interareal connectivity matrix for macaque cerebral cortex. Cerebral Cortex , 24(1), 17–36.

We therefore believe there is evidence for more feedforward than feedback connections. Nevertheless, as stated in response to your next point below, we ran a simulation where feedback and feedforward connectivity were matched.

More generally, it would be useful to clarify what exactly is sufficient:

(a) the information distribution occurs in any RNN, i.e., also in one-area RNNs

(b) the information distribution occurs when there are several, sparsely connected areas

(c) the information distribution occurs when there are feedforward-dominated connections between areas

We better clarify what exactly is sufficient. 

- We trained single-area RNNs and found that these RNNs contained color information; additionally two area RNNs also contained color information in the last area (Fig 5d). 

- We indeed found that the minimal sufficient representations emerged when we had several areas, with Dale’s law constraint on the connectivity. When we had even sparser connections, without Dale’s law, there was significantly more color information, even at 1% feedforward connections; Fig 5a.

- When we matched the percentage of feedforward and feedback connections with Dale’s law constraint on the connectivity (10% feedforward and 10% feedback), we also observed minimal sufficient representations (Fig S9). 

Together, we found that minimal sufficient representations emerged when we had several areas (3 or greater), with Dale’s law constraint on the connectivity, independent of the ratio of feedforward/feedback connections. We thank the reviewer for raising this point about the space of constraints leading to minimal sufficient representations in the late area. We clarified this in the Discussion.

“We also found it was possible to solve this task with single area RNNs, although they did not resemble PMd (Figure S15) since it did not form a minimal sufficient representation. Rather, for our RNN simulations, we found that the following components were sufficient to induce minimal sufficient representations: RNNs with at least 3 areas, following Dale’s law (independent of the ratio of feedforward to feedback connections).”

Thank you for your helpful and constructive comments!

Reviewer #2 (Public Review):

Kleinman and colleagues conducted an analysis of two datasets, one recorded from DLPFC in one monkey and the other from PMD in two monkeys. They also performed similar analyses on trained RNNs with various architectures.

The study revealed four main findings. (1) All task variables (color coherence, target configuration, and choice direction) were found to be encoded in DLPFC. (2) PMD, an area downstream of PFC, only encoded choice direction. (3) These empirical findings align with the celebrated 'information bottleneck principle,' which suggests that FF networks progressively filter out task-irrelevant information. (4) Moreover, similar results were observed in RNNs with three modules.

We thank the reviewer for their comments, feedback and suggestions, which we address below.

While the analyses supporting results 1 and 2 were convincing and robust, I have some concerns and recommendations regarding findings 3 and 4, which I will elaborate on below. It is important to note that findings 2 and 4 had already been reported in a previous publication by the same authors (ref. 43).

Note the NeurIPS paper only had PMd data and did not contain any DLPFC data. That manuscript made predictions about representations and dynamics upstream of PMd, and subsequent experiments reported in this manuscript validated these predictions. Importantly, this manuscript observes an information bottleneck between DLPFC and PMd.

Major recommendation/comments:

The interpretation of the empirical findings regarding the communication subspace in relation to the information bottleneck theory is very interesting and novel. However, it may be a stretch to apply this interpretation directly to PFC-PMd, as was done with early vs. late areas of a FF neural network.

In the RNN simulations, the main finding indicates that a network with three or more modules lacks information about the stimulus in the third or subsequent modules. The authors draw a direct analogy between monkey PFC and PMd and Modules 1 and 3 of the RNNs, respectively. However, considering the model's architecture, it seems more appropriate to map Area 1 to regions upstream of PFC, such as the visual cortex, since Area 1 receives visual stimuli. Moreover, both PFC and PMd are deep within the brain hierarchy, suggesting a more natural mapping to later areas. This contradicts the CCA analysis in Figure 3e. It is recommended to either remap the areas or provide further support for the current mapping choice.

We updated the Introduction to better clarify the predictions of the information bottleneck (IB) principle. In particular, the IB principle predicts that later areas should have minimal sufficient representations of task information, whereas upstream areas should have more information. In PMd, we observed a minimal sufficient representation of task information during the decision-making task. In DLPFC, we observed more task information, particularly more information about the target colors and the target configuration.

In terms of the exact map between areas, we do not believe or intend to claim the DLPFC is the first area implicated in the sensorimotor transformation during our perceptual decision-making task. Rather, DLPFC best matches Area 1 of our model. It is important to note that we abstracted our task so that the first area of our model received checkerboard coherence and target configuration as input (and hence did not need to transform task visual inputs). Indeed, in Figure 1d we hypothesize that the early visual areas should contain additional information, which we do not model directly in this work. Future work could model RNNs to take in an image or video input of the task stimulus. In this case, it would be interesting to assess if earlier areas resemble visual cortical areas. We updated the results, where we first present the RNN, to state the inputs explicitly and be clear the inputs are not images or videos of the checkerboard task.

“The RNN input was 4D representing the target configuration and checkerboard signed coherence, while the RNN output was 2D, representing decision variables for a left and right reach (see Methods).”

Another reason that we mapped Area 1 to DLPFC is because anatomical, physiological and lesion studies suggest that DLPFC receives inputs from both the dorsal and ventral stream (Romanski, et, al, 2007; Hoshi, et al, 2006; Wilson, at al, 1993). The dorsal stream originates from the occipital lobe, passes through the posterior parietal cortex, to DLPFC, which carries visuospatial information of the object. The ventral stream originates from the occipital lobe, passes through the inferior temporal cortex, ventrolateral prefrontal cortex to DLPFC, which encodes the identity of the object, including color and texture. In our RNN simulation, Area 1 receives processed inputs of the task: target configuration and the evidence for each color in the checkerboard. Target configuration contains information of the spatial location of the targets, which represents the inputs from the dorsal stream, while evidence for each color by analogy is the input from the ventral stream. Purely visual areas would not fit this dual input from both the dorsal and ventral stream. A potential alternative candidate would be the parietal cortex which is largely part of the dorsal stream and is thought to have modest color inputs (although there is some shape and color selectivity in areas such as LIP, e.g., work from Sereno et al.). On balance given the strong inputs from both the dorsal and ventral stream, we believe Area 1 maps better on to DLPFC than earlier visual areas.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Line 35/36: Please specify the type of nuisance that the representation is robust to. I guess this refers to small changes in the inputs, not to changes in the representation itself.

Indeed it refers to input variability unrelated to the task. We clarified the text.

(2) For reference, it would be nice to have a tick for the event "Targets on" in Fig.2c.

In this plot, the PSTHs are aligned to the checkerboard onset. Because there is a variable time between target and checkerboard onset, there is a trial-by-trial difference of when the target was turned on, so there is no single place on the x-axis where we could place a “Targets on” tick. In response to this point, we generated a plot with both targets on and check on alignment, with a break in the middle, shown in Supplementary Figure S5. 

(3) It would strengthen the comparison between neural data and RNN if the DPCA components of the RNN areas were shown, as they are shown in Fig.2g,h for the neural data.

We include the PSTHs plotted onto the dPCA components here for Area 1 of the exemplar network. Dashed lines indicate a left reach, while solid lines indicate a right reach, and the color corresponds to the color of the selected target. As expected, we find that the dPCA components capture the separation between components. We emphasize that the trajectory paths along the decoder axes are not particularly meaningful to interpret, except to demonstrate whether variables can be decoded or not (as in Fig 2g,h, comparing DLPFC and PMd). The decoder axes of dPCA are not constrained in any way, in contrast to the readout (encoder) axis (see Methods). This is why our manuscript focuses on analyzing the readout axes. However, if the reviewer strongly prefers these plots to be put in the manuscript, we will add them.   

Author response image 1.

(4) The session-by-session decode analysis presented in Fig.2i suggests that DLPFC has mostly direction information while in Area 1 target information is on top, as suggested by Fig.3g. An additional decoding analysis on trial averaged neural data, i.e. a figure for neural data analogous to Fig.3g,h, would allow for a more straightforward and direct comparison between RNN and neural data. 

We first clarify that we did not decode trial-averaged neural data for either recorded neural data or RNNs. In Fig 3g, h (for the RNN) all decoding was performed on single trial data and then averaged. We have revised the main manuscript to make this clear. Because of this, the mean accuracies we reported for DLPFC and PMd in the text are therefore computed in the same way as the mean accuracies presented in Fig 3g, h. We believe this likely addresses your concern: i.e., the mean decode accuracies presented for both neural data and the RNN were computed the same way. 

If the above paragraph did not address your concern, we also wish to be clear that we presented the neural data as histograms, rather than a mean with standard error, because we found that accuracies were highly variable depending on electrode insertion location. For example, some insertions in DLPFC achieved chance-levels of decoding performance for color and target configuration. For this reason, we prefer to keep the histogram as it shows more information than reporting the mean, which we report in the main text. However, if the reviewer strongly prefers us to make a bar plot of these means, we will add them.

(5) Line 129 mentions an analysis of single trials. But in Fig.2i,j sessions are analyzed. Please clarify.

For each session, we decode from single trials and then average these decoding accuracies, leading to a per-session average decoding accuracy. Note that for each session, we record from different neurons. In the text, we also report the average over the sessions. We clarified this in the text and Methods.

(6) Fig.4c,f show how color and direction axes align with the potent subspaces. We assume that the target axis was omitted here because it highly aligns with the color axis, yet we note that this was not pointed out explicitly.

You are correct, and we revised the text to point this out explicitly.

“We quantified how the color and direction axis were aligned with these potent and null spaces of the intra-areal recurrent dynamics matrix of Area 1 ($\W^1_{rec}$). We did not include the target configuration axis for simplicity, since it highly aligns with the color axis for this network.”

(7) The caption of Fig.4c reads: "Projections onto the potent space of the intra-areal dynamics for each area." Yet, they only show area 1 in Fig.4c, and the rest in a supplement figure. Please refer properly.

Thank you for pointing this out. We updated the text to reference the supplementary figure.

(8) Line 300: "We found the direction axis was more aligned with the potent space and the color axis was more aligned with the null space." They rather show that the color axis is as aligned to the potent space as a random vector, but nothing about the alignments with the null space. Contrarily, on line 379 they write "...with the important difference that color information isn't preferentially projected to a nullspace...". Please clarify.

Thank you for pointing this out. We clarified the text to read: “We found the direction axis was more aligned with the potent space”. The text then describes that the color axis is aligned like a random vector: “In contrast, the color axis was aligned to a random vector.”

(9) Line 313: 'unconstrained' networks are mentioned. What constraints are implied there, Dale's law? Please define and clarify.

Indeed, the constraint refers to Dale’s law constraints. We clarified the text: “Further, we found that W₂₁ in unconstrained 3 area networks (i.e., without Dale's law constraints) had significantly reduced…”

(10) Line 355 mentions a 'feedforward bottleneck'. What does this exactly mean? No E-I feedforward connections, or...? Please define and clarify.

This refers to sparser connections between areas than within an area, as well as a smaller fraction of E-I connections. We clarified the text to read:

“Together, these results suggest  that a connection bottleneck in the form of neurophysiological architecture constraints (i.e., sparser connections between areas than within an area, as well as a smaller fraction of E-I connections) was the key design choice leading to RNNs with minimal color representations and consistent with the information bottleneck principle.”

(11) Fig.5c is supposedly without feedforward connections, but it looks like the plot depicts these connections (i.e. identical to Fig.5b).

In Figure 5, we are varying the E to I connectivity in panel B, and the E-E connectivity in panel C. We vary the feedback connections in Supp Fig. S12. We updated the caption accordingly. 

(12) For reference, it would be nice to have the parameters of the exemplar network indicated in the panels of Fig.5.

We updated the caption to reference the parameter configuration in Table 1 of the Appendix.

(13) Line 659: incomplete sentence

Thank you for pointing this out. We removed this incomplete sentence.

(14) In the methods section "Decoding and Mutual information for RNNs" a linear neural net decoder as well as a nonlinear neural net decoder are described, yet it was unclear which one was used in the end.

We used the nonlinear network, and clarified the text accordingly. We obtained consistent conclusions using a linear network, but did not include these results in the text. (These are reported in Fig. 11 of Kleinman et al, 2021). Moreover, we also obtain consistent results by using an SVM decoder in Fig. S4 for our exemplar parameter configuration.

(15) In the discussion, the paragraph starting from line 410 introduces a new set of results along with the benefits of minimal representations. This should go to the results section.

We prefer to leave this as a discussion, since the task was potentially too simplistic to generate a clear conclusion on this matter. We believe this remains a discussion point for further investigation.

(16) Fig S5: hard to parse. Show some arrows for trajectories (a) (d) is pretty mysterious: where do I see the slow dynamics?

Slow points are denoted by crosses, which forms an approximate line attractor. We clarified this in the caption.

Reviewer #2 (Recommendations For The Authors):

Minor recommendations (not ordered by importance)

(1) Be more explicit that the recordings come from different monkeys and are not simultaneously recorded. For instance, say 'recordings from PFC or PMD'. Say early on that PMD recordings come from two monkeys and that PFC recordings come from 1 of those monkeys. Furthermore, I would highlight which datasets are novel and which are not. For instance, I believe the PFC dataset is a previously unpublished dataset and should be highlighted as such.

We added: “The PMd data was previously described in a study by Chandrasekaran and colleagues” to the main text which clarifies that the PMd data was previously recorded and has been analyzed in other studies.

(2) I personally feel that talking about 'optimal', as is done in the abstract, is a bit of a stretch for this simple task.

In using the terminology “optimal,” we are following the convention of IB literature that optimal representations are sufficient and minimal. The term “optimal” therefore is task-specific; every task will have its own optimal representation. We clarify in the text that this definition comes from Machine Learning and Information Theory, stating:

“The IB principle defines an optimal representation as a representation that is minimal and sufficient for a task or set of tasks.”

In this way, we take an information-theoretic view for describing multi-area representations. This view was satisfactory for explaining and reconciling the multi-area recordings and simulations for this task, and we think it is helpful to provide a normative perspective for explaining the differences in cortical representations by brain area. Even though the task is simple, it still allows us to study how sensory/perceptual information is represented, and well as how choice-related information is being represented.

(3) It is mentioned (and even highlighted) in the abstract that we don't know why the brain distributes computations. I agree with that statement, but I don't think this manuscript answers that question. Relatedly, the introduction mentions robustness as one reason why the brain would distribute computations, but then raises the question of whether there is 'also a computational benefit for distributing computations across multiple areas'. Isn't the latter (robustness) a clear 'computational benefit'?

We decided to keep the word “why” in the abstract, because this is a generally true statement (it is unclear why the brain distributes computation) that we wish to convey succinctly, pointing to the importance of studying this relatively grand question (which could only be fully answered by many studies over decades). We consider this the setting of our work. However, to avoid confusion that we are trying to give a full answer to this question, we are now more precise in the first paragraph of our introduction as to the particular questions we ask that will take a step towards this question. In particular, the first paragraph now asks these questions, which we answer in our study.

“For example, is all stimuli and decision-related information present in all brain areas, or do the cortical representations differ depending on their processing stage? If the representations differ, are there general principles that can explain why the cortical representations differ by brain area?”

We also removed the language on robustness, as we agree it was confusing. Thank you for these suggestions. 

(4) Figure 2e and Fig. 3d, left, do not look very similar. I suggest zooming in or rotating Figure 2 to highlight the similarities. Consider generating a baseline CCA correlation using some sort of data shuffle to highlight the differences.

The main point of the trajectories is to demonstrate that both Area 1 and DLPFC represent both color and direction. We now clarify this in the manuscript. However, we do not intend for these two plots to be a rigorous comparison of similarity. Rather, we quantify similarity using CCA and our decoding analysis. We also better emphasize the relative values of the CCA, rather than the absolute values.

(5) Line 152: 'For this analysis, we restricted it to sessions with significant decode accuracy with a session considered to have a significant decodability for a variable if the true accuracy was above the 99th percentile of the shuffled accuracy for a session.' Why? Sounds fishy, especially if one is building a case on 'non-decodability'. I would either not do it or better justify it.

The reason to choose only sessions with significant decoding accuracy is that we consider those sessions to be the sessions containing information of task variables. In response to this comment, we also now generate a plot with all recording sessions in Supplementary Figure S7. We modified the manuscript accordingly.

“For this analysis, we restricted it to sessions with significant decode accuracy with a session considered to have a significant decodability for a variable if the true accuracy was above the 99th percentile of the shuffled accuracy for a session. This is because these sessions contain information about task variables. However, we also present the same analyses using all sessions in Fig. S7.”

(6) Line 232: 'The RNN therefore models many aspects of our physiological data and is therefore'. Many seems a stretch?

We changed “many” to “key.”

(7) The illustration in Fig. 4B is very hard to understand, I recommend removing it.

We are unsure what this refers to, as Figure 4B represents data of axis overlaps and is not an illustration. 

(8) At some point the authors use IB instead of information bottleneck (eg line 288), I would not do it.

We now clearly write that IB is an abbreviation of Information Bottleneck the first time it is introduced.  

(9) Fig. 5 caption is insufficient to understand it. Text in the main document does not help. I would move most part of this figure, or at least F, to supplementary. Instead, I would move the results in S11 and S10 to the main document.

We clarified the caption to summarize the key points. It now reads: 

“Overall, neurophysiological architecture constraints in the form of multiple areas, sparser connections between areas than within an area, as well as a smaller fraction of E-I connections lead to a minimal color representation in the last area.”

(10) Line 355: 'Together, these results suggest that a connection bottleneck in the form of neurophysiological architecture constraints was the key design choice leading to RNNs with minimal color representations and consistent with the information bottleneck principle.' The authors show convincingly that increased sparsity leads to the removal of irrelevant information. There is an alternative model of the communication subspace hypothesis that uses low-rank matrices, instead of sparse, to implement said bottlenecks (https://www.biorxiv.org/content/10.1101/2022.07.21.500962v2)

We thank the reviewer for pointing us to this very nice paper. Indeed, a low-rank connectivity matrix is another mechanism to limit the amount of information that is passed to subsequent areas. In fact, the low-rank matrix forms a hard-version of our observations as we found that task-relevant information was preferentially propagated along the top singular mode of the inter-areal connectivity matrix. In our paper we observed this tendency naturally emerges through training with neurophysiological architecture constraints. In the paper, for the multi-area RNN, they hand-engineered the multi-area network, whereas our network is trained. We added this reference to our discussion. 

Thank you for your helpful and constructive comments.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this work by Wang et al., the authors use single-molecule super-resolution microscopy together with biochemical assays to quantify the organization of Nipah virus fusion protein F (NiV-F) on cell and viral membranes. They find that these proteins form nanoscale clusters which favors membrane fusion activation, and that the physical parameters of these clusters are unaffected by protein expression level and endosomal cleavage. Furthermore, they find that the cluster organization is affected by mutations in the trimer interface on the NiV-F ectodomain and the putative oligomerization motif on the transmembrane domain, and that the clusters are stabilized by interactions among NiV-F, the AP2-complex, and the clathrin coat assembly. This work improves our understanding of the NiV fusion machinery, which may have implications also for our understanding of the function of other viruses.

Strengths:

The conclusions of this paper are well-supported by the presented data. This study sheds light on the activation mechanisms underlying the NiV fusion machinery.

Weaknesses:

The authors provide limited details of the convolutional neural network they developed in this work. Even though custom-codes are made available, a description of the network and specifications of how it was used in this work would aid the readers in assessing its performance and applicability. The same holds for the custom-written OPTICS algorithm. Furthermore, limited details are provided for the imaging setup, oxygen scavenging buffer, and analysis for the single-molecule data, which limits reproducibility in other laboratories. The claim of 10 nm resolution is not backed up by data and seems low given the imaging conditions and fluorophores used. Fourier Ring Correlation analysis would have validated this claim. If the authors refer to localization precision rather than resolution, then this should be specified and appropriate data provided to support this claim.

We thank reviewer 1 for these suggestions. We described key steps in imaging setup, singlemolecule data reconstruction, the OPTICS algorithm in cluster identification, and 1D CNN in

classification of the OPTICS data in the Materials and Methods section. We also provided a recipe for the imaging buffer. We refer to 10 nm localization precision rather than resolution. The localization precision achieved by our SMLM system is shown in the Author response image 1.

Author response image 1.

The localization precision of the custom-built SMLM. Shows the distribution of localization error at the x (dX), y (dY), and z (dZ) direction in nanometer of blinks generated from Alexa Flour 647 labeled to NiV-F expressed on the plasma membrane of PK13 cells. The lateral precision is <10 nm and the axial precision is < 20 nm. 

Reviewer #2 (Public Review): 

Summary:

In this manuscript, Wang and co-workers employ single molecule light microscopy (SMLM) to detect NiV fusion protein (NiV-F) in the surface of cells. They corroborate that these glycoproteins form microclusters (previously seen and characterized together with the NiVG and Nipah Matrix protein by Liu and co-workers (2018) also with super-resolution light microscopy). Also seen by Liu and coworkers the authors show that the level of expression of NiV-F does not alter the identity of these microclusters nor endosomal cleavage. Moreover, mutations and the transmembrane domain or the hexamer-of-trimer interface seem to have a mild effect on the size of the clusters that the authors quantified.

Importantly, it has also been shown that these particles tend to cluster in Nipah VLPs.

We thank reviewer #2 for the comments and suggestions. This paper is built on Liu et al 1 to further characterize the nanoclusters formed by NiV-F and their role in membrane fusion activation. While Liu et al. studied the NiV glycoprotein distribution at the NiV assembly sites to inform mechanisms in NiV assembly and release, Wang et al. analyzed the nanoorganization and distribution of NiV-F at the prefusion conformation, providing insights into the membrane fusion activation mechanisms.  

Strengths:

The authors have tried to perform SMLM in single VLPs and have shown partially the importance of NiV-F clustering.

Weaknesses:

The labelling strategy for the NiV-F is not sufficiently explained. The use of a FLAG tag in the extracellular domain should be validated and compared with the unlabelled WT NiV-F when expressed in functional pseudoviruses (for example HIV-1 based particles decorated with NiV-F). This experiment should also be carried out for both infection and fusion (including BlaM-Vpr as a readout for fusion). I would also suggest to run a time-of-addition BlaM experiment to understand how this particular labelling strategy affects single virion fusion as compared to the the WT.  

We thank reviewer #2 for this suggestion. We have made various efforts to validate the expression and function of FLAG-tagged NiV-F. The NiV-F-FLAG shows comparable cell surface expression levels and induces similar cell-cell fusion levels in 293T cells as that of untagged NiV-F 1. The NiV-F-FLAG also showed similar levels of virus entry as untagged NiV-F when both were pseudotyped on a recombinant Vesicular Stomatitis Virus (VSV) with the VSV glycoprotein replaced by a Renilla luciferase reporter gene (VSV-ΔG-rLuc; Fig. S1D). We also performed a virus entry kinetics assay using NiV VLPs expressing NiV-M-βlactamase (NiV-M-Bla), NiV-G-HA, and NiV-F-FLAG, NiV-F-AU1 or untagged NiV-F. The intracellular AU1 tag is located at the C-terminus of NiV-F (Genbank accession no. AY816748.1). However, we detected different levels of NiV-M-Bla in equal volume of VLPs, suggesting that the tags in NiV-F affect the budding of the VLPs (Author response image 2A). Therefore, we performed fusion kinetics assay by using VLPs expressing the same levels of NiV-M-Bla. Among them, the NiV-F-FLAG on VLPs shows the most efficient fusion between VLP and HEK293T cell membranes (Author response image 2B), significantly more efficient than that of untagged NiV-F and NiV-FAU1. However, we cannot attribute the enhanced fusion activity to the FLAG tag, because the readout of this assay relies on both the levels of β-lactamase (introduced by NiV-M-Bla in VLPs) and the NiV-F constructs. The tags in NiV-F could affect both the budding of VLPs and the stoichiometry of F and M in individual VLPs. We did not use the HIV-based pseudovirus system because the incorporation of NiV-F into HIV pseudoviruses requires a C-terminal deletion 2,3.

In summary, the FLAG tag does not affect cell-cell fusion 1 and virus entry when pseudotyped to the recombinant VSV-ΔG-rLuc viruses (Fig. S1D). Given that we do not observe any difference in clustering between an HA- and FLAG-tagged NiV-F constructs on PK13 cell surface (Fig. S1A-C), we conclude that the FLAG tag has minimal effect on both the fusion activity and the nanoscale distribution of NiV-F. 

Author response image 2.

Viral entry is not affected by labeling of NiV-F. A) Western blot analysis of NiV-M-Bla in NiV-VLPs generated by HEK293T cells expressing NiV-M-Bla, NiV-G-HA and NiV-F-FLAG, untagged NiV-F, or NiV-F-AU1. Equal volume of VLPs were separated by a denaturing 10% SDS–PAGE and probed against β-lactamase (SANTA CRUZ, sc-66062). B) NiV-VLPs expressing NiV-M-BLa, NiV-G-HA, and NiV-F-FLAG, untagged NiV-F or NiV-F-AU1 expression plasmids were bond to the target HEK293T cells loaded with CCF2-AM dye at 4°C. The Blue/Green (B/G) ratio was measured at 37°C for 4 hrs at a 3-min interval. Results were normalized to the maximal B/G ratio of NiV-F-FLAG-NiV VLPs. Results from one representative experiment out of three independent experiments are shown. 

It would also be very important to compare the FLAG labelling approach with recent advances in the field (for instance incorporating noncanonical amino acids (ncAAs) into NiVF by amber stop-codon suppression, followed by click chemistry). 

We are greatly thankful for this comment from reviewer #2. Labeling noncanonical amino acids (ncAAs) with biorthogonal click chemistry is indeed a more precise labeling strategy compared to the traditional epitope labeling approach used in this paper. We will explore the applications of ncAAs labeling in single-molecule localization imaging and virus-host interactions in future projects. 

In this paper, the FLAG tag inserted in NiV-F protein seems to have minimal effect on the NiV-F-induced virus entry and cell-cell fusion 1 (Fig. S1). Although the FLAG tag labeling approach may increase the detectable size of NiV-F nanoclusters due to the use of the antibody complex, it should not affect our conclusions drawn from the relative comparisons between wt and mutant NiV-F or control and drug-treated cells. 

The correlation between the existence of microclusters of a particular size and their functionality is missing. Only cell-cell fusion assays are shown in supplementary figures and clearly, single virus entry and fusion cannot be compared with the biophysics of cell-cell fusion. Not only the environment is completely different, membrane curvature and the number of NiV-F drastically varies also. Therefore, specific fusion assays (either single virus tracking and/or time-of-addition BlaM kinetics with functional pseudoviruses) are needed to substantiate this claim.  

We thank Reviewer 2 for the suggestion. To support the link between F clustering and viruscell membrane fusion, we conducted pseudotyped virus entry and VLP fusion kinetics assays, as shown in revised Figure S4. The viral entry results (Fig. S4 E and F) corroborate that of the cell-cell fusion assay (Fig. S4A and B) and previously published data 4. The fusion kinetics confirmed that the real-time fusion kinetics was affected by mutations at the hexameric interface, with the hypo-fusogenic mutants L53D and V108D exhibited reduced entry efficiency while the hyper-fusogenic mutant Q393L showed increased efficiency (Fig. S4G and H). The results were described in detail in the revised manuscript. 

Additionally, we performed a pseudotyped virus entry assay on the LI4A (Fig. S6F and G) and YA (Fig. S7F and G) mutants to verify the function of these mutants on viruses in revised Supplemental Figures. Neither LI4A nor YA incorporated into the VSV/NiV pseudotyped viruses as shown by the Western blot analyses of the pseudovirions (Fig. S6F and S7F), and thus did not induce virus entry, consisting with the cell-cell fusion results (Fig. S6C, D and Fig. S7C, D). We did not perform the entry kinetic assay of these two mutants as they do not incorporate into VLPs or pseudovirions. 

The authors also claim they could not characterize the number of NiV-F particles per cluster. Another technique such as number and brightness (Digman et al., 2008) could support current SMLM data and identify the number of single molecules per cluster. Also, this technology does not require complex microscopy apparatus. I suggest they perform either confocal fluorescence fluctuation spectroscopy or TIRF-based nandb to validate the clusters and identify how many molecule are present in these clusters.  

We thank reviewer 2 for this suggestion. Determining the true copy number of NiV-F in individual clusters could verify whether the F clusters on the plasma membrane are hexamer-of-trimer assemblies. Regardless, it does not affect our conclusion that the organization of NiV-F into nanoclusters affects the membrane fusion triggering ability. The confocal fluorescence fluctuation spectroscopy (FFS) and TIRF-based analyses are accessible tools for quantifying fluorophore copy numbers and/or stoichiometry based on fluorescence fluctuation or photobleaching. However, these methods are unable to quantify the number of proteins in individual clusters because they analyze fluorophores either in the entire cell (as in wide-field epifluorescence microscopy coupled with FFS and TIRF-coupled photobleaching) 5–7 or within a large excitation volume (confocal laser scanning microscopycoupled FFS) 8. Both of these volumes are significantly larger than a single NiV-F cluster, which has an average diameter of 24-26 nm (Fig. 1F). 

The current SMLM setup is useful for characterizing the protein distribution and organization. However, quantifying the true protein copy number within a nanocluster is challenging because of the stochasticity of fluorophore blinking and the unknown labeling stoichiometry 9–11. To address the challenge in fluorophore blinking, quantitative DNA-PAINT (qDNA-PAINT) may be used because the on-off frequency of the fluorophores is tied to the well-defined kinetic constants of DNA binding and the influx rate of the imager strands, rather than the stochasticity of fluorophore blinking. Thus, the frequency of blinks can be translated to protein counting 12. To address the challenge in unknown labeling stoichiometry, DNA origami can be used as a calibration standard 11. DNA origami supports handles at a regular space with several to tens of nanometers apart, and the handles can be conjugated with a certain number of proteins of interest. The copy number of protein interest in the experimental group can be determined by comparing the SMLM localization distribution of the sample to that of the DNA origami calibration standard. Given the requirement of a more sophisticated SMLM setup and a high-precision calibration tool, we will explore the quantification of NiV-F copy numbers in nanoclusters in a future project. 

Also, it is not clear how many cells the authors employ for their statistics (at least 30-50 cells should be employed and not consider the number of events blinking events. I hope the authors are not considering only a single cell to run their stats... The differences between the mutants and the NiV-F is minor even if their statistical analyses give a difference (they should average the number and size of the clusters per cell for a total of 30-50 cells with experiments performed at least in three different cells following the same protocol). Overall, it seems that the authors have only evaluated a very low number of cells.

We disagree with this comment from Reviewer #2. The sample size for cluster analysis in SMLM images was chosen by considering the target of the study (cells and VLPs) and the data acquisition and analysis standards in the SMLM imaging field. We also noted the sample size (# of ROI and cells) in the figure legend. 

Below, we compared the sample sizes in our study to those in similar studies that used comparable imaging and cluster analysis methods from 2015 to 2024. The classical clustering analysis methods are categorized into global clustering (e.g. nearest neighbor analysis, Ripley’s K function, and pair correlation function) and complete clustering, such as density-based analysis (e.g. DBSCAN, Superstructure, FOCAL, ToMATo) and Tessellationbased analysis (e.g. Delaunay triangulation, Voronoii Tessellation). The global clustering analysis method provides spatial statistics for global protein clustering or organization (e.g. clustering extent), while the complete clustering approach extracts information from a single-cluster level, such as the morphology and localization density of individual clusters. We used the density-based analyses, DBSCAN and OPTICS, for cluster analysis on cell plasma membranes and VLP membranes. 

Author response table 1.

The comparison of imaging methods, analysis methods, and sample size in the current study to other studies conducted from 2015 to 2024.

They should also compare the level of expression (with the number of molecules per cell provided by number and brightness) with the total number of clusters. 

We thank reviewer 2 for this suggestion. We compared the level of expression with the total number of clusters for F-WT in Figure 1I in the main text.  

The same applies to the VLP assay. I assume the authors have only taken VLPs expressing both NiV-M and NiV-F (and NiV-G). But even if this is not clearly stated I would urge the authors to show how many viruses were compared per condition (normally I would expect 300 particles per condition coming from three independent experiments. As a negative control to evaluate the cluster effect I would mix the different conditions. Clearly you have clusters with all conditions and the differences in clustering depending on each condition are minimal. Therefore you need to increase the n for all experiments.

We thank reviewer 2 for this comment. We acquired and analyzed more images of NiV VLPs bearing F-WT, Q393L, L53D, and V108D. Results are shown in the revised Figure 4 and the number of VLPs (>300) used for analysis is specified in the figure legend. An increased number of VLP images does not affect the classification result in Figure 4C. 

As for the suggestion on “evaluating the cluster effect at different mixed conditions”, I assume that reviewer 2 would like to see how the presence of different viral structural proteins (F, M, and G) on VLPs could affect F clustering.  We showed that the organization of NiV envelope proteins on the VLP membrane is similar in the presence or absence of NiV-M by direct visualization 27, suggesting that the effect of NiV-M on F-WT clustering on VLPs is minimal. We also show comparable incorporation of NiV-F among the NiV-F hexamer-oftrimer mutants (Fig. 4A). Therefore, we did not test the F clustering at different F, M, and G combinations in this paper. However, this could be an interesting question to pursue in a paper focusing on NiV VLP production. 

Reviewer #3 (Public Review):

Summary:

The manuscript by Wang and colleagues describes single molecule localization microscopy to quantify the distribution and organization of Nipah virus F expressed on cells and on virus-like particles. Notably the crystal structure of F indicated hexameric assemblies of F trimers. The authors propose that F clustering favors membrane fusion.

Strengths:

The manuscript provides solid data on imaging of F clustering with the main findings of:

-  F clusters are independent of expression levels

-  Proteolytic cleavage does not affect F clustering

-  Mutations that have been reported to affect the hexamer interface reduce clustering on cells and its distribution on VLPs - - F nanoclusters are stabilized by AP

Weaknesses:

The relationship between F clustering and fusion is per se interesting, but looking at F clusters on the plasma membrane does not exclude that F clustering occurs for budding. Many viral glycoproteins cluster at the plasma membrane to generate micro domains for budding. 

This does not exclude that these clusters include hexamer assemblies or clustering requires hexamer assemblies. 

We thank reviewer #3 for this question. We did not focus on the role of NiV-F clusters for budding in the current manuscript, although this is an interesting topic to pursue. In this manuscript, we observed that NiV VLP budding is decreased for some cluster-disrupting mutants, such as F-YA, and F-LI4A. however, F-V108D showed increased budding compared to F-WT (Fig. 4A). We also observed that VLPs and VSV/NiV pseudoviruses expressing L53D have little NiV-G (Fig. 4A, Fig. S4F and S4H), although the incorporation level of L53D is comparable to that of wt F in both VLPs and pseudovirions (Fig. 4A and Fig. S4F). L53D is a hypofusogenic mutant with decreased clustering ability. Therefore, our current data do not show a clear link between F clustering and NiV VLP budding or glycoprotein incorporation. 

We reported that both NiV-F and -M form clusters at the plasma membrane although NiV-F clusters are not enriched at the NiV-M positive membrane domains 1. This result indicates that NiV-M is the major driving force for assembly and budding, while NiV-F is passively incorporated into the assembly sites. The central role of NiV-M in budding is also supported by a recent study showing that NiV-M induces membrane curvature by binding to PI(4,5)P2 in the inner leaflet of the plasma membrane 28. However, the expression of NiV-F alone induces the production of vesicles bearing NiV-F 29 and NiV-F recruits vesicular trafficking and actin cytoskeleton factors to VLPs either alone or in combination with NiV-G and -M, indicating a potential autonomous role in budding 30. Additionally, several electron microscopy studies show that the paramyxovirus F forms 2D lattice interspersed above the M lattice, suggesting the participation of F in virus assembly and budding. Nonetheless, the evidence above suggests that NiV-F may play a role in budding, but our data cannot correlate NiV-F clustering to budding. 

Assuming that the clusters are important for entry, hexameric clusters are not unique to Nipah virus F. Similar hexameric clusters have been described for the HEF on influenza virus C particles (Halldorsson et al 2021) and env organization on Foamy virus particles (Effantin et al 2016), both with specific interactions between trimers. What is the organization of F on Nipah virus particles? If F requires to be hexameric for entry, this should be easily imaged by EM on infectious or inactivated virus particles. 

We thank reviewer #3 for this suggestion. The hexamer-of-trimer NiV-F is observed on the VLP surface by electron tomography 4. The NiV-F hexamer-of-trimers are arranged into a soccer ball-like structure, with one trimer being part of multiple hexamer-of-trimers. The implication of NiV-F clusters in virus entry and the potential mechanism for NiV-F higherorder structure formation are discussed in the revised manuscripts. 

AP stabilization of the F clusters is curious if the clusters are solely required for entry? Virus entry does not recruit the clathrin machinery. Is it possible that F clusters are endocytosed in the absence of budding? 

We thank reviewer #3 for this question. The evidence from the current study does not exclude the role of NiV-F clustering in virus budding. NiV-F is known to be endocytosed in the virus-producing cells for cleavage by Cathepsin B or L at endocytic compartments at a pH-dependent manner31–33 in the absence of budding. However, given that all cleaved and uncleaved NiV-F have an endocytosis signal sequence at the cytoplasmic tail and are able to interact with AP-2 for endosome assembly and the cleaved and uncleaved F may have similar clustering patterns (Fig. 2), we do not think NiV-F clustering is specifically regulated for the cleavage of NiV-F. A plausible hypothesis is that NiV-F clusters are stabilized by multiple intrinsic factors (e.g. trimer interface) and host factors (e.g. AP-2) on cell membrane for cell-cell fusion and virus budding. We linked the clustering to the fusion ability of NiV-F in this study, but the NiV-F clustering may also be important in facilitating virus budding. Once in the viruses, the higher-order assembly of the clusters (e.g. lattice) may form due to protein enrichment, and the cell factors may not be the major maintenance force. 

Clusters are required for budding. 

Other points:

Fig. 3: Some of the V108D and L53D clusters look similar in size than wt clusters. It seems that the interaction is important but not absolutely essential. Would a double mutant abrogate clustering completely?

We thank Reviewer #3 for the suggestion. We generated a double mutant of NIV-F with L53D and V108D (NiV-F-LV) and assessed its expression and processing. Although the mutant retained processing capability, it exhibited minimal surface expression, making it unfeasible to analyze its nano-organization on the cell or viral membrane.

Author response image 4.

The expression and fusion activity of Flag-tagged NiV-F and NiV-F L53D-V108D (LV). (A) Representative western blot analysis of NiV-F-WT, LV in the cell lysate of 293T cells. 293T cells were transfected by NiV-F-WT or the LV mutant. The empty vector was used as a negative control. The cell lysates were analyzed on SDS-PAGE followed by western blotting after 28hrs post-transfection. F0 and F2 were probed by the M2 monoclonal mouse antiFLAG antibody. GAPDH was probed by monoclonal mouse anti-GAPDH. (B) Representative images of 293T cell-cell fusion induced by NiV-G and NiV-F-WT or NiV-F-LV. 293T cells were co-transfected with plasmids coding for NiV-G and empty vector (NC) or NiV-F constructs. Cells were fixed at 18 hrs post-transfection. Arrows point to syncytia. Scale bar: 10um. (C) Relative cell-cell fusion levels in 293T cells in (B). Five fields per experiment were counted from three independent experiments. Data are presented as mean ± SEM. (D) The cell surface expression levels of NiV-F-WT, NiV-F-LV in 293T cells measured by flow cytometry. Mean fluorescence Intensity (MFI) values were calculated by FlowJo and normalized to that of F-WT. Data are presented as mean ± SEM of three independent experiments. Statistical significance was determined by the unpaired t-test with Welch’s correction (*P<0.05, **P<0.01, ***P<0.001, ****P<0.0001). Values were compared to that of the NiV-F-WT.

Fig. 4: The distribution of F on VLPs should be confirmed by cryoEM analyses. This would also confirm the symmetry of the clusters. The manuscript by Chernomordik et al. JBC 2004 showed that influenza HA outside the direct contact zone affects fusion, which could be further elaborated in the context of F clusters and the fusion mechanism.

We thank reviewer 3 for this suggestion. The distribution of F on VLPs was resolved by electron tomogram which showed that the NiV-F hexamer-of-trimers are arranged into a soccer ball-like structure 4. The role of influenza HA outside of the contact zone in fusion activation is an interesting phenomenon. It may address the energy transmission within and among clusters. We will pursue this topic in a future project.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

•  Please define all used abbreviations throughout the manuscript and in the SI.

We defined the abbreviations at their first usage. 

•  The sentence starting with "Additionally, ..." on line 155 appears to be incomplete.

We corrected this sentence.  

•  The statement starting with "As reported, ..." on line 181 should be supported by a reference.

We added a reference. 

•  In Fig. 4C, it is unclear what the x and y axes represent.  

Fig. 4C is a t-SNE plot for visualizing high-dimensional data in a low-dimensional space. It maintains the local data structure but does not represent exact quantitative relationships. In other words, points that are close together in Fig. 4C are also close in the high-dimensional space, meaning the OPTICS plots, which reflect the clustering patterns, are similar for two points that are positioned near each other in Fig. 4C. Therefore, the x and y axes do not represent the original, quantitative data, and thus the axis titles are meaningless.  

•  The reference on line 306 appears to be unformatted.

We reformatted the reference.  

Reviewer #2 (Recommendations For The Authors):

The authors need to include the overall statistics for each experiment (at least 30 to 50 cells with three independent experiments are needed). 

We highlighted the sample size (number of ROI and number of cells) used for analysis in the figure legend. The determination of the sample size is justified in Table 1 in the response letter. 

The authors need to generate a functional pseudovirus system (for example HIVpp/NiV F) to run both infectivity and fusion experiments (including Apr-BlaM assay). 

We tested viral entry using a VSV/NiV pseudovirus system and the viral entry kinetics using VLPs expressing NiV-M-β-lactamase. The results are presented in Fig. S1, S4, S6, and S7.  

Reviewer #3 (Recommendations For The Authors):

Even low resolution EM data on VLPs or viruses would strengthen the conclusions.

We thank this reviewer for the suggestion. We cited the NiV VLP images acquired by electron tomography 4, but we currently have limited resources to perform cryoEM on NiV VLPs.  

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Author Response

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

Reviewer #1

The study provides a complete comparative interactome analysis of α-arrestin in both humans and drosophila. The authors have presented interactomes of six humans and twelve Drosophila α-arrestins using affinity purification/mass spectrometry (AP/MS). The constructed interactomes helped to find α-arrestins binding partners through common protein motifs. The authors have used bioinformatic tools and experimental data in human cells to identify the roles of TXNIP and ARRDC5: TXNIP-HADC2 interaction and ARRDC5-V-type ATPase interaction. The study reveals the PPI network for α-arrestins and examines the functions of α-arrestins in both humans and Drosophila.

Comments

I will like to congratulate the authors and the corresponding authors of this manuscript for bringing together such an elaborate study on α-arrestin and conducting a comparative study in drosophila and humans.

Introduction:

The introduction provides a rationale behind why the comparison between humans and Drosophila is carried out.

• Even though this is a research manuscript, including existing literature on similar comparison of α-arrestin from other articles will invite a wide readership.

Results:

The results cover all the necessary points concluded from the experiments and computational analysis.

1) The authors could point out the similarity of the α-arrestin in both humans and Drosophila. While comparing α-arrestin in both humans and Drosophila If percentage homology between α-arrestin of both Drosophila and humans needs to be calculated.

Thank you for your insightful feedback. As suggested by reviewer, we determined percentage homology of α-arrestin protein sequences from human and Drosophila using Clustal Omega. This homology is now illustrated as a heatmap in revised Figure S5. Please note that only the values with percentage homology of 40% or higher are selectively labeled.

• Citing the direct connecting genes from the network in the text will invite citations and a wider readership.

Figures:

The images are elaborate and well-made.

2) The authors could use a direct connected gene-gene network that pointing interactions. This can be used by other readers working on the same topic and ensure reproducibility and citations.

We appreciate your valuable comment. Based on the reviewer’s suggestion, we have developed a new website in which one can navigate the gene-gene networks of α-arrestins. These direct connected gene-gene networks are housed in the network data exchange (NDEx) project. Additionally, we have included gene ontology and protein class details for α-arrestins’ interactors in these set of networks, offering a more comprehensive view of α-arrestins’ interactomes.

On page 24 lines 15-18, we have revised the manuscript to introduce the newly developed website, as follows.

“Lastly, to assist the research community, we have made comprehensive α-arrestin interactome maps on our website (big.hanyang.ac.kr/alphaArrestin_PPIN). Researchers can search and download their interactomes of interest as well as access information on potential cellular functions and protein class associated with these interactomes.”  

3-1) The co-expression interactions represented as figures should reveal interaction among the α-arrestin and other genes. Which are the sub-network genes does the α- arrestin interact to/ with from the sub-network? The arrows are only pointing at the sub-networks. The figures do not reveal their interaction. Kindly reveal the interaction in the figure with the proper nodes in the figure.

3-2) Figure 2: the network attached in both human and drosophila is well represented. The green lines from α-arrestin indicate the strength of the interaction. Several smaller expression networks are seen. But "α-arrestin" in both organisms seems highly disconnected from all the genes. Connected genes have edges, not arrows. If α-arrestin can be shown connected to these gene-gene networks will help in identifying which genes connect with which gene through α-arrestin. This can be used by other readers working on the same topic and ensure reproducibility and citations.

Thank you for your valuable comment. In response to the reviewer’s recommendation, we’ve added supplementary figure, Figure S4, which illustrates direct interaction between α-arrestin and protein components of clustered complexes (or sub-networks) in addition to the associations shown between α-arrestins and the clustered complexes in Figure 2. We believe that this newly incorporated information regarding direct protein interactions will invite citations and wider readership as the reviewer pointed out.

On page 12 line 27 to page 13 line 5, we have revised the manuscript to cite the direction interactions between ARRDC3 and proteins involved in ubiquitination-dependent proteolysis, as follows.

“While the association of ARRDC3 with these ubiquitination-dependent proteolysis complexes is statistically insignificant, ARRDC3 does interact with individual components of these complexes such as NEDD4, NEDD4L, WWP1, and ITCH (Figure S4A). This suggest their functional relevance in this context, as previously reported in both literatures and databases (Nabhan et al., 2010; Shea et al., 2012; Szklarczyk et al., 2015; Warde-Farley et al., 2010) (Puca & Brou, 2014; Xiao et al., 2018).”

Direct interaction between α-arrestins and protein components of clustered complexes are illustrated in the newly added figure, Figure S4.

4-1) Figure 4. The Protein blot image was blurred. Kindly provide a higher-resolution image.

4-2) Figure 5. B. - The authors can provide images with higher resolution blot images. The bands were not visible.

We appreciate for valuable comment. Unfortunately, the protein blot image was scanned from the original film and the images we provided in the figure represent the highest resolution that we have obtained to date. Raw, uncropped images are shown in Author response image 1 and 2.

Author response image 1.

Raw image of Figure 4B

Author response image 2.

Raw image of Figure 5B

5) Figure: 5. A. - I see non-specific amplifications in the gel images. Are these blotting images? or the gel images that were changed to "Grayscale"? Non-specific amplification may imply that the experiment was not repeated and standardized. Was it gel images or blot images?

We appreciate your insightful comment. The images in Figure 5A represent western blot bands from co-immunoprecipitation assay for analysis of the interaction between TXNIP and HDAC2 proteins. Since immunoblotting using immunoprecipitates can usually detect some non-specific bands from heavy (~ 50 kDa) and light (~25 kDa) chains of the target antibody or from multiple co-immunoprecipitated proteins, we assume that the vague non-specific bands in Figure 5A might be a heavy chain of TXNIP or HDAC2 antibody or an unclear non-specific band. Because target bands showed strong intensity and very clear pattern compared to the non-specific bands in the co-immunoprecipitation assay, we believe that this data is sufficient to support the interaction of TXNIP with HDAC2. Finally, In the revised Figure 5A, we’ve modified the labeling for different experimental conditions, namely siCon and siTXNIP treatments, and added expected size of proteins (kDa), as shown below.

6) Figure 5. A. RT-PCR analysis: What was your expected size of the amplifications? the ladder indicated is in KDa. Is that right?

We appreciate your insightful questions. As mentioned above, Figure 5A shows the blotting images of co-immunoprecipitation analysis, and the ladder indicates the molecular weight (kDa) of protein markers. For clearer interpretation, the expected size of target proteins has been added in Figure 5A in the revised manuscript.

7) How were the band intensities determined?

Thank you for your question. For quantification of immunoblot results, the densities of target protein bands were analyzed with Image J, as we described in the Materials and Methods.

Discussion:

The authors have utilized and discussed the conclusion they draw from their study. But could highlight more on ARRDCs and why it was selected out of the other arrestins. The authors have provided future work directions associated with their work.

8) Why were only ARRDCs presented amongst all the arrestin in the main part of the manuscript?

We’re grateful for your valuable feedback. The reason we focused on α-arrestins was that α-arrestins have been discovered relatively recently, especially when compared to more established visual/ β-arrestin proteins in the same arrestin family but the biological functions of many α-arrestins remain largely unexplored, with notable exceptions in the budding yeast model and a few α-arrestins in mammals and invertebrate species. Most importantly, comparative study highlighting the shared or unique features of α-arrestins is yet to be undertaken. To gain a more comprehensive understanding of these unexplored α-arrestins across multiple species, we’ve centered our research on the ARRDCs within the arrestin protein family.

On page 21 lines 8-17, we’ve edited the manuscript to emphasize the importance of a comparative study on α-arrestins, as detailed below.

“According to a phylogenetic analysis of arrestin family proteins, α-arrestins were shown to be ubiquitously conserved from yeast to human (Alvarez, 2008). However, compared to the more established visual/ β-arrestin proteins, α-arrestins have been discovered more recently and much of their molecular mechanisms and functions remain mostly unexplored except for budding yeast model (Zbieralski & Wawrzycka, 2022). Based on the high-confidence interactomes of α-arrestins from human and Drosophila, we identified conserved and specific functions of these α-arrestins. Furthermore, we uncovered molecular functions of newly discovered function of human specific α-arrestins, TXNIP and ARRDC5. We anticipate that the discovery made here will enhance current understanding of α-arrestins.”

9) The discussion could be elaborated more by utilizing the data.

We appreciate your insightful feedback. Based on the reviewer’s suggestion, we’ve enhanced the discussion in the manuscript to provide a clearer interpretation of our results. First, we’ve added description of conserved protein complexes significantly associated with α-arrestins, stated on page 22 lines 5-12 and lines 23-26.

Page 22 lines 5-12: “The integrative map of protein complexes also highlighted both conserved and unique relationships between α-arrestins and diverse functional protein complexes. For instance, protein complexes involved in ubiquitination-dependent proteolysis, proteasome, RNA splicing, and intracellular transport (motor proteins) were prevalently linked with α-arrestins in both human and Drosophila. To more precisely identify conserved PPIs associated with α-arrestins, we undertook ortholog predictions within the α-arrestins’ interactomes. This revealed 58 orthologous interaction groups that were observed to be conserved between human and Drosophila (Figure 3).”

Page 22 lines 23-26: “Additionally, interaction between α-arrestins and entities like motor proteins, small GTPase, ATP binding proteins, and endosomal trafficking components were identified to be conserved. Further validation of these interactions could unveil molecular mechanisms consistently associated with these cellular functions.”

Secondly, we’ve added description of role of ARRDC5 in osteoclast maturation, as stated on page 23 lines 22-24.

“Conversely, depletion of ARRDC5 reduces osteoclast maturation, underscoring the pivotal role of ARRDC5 in osteoclast development and function (Figure S9A and B).”

Lastly, we examined the association between α-arrestins’ interactomes and human diseases, incorporating our findings into the discussion. The newly introduced figure based on the result is Figure S10.

On page 24 lines 10-14, we’ve added discussion on Figure S10 as follows.

“We further explored association between α-arrestins’ interactomes and disease pathways (Figure S10). Notably, the interactomes of α-arrestins in human showed clear links to specific diseases. For instance, ARRDC5 is closely associated with disease resulting from viral infection and cardiovascular conditions. ARRDC2, ARRDC4, and TXNIP share common association with certain neurodegenerative diseases, while ARRDC1 is implicated in cancer.”

Supplementary figures:

The authors have a rigorous amount of work added together for the success of this manuscript.

10) The reference section needs editing before publication. Maybe the arrangement was disturbed during compiling.

Thank you for your valuable comment. Based on the reviewer’s suggestion, we have rearranged the reference section to enhance its clarity. Below are excerpts from the update reference section in the manuscript.

“Adenuga, D., & Rahman, I. (2010). Protein kinase CK2-mediated phosphorylation of HDAC2 regulates co-repressor formation, deacetylase activity and acetylation of HDAC2 by cigarette smoke and aldehydes. Arch Biochem Biophys, 498(1), 62-73. doi:10.1016/j.abb.2010.04.002

Adenuga, D., Yao, H., March, T. H., Seagrave, J., & Rahman, I. (2009). Histone Deacetylase 2 Is Phosphorylated, Ubiquitinated, and Degraded by Cigarette Smoke. American Journal of Respiratory Cell and Molecular Biology, 40(4), 464-473. doi:10.1165/rcmb.2008-0255OC

Akalin, A., Franke, V., Vlahovicek, K., Mason, C. E., & Schubeler, D. (2015). Genomation: a toolkit to summarize, annotate and visualize genomic intervals. Bioinformatics, 31(7), 1127-1129. doi:10.1093/bioinformatics/btu775

Alvarez, C. E. (2008). On the origins of arrestin and rhodopsin. BMC Evol Biol, 8, 222. doi:10.1186/1471-2148-8-222”

11) many important references were missing.

We appreciate and agree with the reviewer’s comment. In response to the reviewer’s recommendation, we’ve thoroughly reviewed the manuscript and below are sections of the manuscript where around 20 new references have been added.

On page 8 lines 12-14:

“Utilizing the known affinities between short linear motifs in α-arrestins and protein domains in interactomes(El-Gebali et al., 2019; UniProt Consortium, 2018) “

On page 8 lines 19-22:

“One of the most well-known short-linear motifs in α-arrestin is PPxY, which is reported to bind with high affinity to the WW domain found in various proteins, including ubiquitin ligases (Ingham, Gish, & Pawson, 2004; Macias et al., 1996; Sudol, Chen, Bougeret, Einbond, & Bork, 1995)”

On page 9 lines 3-6:

“Next, we conducted enrichment analyses of Pfam proteins domains (El-Gebali et al., 2019; Huang da, Sherman, & Lempicki, 2009b) among interactome of each α-arrestin to investigate known and novel protein domains commonly or specifically associated (Figure S3A; Table S5).”

On page 9 lines 7-10:

“HECT and C2 domains are well known to be embedded in the E3 ubiquitin ligases such as NEDD4, HECW2, and ITCH along with WW domains (Ingham et al., 2004; Melino et al., 2008; Rotin & Kumar, 2009; Scheffner, Nuber, & Huibregtse, 1995; Weber, Polo, & Maspero, 2019)”

On page 10 lines 12-16:

“In fact, the known binding partners, NEDD4, WWP2, WWP1, and ITCH in human and CG42797, Su(dx), Nedd4, Yki, Smurf, and HERC2 in Drosophila, that were detected in our data are related to ubiquitin ligases and protein degradation (C. Chen & Matesic, 2007; Ingham et al., 2004; Y. Kwon et al., 2013; Marin, 2010; Melino et al., 2008; Rotin & Kumar, 2009) (Figure 1E; Figure S2F).”

On page 13 lines 20-21:

“Given that α-arrestins are widely conserved in metazoans (Alvarez, 2008; DeWire, Ahn, Lefkowitz, & Shenoy, 2007), “

On page 14 lines 12-17:

“The most prominent functional modules shared across both species were the ubiquitin-dependent proteolysis, endosomal trafficking, and small GTPase binding modules, which are in agreement with the well-described functions of α-arrestins in membrane receptor degradation through ubiquitination and vesicle trafficking (Dores et al., 2015; S. O. Han et al., 2013; Y. Kwon et al., 2013; Nabhan et al., 2012; Puca & Brou, 2014; Puca et al., 2013; Shea et al., 2012; Xiao et al., 2018; Zbieralski & Wawrzycka, 2022) (Figure 3).”  

Reviewer #2

In this manuscript, the authors present a novel interactome focused on human and fly alpha-arrestin family proteins and demonstrate its application in understanding the functions of these proteins. Initially, the authors employed AP/MS analysis, a popular method for mapping protein-protein interactions (PPIs) by isolating protein complexes. Through rigorous statistical and manual quality control procedures, they established two robust interactomes, consisting of 6 baits and 307 prey proteins for humans, and 12 baits and 467 prey proteins for flies. To gain insights into the gene function, the authors investigated the interactors of alpha-arrestin proteins through various functional analyses, such as gene set enrichment. Furthermore, by comparing the interactors between humans and flies, the authors described both conserved and species-specific functions of the alpha-arrestin proteins. To validate their findings, the authors performed several experimental validations for TXNIP and ARRDC5 using ATAC-seq, siRNA knockdown, and tissue staining assays. The experimental results strongly support the predicted functions of the alpha-arrestin proteins and underscore their importance. `

I would like to suggest the following analyses to further enhance the study:

1) It would be valuable if the authors could present a side-by-side comparison of the interactomes of alpha-arrestin proteins, both before and after this study. This visual summary network would demonstrate the extent to which this work expanded the existing interactome, emphasizing the overall contribution of this study to the investigation of the alpha-arrestin protein family.

We greatly appreciate your insightful feedback. In response to the reviewer’s suggestion, we’ve depicted a network of known PPIs associated with α-arrestins (Figure S2C and D). Furthermore, by comparing our high-confidence PPIs to these known sets, we found that the overlaps are statistically significant and the high-confidence PPIs of α-arrestins broaden the existing interactome (Figure S2E).

From page 7 line 26 to page 8 line 8, we’ve detailed this side-by-side comparisons of existing interactome and newly discovered high-confidence PPIs of α-arrestins, as outline below.

“As a result, we successfully identified many known interaction partners of α-arrestins such as NEDD4, WWP2, WWP1, ITCH and TSG101, previously documented in both literatures and PPI databases (Figure S2C-F) (Colland et al., 2004; Dotimas et al., 2016; Draheim et al., 2010; Mellacheruvu et al., 2013; Nabhan et al., 2012; Nishinaka et al., 2004; Puca & Brou, 2014; Szklarczyk et al., 2015; Warde-Farley et al., 2010; Wu et al., 2013). Additionally, we greatly expanded repertoire of PPIs associated with α-arrestins in human and Drosophila, resulting in 390 PPIs between six α-arrestins and 307 prey proteins in human, and 740 PPIs between twelve α-arrestins and 467 prey proteins in Drosophila (Figure S2E). These are subsequently referred to as ‘high-confidence PPIs’ (Table S3).”

2) While the authors conducted several analyses exploring protein function, there is a need to further explore the implications of the interactome in human diseases. For instance, it would be beneficial to investigate the association of the newly identified interactome members with specific human diseases. Including such investigations would strengthen the link between the interactome and human disease contexts.

Thank you for your valuable comment. As suggested by the reviewer, we examined the association between α-arrestins’ interactomes and human diseases, incorporating our findings into the discussion. The newly introduced figure based on the result is Figure S10.

On page 24 lines 10-14, we’ve added discussion on Figure S10 as follows.

“We further explored association between α-arrestins’ interactomes and disease pathways (Figure S10). Notably, the interactomes of α-arrestins in human showed clear links to specific diseases. For instance, ARRDC5 is closely associated with disease resulting from viral infection and cardiovascular conditions. ARRDC2, ARRDC4, and TXNIP share common association with certain neurodegenerative diseases, while ARRDC1 is implicated in cancer.”

Reviewer #3:

Lee, Kyungtae and colleagues have discovered and mapped out alpha-arrestin interactomes in both human and Drosophila through the affinity purification/mass spectrometry and the SAINTexpress method. They found the high confident interactomes, consisting of 390 protein-protein interactions (PPIs) between six human alpha-arrestins and 307 preproteins, as well as 740 PPIs between twelve Drosophila alpha-arrestins and 467 prey proteins. To define and characterize these identified alpha-arrestin interactomes, the team employed a variety of widely recognized bioinformatics tools. These included protein domain enrichment analysis, PANTHER for protein class enrichment, DAVID for subcellular localization analysis, COMPLEAT for the identification of functional complexes, and DIOPT to identify evolutionary conserved interactomes. Through these analyses, they confirmed known alpha-arrestin interactors' role and associated functions such as ubiquitin ligase and protease. Furthermore, they found unexpected biological functions in the newly discovered interactomes, including RNA splicing and helicase, GTPase-activating proteins, ATP synthase. The authors carried out further study into the role of human TXNIP in transcription and epigenetic regulation, as well as the role of ARRDC5 in osteoclast differentiation. This study holds important value as the newly identified alpha-arrestin interactomes are likely aiding functional studies of this group of proteins. Despite the overall support from data for the paper's conclusions, certain elements related to data quantification, interpretation, and presentation demand more detailed explanation and clarification.

1) In Figure 1B, it is shown that human alpha-arrestins were N-GFP tagged (N-terminal) and Drosophila alpha-arrestins were C-GFP (C-terminal). However, the rationale of why the authors used different tags for human and fly proteins was not explained in the main text and methods.

We appreciate your valuable comment. Both N- and C-terminally tagged α-arrestins have been used previously. Given that our study aims to increase the repertoire of α-arrestin interacting proteins, where GFP is added might not be a concern. We note that GFP is a relatively bulky tag, and tagging a protein with GFP can potentially abolish the interaction with some of the binding proteins. Follow-up studies utilizing different approaches for detecting protein-protein interactions, such as BioID and yeast two-hybrid, will allow us to build more comprehensive α-arrestin interactomes.

2) In Figure 2A, there seems to be an error for labeling the GAL4p/GAL80p complex that includes NOTCH2, NOTCH1 and TSC2.

Thank you for comment. We double-checked COMPLEAT (protein COMPLex Enrichment Analysis Tool) database for the name of protein complex consisting of NOTCH1, NOTCH2, AND TSC2. The database indeed labeled this complex as the “GAL4p/GAL80p complex”. However, given the potential for mis-annotation (since we could not ascertain the relevance of these proteins to the “GAL4p/GAL80p complex”), we chose to exclude this protein complex from the network. The update protein complex network is illustrated in the revised Figure 2A.

3) In Figure 5, given that knockdown of TXNIP did not affect the levels and nuclear localization of HDAC2, the authors suggest that TXNIP might modulate HDAC2 activity. However, the ChiP assay suggest a different model - TXNIP-HDAC2 interaction might inhibit the chromatin occupancy of HDAC2, reducing histone deacetylation and increasing global chromatin accessibly. The authors need to propose a model consistent with these sets of all data.

We greatly appreciate your detailed feedback. Our data indicates a global decrease in chromatin accessibility (Figure 4C-G) and a diminished interaction between TXNIP and HDAC2 under depletion of TXNIP (Figure 5A). Additionally, we observed an increased occupancy of HDAC2 and subsequent histone deacetylation at TXNIP-target promoter regions (Figure 5C) without any changes in the HDAC2 expression level (Figure 5A) in TXNIP- knockdown cells. From these observations, we infer that the interaction between TXNIP-HDAC2 might suppress the function of HDAC2, a major gene silencer affecting the formation of condensed or accessible chromatin by deacetylating activity. Although we checked whether TXNIP could induce cytosolic retention of HDAC2 to inhibit nuclear function of HDAC2, TNXIP knockdown did not alter its subcellular localization (Figure 5B).

To elucidate the mechanism by which TXNIP inhibits the function of HDAC2, we further investigated the effect of TXNIP on the levels of HDAC2 phosphorylation, which is known to be crucial for its deacetylase activity and the formation of transcriptional repressive complex. However, as shown in the Figure S8C and D, the knockdown of TXNIP did not affect the HDAC2 phosphorylation status, as well as the interaction between HDAC2 and other components in NuRD complex in the immunoblotting and co-IP assays, respectively. The results suggest that TXNIP may inhibit the function of HDAC2 independently of these factors.

Following the reviewer’s suggestion, we carefully provided a proposed model describing the possible role of TXNIP in transcriptional regulation through interaction with HDAC2 and co-repressor complex in Figure S8E.

Description of these newly added figures can be found in the revised manuscript from page 18 line 7 to 27, as outlined below.

“HDAC2 typically operates within the mammalian nucleus as part of co-repressor complexes as it lacks ability to bind to DNA directly (Hassig, Fleischer, Billin, Schreiber, & Ayer, 1997). The nucleosome remodeling and deacetylation (NuRD) complex is one of the well-recognized co-repressor complexes that contains HDAC2 (Kelly & Cowley, 2013; Seto & Yoshida, 2014) and we sought to determine if depletion of TXNIP affects interaction between HDAC2 and other components in this NuRD complex. While HDAC2 interacted with MBD3 and MTA1 under normal condition, the interaction between HDAC2 and MBD3 or MTA1 was not affected upon TXNIP depletion (Figure S8C). Next, given that HDAC2 phosphorylation is known to influence its enzymatic activity and stability (Adenuga & Rahman, 2010; Adenuga, Yao, March, Seagrave, & Rahman, 2009; Bahl & Seto, 2021; Tsai & Seto, 2002), we tested if TXNIP depletion alters phosphorylation status of HDAC2. The result indicated, however, that phosphorylation status of HDAC2 does not change upon TXNIP depletion (Figure S8D). In summary, our findings suggest a model where TXNIP plays a role in transcriptional regulation independent of these factors (Figure S8E). When TXNIP is present, it directly interacts with HDAC2, a key component of transcriptional co-repressor complex. This interaction suppresses the HDAC2 ‘s recruitment to target genomic regions, leading to the histone acetylation of target loci possibly through active complex including histone acetyltransferase (HAT). As a result, transcriptional activation of target gene occurs. In contrast, when TXNIP expression is diminished, the interaction between TXNIP and HDAC2 weakens. This restores histone deacetylating activity of HDAC2 in the co-repressor complex, leading to subsequent repression of target gene transcription.”

4) The authors showed that ectopic expression of ARRDC5 increased osteoclast differentiation and function. Does loss of ARDDC5 lead to defects in osteoclast function and fate determination?

We appreciate your valuable comment. We have confirmed the endogenous expression of ARRDC5 in osteoclasts and conducted a loss-of-function study using shARRDC5. As determined by qPCR, ARRDC5 was endogenously expressed very low in osteoclasts. Even during RANKL-induced osteoclast differentiation, the CT value (29-31) for ARRDC5 expression was high in osteoclasts compared to the CT value (17-24) for the expression of marker genes Cathepsin K, TRAP, and NFATc1. Even though its endogenous expression was very low, we generated ARRDC5 knockdown cells by infecting BMMs with lentivirus expressing shRNA of ARRDC5 and subsequently differentiated the cells into mature osteoclasts. After five days of differentiation, we observed a significant decrease in the total number of TRAP-positive multinucleated cells (No. of TRAP+ MNCs) in shARRDC5 cells compared to that in the control cells. This result indicates that the loss of ARRDC5 leads to defects in osteoclast differentiation. Result of this loss-of-function study using shARRDC5 is depicted in Figure S9A and B.

In the revised manuscript, following sentence explaining Figure S9A and B was added on page 19 lines 15-17 as follows.

“Depletion of ARRDC5 using short hairpin RNA (shRNA) impaired osteoclast differentiation, further affirming its crucial role in this differentiation process (Figure S9A and B).”

5) From Figure 6D, the authors argued that ARRDC5 overexpression resulted in more V-ATPase signals: however, there is no quantification. Quantification of the confocal images will foster the conclusion. Also, western blots for V-ATPase proteins will provide an alternative way to determine the effects of ARRDC5.

We appreciate your insightful feedback. As suggested by the reviewer, we quantified V-type ATPase signals using confocal images, which were shown in Figure 6D. The ImageJ program was employed for integrated density measurements, and the integrated density of GFP-GFP overexpressing osteoclasts was set to 1 for relative comparison. The result in the revised Figure 6D revealed a significant increase in V-type ATPase signals in GFP-ARRDC5 overexpressing osteoclasts compared to that in GFP-GFP overexpressing osteoclasts, as outlined below.

We also agree with the reviewer’s comment that Western blot for V-ATPase proteins will be an alternative way to determine the effects of ARRDC5 in osteoclast differentiation. We have confirmed no different expression of V-type ATPase between GFP-GFP and GFP-ARRDC5 overexpressing osteoclasts using qPCR and western blot analysis. The corresponding western blot result is shown in the revised Figure S9C.

In addition, the corresponding qPCR that measures the expression level of V-type ATPase between GFP-GFP and GFP-ARRDC5 overexpressing osteoclasts is shown in Author response image 3.

Author response image 3.

Moreover, based on the references, the V-type ATPase is localized at the plasma membrane during osteoclast differentiation (Toyomura et al., 2003). Although mRNA and protein expression levels were similar in both cells, localization of V-ATPase in plasma membrane was significantly increased in GFP-ARRDC5 overexpressing osteoclasts compared to that in GFP-GFP osteoclasts, as shown in the revised Figure 6D above.

6) The results from Figure 6D did not support the authors' argument that ARRDC5 might control the membrane localization of the V-ATPase, as bafilomycin is the V-ATPase inhibitor. ARRDC5 knockdown experiments will help to determine whether ARRDC5 can control the membrane localization of the V-ATPase in osteoclast.

Thank you for your insightful comment. V-type ATPase has been reported to play an important role in the differentiation and function of osteoclasts (Feng et al., 2009; Qin et al., 2012). Given that various subunits of the V-type ATPase interact with ARRDC5 (Figure 6A), we speculated that ARRDC5 might be involved in the function of this complex and play a role in osteoclast differentiation and function. As answered above, GFP-ARRDC5 overexpressing osteoclasts showed a similar expression level of V-type ATPase to GFP-GFP cells but exhibited increased V-type ATPase signals at the cell membrane compared to those in GFP-GFP cells (Figure 6D). Additionally, co-localization of ARRDC5 and V-type ATPase was observed in the osteoclast membrane (Figure 6D), as predicted by the human ARRDC5-centric PPI network. On the other side, bafilomycin A1, a V-type ATPase inhibitor, not only blocked localization of V-type ATPase to plasma membrane in GFP-ARRDC5 overexpressing osteoclasts, but also reduced ARRDC5 signals (Figure 6D). These results indicate that ARRDC5 plays a role in osteoclast differentiation and function by interacting with V-type ATPase and promoting the localization of V-type ATPase to plasma membrane in osteoclasts.

V-type ATPase present in osteoclast membrane is important to cell fusion, maturation, and function during osteoclast differentiation (Feng et al., 2009; Qin et al., 2012). GFP-ARRDC5 overexpressing osteoclasts showed a significant increase of V-type ATPase signals in the cell membrane compared to GFP-GFP cells (Figure 6D), and also significantly increased cell fusion (No. of TRAP+ MNCs in Figure 6B) and resorption activity (resorption pit formation in Figure 6C). However, ARRDC5 knockdown in osteoclasts (shARRDC5 cells) showed a significant decrease in No. of TRAP+ MNCs compared to that in the control cells, indicating that the loss of ARRDC5 leads to defects in cell fusion during osteoclast differentiation (Figure S9A and B). As described above, the endogenous expression of ARRDC5 was very low in osteoclasts and could be specifically expressed in a certain timepoint during the differentiation. Therefore, to better understand the interaction with V-type ATPase of ARRDC5 in osteoclasts, ARRDC5 overexpression is more suitable than its knockdown.

Part of the manuscript on page 19 line 21 to page 20 line 6 was edited to support our statement, as outlined below.

“The V-type ATPase is localized at the osteoclast plasma membrane (Toyomura et al., 2003) and its localization is important for cell fusion, maturation, and function during osteoclast differentiation (Feng et al., 2009; Qin et al., 2012). Furthermore, its localization is disrupted by bafilomycin A1, which is shown to attenuate the transport of the V-type ATPase to the membrane (Matsumoto & Nakanishi-Matsui, 2019). We analyzed changes in the expression level and localization of V-type ATPase, especially V-type ATPase V1 domain subunit (ATP6V1), in GFP-GFP and GFP-ARRDC5 overexpressing osteoclasts. The level of V-type ATPase expression did not change in osteoclasts regardless of ARRDC5 expression levels (Figure S9C). GFP signals were detected at the cell membrane when GFP-ARRDC5 was overexpressed, indicating that ARRDC5 might also localize to the osteoclast plasma membrane (Figure 6D; Figure S9D). In addition, we detected more V-type ATPase signals at the cell membrane in the GFP-ARRDC5 overexpressing osteoclasts, and ARRDC5 and V-type ATPase were co-localized at the osteoclast membrane (Figure 6D; Figure S9D).”

7) The tables (excel files) do not have proper names for each table S numbers. Please correct the name of excel files for readers.

We appreciate your valuable comments. In response to the reviewer’s suggestion, we’ve renamed excel files to more appropriate titles for easier readability. List of renamed tables (excel files) are shown below.

Table S1. List of α-arrestins from human and Drosophila Table S2. Evaluation sets of α-arrestins PPIs Table S3. Summary tables of SAINTexpress results Table S4. Protein domains and short linear motifs in the α-arrestin interactomes Table S5. Enriched Pfam domains in the α-arrestin interactomes Table S6. Subcellular localizations of α-arrestin interactomes Table S7. Summary of protein complexes and cellular components associated with α-arrestin Table S8. Orthologous relationship of α-arrestin interactomes between human and Drosophila Table S9. Summary of ATAC- and RNA-seq read counts before and after processing Table S10. Differential accessibility of ACRs and gene expression Table S11. Summary of ATAC-seq peaks located in promoters and gene expression level Table S12. List of primer sequences used in this study

8) http://big.hanyang.ac.kr/alphaArrestin_Fly link does not work. Please fix the link.

We appreciate your comment. In response to the reviewer’s comment, we have made comprehensive α-arrestin interactome maps on our new website (big.hanyang.ac.kr/alphaArrestin_PPIN) and confirmed that users can be re-directed to networks housed in NDEx.

Author response image 4.

Screen shot of the first page of the newly developed website.

Website address: big.hanyang.ac.kr/‌‌‌‌‌‍‍‍‌‌alphaArrestin_PPIN

Author response image 5.

Screen shot of the gene-gene network involving α-arrestin in human.

Author response:

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

eLife assessment

This useful study describes an antibody-free method to map G-quadruplexes (G4s) in vertebrate cells. While the method might have potential, the current analysis is primarily descriptive and does not add substantial new insights beyond existing data (e.g., PMID:34792172). While the datasets provided might constitute a good starting point for future functional studies, additional data and analyses would be needed to fully support the major conclusions and, at the same time, clarify the advantage of this method over other methods. Specifically, the strength of the evidence for DHX9 interfering with the ability of mESCs to differentiate by regulating directly the stability of either G4s or R-loops is still incomplete.

We thank the editors for their helpful comments.

Given that antibody-based methods have been reported to leave open the possibility of recognizing partially folded G4s and promoting their folding, we have employed the peroxidase activity of the G4-hemin complex to develop a new method for capturing endogenous G4s that significantly reduces the risk of capturing partially folded G4s. We have included a new Fig. 9 and a new section “Comparisons of HepG4-seq and HBD-seq with previous methods” to carefully compare our methods to other methods.

In the Fig. 7, we applied the Dhx9 CUT&Tag assay to identify the G4s and R-loops directly bound by Dhx9 and further characterized the differential Dhx9-bound G4s and R-loops in the absence of Dhx9. Dhx9 is a versatile helicase capable of directly resolving R-loops and G4s or promoting R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). Furthermore, we showed that depletion of Dhx9 significantly altered the levels of G4s or R-loops around the TSS or gene bodies of several key regulators of mESC and embryonic development, such as Nanog, Lin28a, Bmp4, Wnt8a, Gata2, and Lef1, and also their RNA levels (Fig.7 I). The above evidence is sufficient to support the transcriptional regulation of mESCs cell fate by directly modulating the G4s or R-loops within the key regulators of mESCs.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Non-B DNA structures such as G4s and R-loops have the potential to impact genome stability, gene transcription, and cell differentiation. This study investigates the distribution of G4s and R-loops in human and mouse cells using some interesting technical modifications of existing Tn5-based approaches. This work confirms that the helicase DHX9 could regulate the formation and/or stability of both structures in mouse embryonic stem cells (mESCs). It also provides evidence that the lack of DHX9 in mESCs interferes with their ability to differentiate.

Strengths:

HepG4-seq, the new antibody-free strategy to map G4s based on the ability of Hemin to act as a peroxidase when complexed to G4s, is interesting. This study also provides more evidence that the distribution pattern of G4s and R-loops might vary substantially from one cell type to another.

We appreciate your valuable points.

Weaknesses:

This study is essentially descriptive and does not provide conclusive evidence that lack of DHX9 does interfere with the ability of mESCs to differentiate by regulating directly the stability of either G4 or R-loops. In the end, it does not substantially improve our understanding of DHX9's mode of action.

In this study, we aimed to report new methods for capturing endogenous G4s and R-loops in living cells. Dhx9 has been reported to directly unwind R-loops and G4s or promote R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). To understand the direct Dhx9-bound G4s and R-loops, we performed the Dhx9 CUT&Tag assay and analyzed the co-localization of Dhx9-binding sites and G4s or R-loops. We found that 47,857 co-localized G4s and R-loops are directly bound by Dhx9 in the wild-type mESCs and 4,060 of them display significantly differential signals in absence of Dhx9, suggesting that redundant regulators exist as well. We showed that depletion of Dhx9 significantly altered the RNA levels of several key regulators of mESC and embryonic development, such as Nanog, Lin28a, Bmp4, Wnt8a, Gata2, and Lef1, which coincides with the significantly differential levels of G4s or R-loops around the TSS or gene bodies of these genes (Fig.7). The comprehensive molecular mechanism of Dhx9 action is indeed not the focus of this study. We will work on it in the future studies. Thank you for the comments.

There is no in-depth comparison of the newly generated data with existing datasets and no rigorous control was presented to test the specificity of the hemin-G4 interaction (a lot of the hemin-dependent signal seems to occur in the cytoplasm, which is unexpected).

The specificity of hemin-G4-induced peroxidase activity and self-biotinylation has been well demonstrated in previous studies (PMID: 19618960, 22106035, 28973477, 32329781). In the Fig.1A, we compared the hemin-G4-induced biotinylation levels in different conditions. Cells treated with hemin and Bio-An exhibited a robust fluorescence signal, while the absence of either hemin or Bio-An almost completely abolished the biotinylation signals, suggesting a specific and active biotinylation activity. To identify the specific signals, we have included the non-label control and used this control to call confident HepG4 peaks in all HepG4-seq assays.

The hemin-RNA G4 complex has also been reported to have mimic peroxidase activity and trigger similar self-biotinylation signals as DNA G4s (PMID: 32329781, 31257395, 27422869). Therefore, it is not surprising to observe hemin-dependent signals in the cytoplasm generated by cytoplasmic RNA G4s.

In the revised version, we have included a new Fig. 9 and a new section “Comparisons of HepG4-seq and HBD-seq with previous methods” to carefully compare our methods to other methods.

The authors talk about co-occurrence between G4 and R-loops but their data does not actually demonstrate co-occurrence in time. If the same loci could form alternatively either R-loops or G4 and if DHX9 was somehow involved in determining the balance between G4s and R-loops, the authors would probably obtain the same distribution pattern. To manipulate R-loop levels in vivo and test how this affects HEPG4-seq signals would have been helpful.

Single-molecule fluorescence studies have shown the existence of a positive feedback mechanism of G4 and R-loop formation during transcription (PMID: 32810236, 32636376), suggesting that G4s and Rloops could co-localize at the same molecule. Dhx9 is a versatile helicase capable of directly resolving R-loops and G4s or promoting R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). Although depletion of Dhx9 resulted in 6,171 Dhx9-bound co-localized G4s and R-loops with significantly altered levels of G4s or R-loops, only 276 of them (~4.5%) harbored altered G4s and R-loops, suggesting that the interacting G4s and R-loops are rare in living cells. Nowadays, the genome-wide co-occurrence of two factors are mainly obtained by bioinformatically intersection analysis. We agreed that F We will carefully discuss this point in the revised version. At the same time, we will make efforts to develop a new method to map the co-localized G4 and R-loop in the same molecule in the future study.

This study relies exclusively on Tn5-based mapping strategies. This is a problem as global changes in DNA accessibility might strongly skew the results. It is unclear at this stage whether the lack of DHX9, BLM, or WRN has an impact on DNA accessibility, which might underlie the differences that were observed. Moreover, Tn5 cleaves DNA at a nearby accessible site, which might be at an unknown distance away from the site of interest. The spatial accuracy of Tn5-based methods is therefore debatable, which is a problem when trying to demonstrate spatial co-occurrence. Alternative mapping methods would have been helpful.

In this study, we used the recombinant streptavidin monomer and anti-GP41 nanobody fusion protein (mSA-scFv) to specifically recognize hemin-G4-induced biotinylated G4 and then recruit the recombinant GP41-tagged Tn5 protein to these G4s sites. Similarly, the recombinant V5-tagged N-terminal hybrid-binding domain (HBD) of RNase H1 specifically recognizes R-loops and recruit the recombinant protein G-Tn5 (pG-Tn5) with the help of anti-V5 antibody. Therefore, the spatial distance of Tn5 to the target sites is well controlled and very short, and also the recruitment of Tn5 is specifically determined by the existence of G4s in HepG4-seq and R-loops in HBD-seq. In addition, RNase treatment markedly abolished the HBD-seq signals and the non-labeled controls exhibit obviously reduction of HepG4-seq signals, demonstrating that HBD-seq and HepG4-seq were not contamination from tagmentation of asccessible DNA.

Reviewer #2 (Public Review):

Summary:

In this study, Liu et al. explore the interplay between G-quadruplexes (G4s) and R-loops. The authors developed novel techniques, HepG4-seq and HBD-seq, to capture and map these nucleic acid structures genome-wide in human HEK293 cells and mouse embryonic stem cells (mESCs). They identified dynamic, cell-type-specific distributions of co-localized G4s and R-loops, which predominantly localize at active promoters and enhancers of transcriptionally active genes. Furthermore, they assessed the role of helicase Dhx9 in regulating these structures and their impact on gene expression and cellular functions.

The manuscript provides a detailed catalogue of the genome-wide distribution of G4s and R-loops. However, the conceptual advance and the physiological relevance of the findings are not obvious. Overall, the impact of the work on the field is limited to the utility of the presented methods and datasets.

Strengths:

(1) The development and optimization of HepG4-seq and HBD-seq offer novel methods to map native G4s and R-loops.

(2) The study provides extensive data on the distribution of G4s and R-loops, highlighting their co-localization in human and mouse cells.

(3) The study consolidates the role of Dhx9 in modulating these structures and explores its impact on mESC self-renewal and differentiation.

We appreciate your valuable points.

Weaknesses:

(1) The specificity of the biotinylation process and potential off-target effects are not addressed. The authors should provide more data to validate the specificity of the G4-hemin.

The specificity of hemin-G4-induced peroxidase activity and self-biotinylation has been well demonstrated in previous studies (PMID: 19618960, 22106035, 28973477, 32329781). In the Fig.1A, we compared the hemin-G4-induced biotinylation levels in different conditions. Cells treated with hemin and Bio-An exhibited a robust fluorescence signal, while the absence of either hemin or Bio-An almost completely abolished the biotinylation signals, suggesting a specific and active biotinylation activity.

(2) Other methods exploring a catalytic dead RNAseH or the HBD to pull down R-loops have been described before. The superior quality of the presented methods in comparison to existing ones is not established. A clear comparison with other methods (BG4 CUT&Tag-seq, DRIP-seq, R-CHIP, etc) should be provided.

Thank you for the suggestions. We have included a new Fig. 9 and a new section “Comparisons of HepG4-seq and HBD-seq with previous methods” to carefully compare our methods to other methods.

(3) Although the study demonstrates Dhx9's role in regulating co-localized G4s and R-loops, additional functional experiments (e.g., rescue experiments) are needed to confirm these findings.

Dhx9 has been demonstrate as a versatile helicase capable of directly resolving R-loops and G4s or promoting R-loop formation in previous studies (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). We believe that the current new dataset and previous studies are enough to support the capability of Dhx9 in regulating co-localized G4s and R-loops.

(4) The manuscript would benefit from a more detailed discussion of the broader implications of co-localized G4s and R-loops.

Thank you for the suggestions. We have included the discussion in the revised version.

(5) The manuscript lacks appropriate statistical analyses to support the major conclusions.

We apologized for this point. Whereas we have applied careful statistical analyses in this study, lacking of some statistical details make people hard to understand some conclusions. We have carefully added details of all statistical analysis.

(6) The discussion could be expanded to address potential limitations and alternative explanations for the results.

Thank you for the suggestions. We have included the discussion about this point in the revised version.

Reviewer #3 (Public Review):

Summary:

The authors developed and optimized the methods for detecting G4s and R-loops independent of BG4 and S9.6 antibody, and mapped genomic native G4s and R-loops by HepG4-seq and HBD-seq, revealing that co-localized G4s and R-loops participate in regulating transcription and affecting the self-renewal and differentiation capabilities of mESCs.

Strengths:

By utilizing the peroxidase activity of G4-hemin complex and combining proximity labeling technology, the authors developed HepG4-seq (high throughput sequencing of hemin-induced proximal labelled G4s), which can detect the dynamics of G4s in vivo. Meanwhile, the "GST-His6-2xHBD"-mediated CUT&Tag protocol (Wang et al., 2021) was optimized by replacing fusion protein and tag, the optimized HBD-seq avoids the generation of GST fusion protein aggregates and can reflect the genome-wide distribution of R-loops in vivo.

The authors employed HepG4-seq and HBD-seq to establish comprehensive maps of native co-localized G4s and R-loops in human HEK293 cells and mouse embryonic stem cells (mESCs). The data indicate that co-localized G4s and R-loops are dynamically altered in a cell type-dependent manner and are largely localized at active promoters and enhancers of transcriptionally active genes.

Combined with Dhx9 ChIP-seq and co-localized G4s and R-loops data in wild-type and dhx9KO mESCs, the authors confirm that the helicase Dhx9 is a direct and major regulator that regulates the formation and resolution of co-localized G4s and R-loops.

Depletion of Dhx9 impaired the self-renewal and differentiation capacities of mESCs by altering the transcription of co-localized G4s and R-loops-associated genes.

In conclusion, the authors provide an approach to studying the interplay between G4s and R-loops, shedding light on the important roles of co-localized G4s and R-loops in development and disease by regulating the transcription of related genes.

We appreciate your valuable points.

Weaknesses:

As we know, there are at least two structure data of S9.6 antibody very recently, and the questions about the specificity of the S9.6 antibody on RNA:DNA hybrids should be finished. The authors referred to (Hartono et al., 2018; Konig et al., 2017; Phillips et al., 2013) need to be updated, and the authors' bias against S9.6 antibodies needs also to be changed. However, as the authors had questioned the specificity of the S9.6 antibody, they should compare it in parallel with the data they have and the data generated by the widely used S9.6 antibody.

Thank you for the updating information about the structure data of S9.6 antibody. We politely disagree the specificity of the S9.6 antibody on RNA:DNA hybrids. The structural studies of S9.6 (PMID: 35347133, 35550870) used only one RNA:DNA hybrid to show the superior specificity of S9.6 on RNA:DNA hybrid than dsRNA and dsDNA. However, Fabian K. et al has reported that the binding affinities of S9.6 on RNA:DNA hybrid exhibits obvious sequence-dependent bias from null to nanomolar range (PMID: 28594954). We have included the comparison between S9.6-derived data and our HBD-seq data in the Fig.9 and the section “Comparisons of HepG4-seq and HBD-seq with previous methods”.

Although HepG4-seq is an effective G4s detection technique, and the authors have also verified its reliability to some extent, given the strong link between ROS homeostasis and G4s formation, and hemin's affinity for different types of G4s, whether HepG4-seq reflects the dynamics of G4s in vivo more accurately than existing detection techniques still needs to be more carefully corroborated.

Thank you for pointing out this issue. In the in vitro hemin-G4 induced self-biotinylation assay, parallel G4s exhibit higher peroxidase activities than anti-parallel G4s. Thus, the dynamics of G4 conformation could affect the HepG4-seq signals (PMID: 32329781). In the future, people may need to combine HepG4-seq and BG4s-eq to carefully explain the endogenous G4s. We have discussed this point in the revised version.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Figures 1A&1G. Although no merge images were provided, it seems that the biotin signals are strongly enriched outside the nucleus. This suggests that hemin is not specific for G4s in DNA. Does it mean that Hemin can also recognise G4 on RNAs? How do the authors understand the cytoplasmic signal?

Hemin indeed could interact with RNA G4 to obtain the peroxidase activity like DNA G4-hemin complex (PMID: 27422869, 32329781, 31257395). The cytoplasmic signals in Figure 1A&1G were derived from RNA G4.

Figure 1A: The fact that there is no Alexa647 signal without hemin or Bio-An does not actually demonstrate that the signals are specific. These controls do not actually test for the specificity of the G4-Hemin interaction.

The specificity of hemin-G4-induced peroxidase activity and self-biotinylation has been well demonstrated in previous studies (PMID: 19618960, 22106035, 28973477, 32329781). In this study, we performed the IF to confirm this phenomena.

Figure 1C: It looks like the HepG4-seq signals are simply an amplification of the noise given by the Tn5 (the non-label ctrl has the same pattern, albeit weaker). It is unclear why this happens but it might happen if somehow hemin increased the probability that the Tn5 is close to chromatin in an unspecific manner (it would cut G-rich, nucleosome-poor, accessible sites in an unspecific manner). To discard this possibility, it would be interesting to investigate directly which loci are biotinylated. For this, the authors could extract and sonicate the genomic DNA and use streptavidin to enrich for biotinylated fragments. Strand-specific DNA sequencing could then be used to map the biotinylated loci.

In the cell culture medium, there were a certain amount of hemin from serum and a low dosage of biotin from the basal medium DMEM, which could not be avoid. Thus, these contaminated hemin and biotin would generate the background signals observed in the Non-label control samples. The biotinylated sites were specifically recognized by the recombinant Streptavidin monomer which further recruits Tn5 to the biotinylated sites with the help of Moon-tag. Different from the signals in the HEK293 samples, a much more robust HepG4-seq signals were observed in the mESC samples and the signals were also abolished in the non-label control samples. Thus, the relatively small signal-to-noise ratio in the HEK293 samples suggest the week abundance of endogenous G4s in the HEK293 cells. Thus, we politely disagree that hemin increased the non-specific recruitment of Th5. In addition, the CUT&Tag technology has been wildly demonstrated to have a much lower background, high signal-to-noise ratio and high sensitivity. Thus, we also politely disagree to replace the CUT&Tag with the traditional DNA library preparation method.

Figure 1H: No spike-in was added and the data are not quantitative. The number of replicates is unclear. 70000 extra peaks (10x) after inhibition of BLM or WRN seems enormous. These extra peaks should be better characterised: do they contain G4 motifs? Are they transcribed? etc...; again what kind of controls should be used here, in case the inhibition of BLP and WRN has a global impact on chromatin accessibility?

To quantitatively compare different samples, we have normalized all samples according their de-duplicated uniquely mapping reads numbers. Given that the inhibitors were dissolved in the DMSO, we used the DMSO as the control. Since the Tn5 were specifically recruited the biotinylated G4 sites through the recombinant Streptavidin monomer protein and the moon tag system, the chromatin accessibility will not affect the Tn5, which were normally observed in the ATAT-seq.

As suggested, we have analyzed the enriched motifs of the extra peaks induced by BLM or WRN inhibition and showed that the top enriched motifs are also G-rich in the supplementary Fig.1E. In addition, we analyzed the RNA-seq levels of genes-associated with these extra peaks. As shown in the figure below, the majority of these genes are actively transcribed.

Author response image 1.

Figure 2: The mutated version of HBD should have been used as a control. As shown clearly in PMID: 37819055, the HBD domain does interact in an unspecific manner with chromatin at low levels. As above, this might be enough to increase the local concentration of the Tn5 close to chromatin in the Cut&Tag approach and to cleave accessible sites close to TSS in an unspecific manner.

As shown in Fig.2B and Fig.4A, we have included the RNase treatment as the control and showed that the HBD-seq-identified R-loops signals are dramatically attenuated (Fig.2B) or almost completely abolished after the RNase treatment (Fig.4A). These data demonstrate the specificity of HBD-seq.

Figure 2: What fraction of the HEPG4-seq signal is sensitive to RNase treatment? The authors used a combination of RNase A and RNase H but previous data have shown that the RNase A treatment is sufficient to remove the HBD-seq signal (which means that it is not actually possible on this sole basis to claim or disclaim that the signals do correspond to genuine R-loops). Do the authors have evidence that the RNase H treatment alone does impact their HBD-seq or HEPG4-seq signals?

As shown in Fig.2B and Fig.4A, the HBD-seq-identified R-loops signals are all dramatically attenuated (Fig.2B) or almost completely abolished after the RNase treatment (Fig.4A). The specificity of HBD on recognizing R-loops has been carefully demonstrated in the previous study (PMID: 33597247). In this study, we used the same two copies of HBD (2xHBD) and replaced the GST tag to EGFP-V5 to reduce the possibility of variable high molecular-weight aggregates caused by GST tag. In addition, RNase H treatment has been shown to fail to completely abolish the CUT&Tag signals since a subset of DNA-RNA hybrids with high GC skew are partially resistant to RNase H (PMID: 32544226, 33597247). In consideration of the high GC skew of co-localized G4s and R-loops, we combined the RNase A and RNase H. We currently did not have the RNaseH alone samples.

Figure 3A: "RNA-seq analysis revealed that the RNA levels of co-localized G4s and R-loops-associated genes are significantly higher": the differences are not very convincing.

In the Figure 3A, we have performed the Mann-Whitney test to examine the significance in the revised manuscript. RNA levels of co-localized G4s and R-loops-associated genes are indeed significantly higher than all genes, G4s or R-loops- associated genes with the Mann-Whitney test p < 2.2E-16.

Figure 3B: the patterns for "G4" and "co-localised G4 and R-loop" are extremely similar, suggesting that nearly all G4s mapped here could also form R-loops. If this is the case, most of the HEPG4-seq signals should be sensitive to exogenous RNase H treatment or to the in vivo over-expression of RNase H1. This should be tested (see above).

The percentage of co-localized G4 and R-loop in G4 peaks is 80.3% ( 5,459 out of 6,799) in HEK293 cells and 72.0% (68,482 out of 95,128) in mESC cells, respectively. The co-localization does not mean that G4 and R-loop interact with each other. We have showed that only small proportion of co-localized G4s and R-loops displayed differential G4s and R-loops at the same time in the dhx9KO mESCs (Fig. 6D, Supplementary Fig. 3B), suggesting that the majority of co-localized G4s and R-loops do not interact with each other. Thus, we thought that it is not necessary to perform the RNase H test.

Figure 3C: there is no correlation between the FC of G4 and the FC of RNA; this is not really consistent with the idea that the stabilisation of G4 is the driver rather than a consequence of the transcriptional changes.

Given that the treatment of WRN or BLM inhibition induced a large mount of G4 accumulation (Fig.1H-I), we examined the transcription effect on genes associated with these accumulated G4s in Fig.3C. We indeed observed the effect of G4 accumulation on transcription of G4-associated genes. Given that G4 stabilization triggers the transcriptional changes, it does not mean that the transcriptional changes should be highly correlated with the increase levels of G4s. To our knowledge, we have not observed this type of connections in the previous studies. 

l279: the overlap with H3K4me1 is really not convincing.

For all G4 peaks, the signals of H3K4me1 indeed exhibit a high background around the center of G4 peaks but we still could observe a clear peak in the center.

Figure 5C: it should be clearly indicated here that the authors compare Cut&Tag and ChIP data. The origin of the ChIP-seq data is also unclear and should be indicated.

Thank you for the suggestions. We have clarified this point.

For the ChIP data, we have described the origin of ChIP-seq data in the “Data availability” section as below: “The ChIP-seq data of histone markers and RNAP are openly available in GNomEx database (accession number 44R) (Wamstad et al., 2012).”

Reviewer #2 (Recommendations For The Authors):

(1) Figure 1A. An experimental condition lacking H2O2 (-H2O2) should be included.

We have added this control in Fig.1A

(2) Does RNAse H affect G4 profiles?

We have not tested the effect of RNase H on G4 forming. However, we have showed that only small proportion of co-localized G4s and R-loops displayed differential G4s and R-loops at the same time in the dhx9KO mESCs (Fig. 6D, Supplementary Fig. 3B), suggesting that the majority of co-localized G4s and R-loops do not interact with each other. Thus, we thought that it is not necessary to perform the RNase H test on G4. In addition, to treat cells wit RNase H, we have to permeabilize cells first to let RNase H enter the nuclei. If so, we will lose the pictures of endogenous G4s.

(3) Figure 2G. R-loops are detected upstream of the KPNB1 gene. What is this region? Is it transcribed?

We are so sorry to make a mistake when we prepared this figure. We have change it to the correct one in Fig. 2G. The R-loop is around the TSS of KPNB1. We also showed the RNA-seq data in this region in Author response image 2 below. This region is indeed transcribed.

Author response image 2.

(4) Did BLM and WRN inhibition specifically affect the expression of genes containing colocalized G4s and R-loops? Was the effect seen in other genes as well? Appropriate statistical analyses are needed.

In the Fig.3, we have shown that the accumulation of co-localized G4 and R-loops induced by the inhibition of BLM or WRN significantly caused the changes of genes (480 in BLM inhibition, 566 in WRN inhibition) containing these structures most of which are localized at the promoter-TSS regions. We indeed detected the effect in other genes as well. There were 918 and 1020 genes with significantly changes (padjust <0.05 & FC >=2 or FC <=0.5) in BLM and WRN inhibition, respectively.

(5) The claim that "The co-localized G4s and R-loops-mediated transcriptional regulation in HEK293 cells" (title of Figure 3) is not supported by the presented data. A causality link is not established in this study, which only reports correlations between G4s/R-loops and transcription regulation.

We politely disagree with this point. BLM and WRN are the best characterized DNA G4-resolving helicase ((Fry and Loeb, 1999; Mendoza et al., 2016; Mohaghegh et al., 2001). Here, we used the selective small molecules to specifically inhibit their ATPase activity and observed dramatical induction of G4 accumulation. Notably, the accumulated G4s that trigger the transcriptional changes are mainly located at the promoter-TSS region. If the transcriptional changes trigger the G4 accumulations, we should not observe such a biased distribution and more accumulated G4s should be detected in the gene body.

(6) The effect of Dhx9 KO on colocalized G4s/R-loops and transcription is not clear. The suggestion that Dhx9 could regulate transcription by modulating G4s, R-loops, and co-localized G4s and R-loops is not supported by the presented data. Additional experiments and statistical analyses are needed to conclude the role of Dhx9 on colocalized G4s/Rloops and transcription.

Dhx9 has been extensively studied and reported to directly unwind R-loops and G4s or promote R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). Thus, it is not necessary to repeat these assays again. To understand the direct Dhx9-bound G4s and R-loops, we performed the Dhx9 CUT&Tag assay and analyzed the co-localization of Dhx9-binding sites and G4s or R-loops. 47,857 co-localized G4s and R-loops are directly bound by Dhx9 in the wild-type mESCs and 4,060 of them display significantly differential signals in absence of Dhx9, suggesting that redundant regulators exist as well. These data have clearly shown the roles of Dhx9 directly modulating the stabilities of G4s and R-loops. Furthermore, we showed that loss of Dhx9 caused 816 Dhx9 directly bound colocalized G4 and R-loop associated genes significantly differentially expressed, supporting the transcriptional regulation of Dhx9. We performed the differential analysis following the standard pipeline: DESeq2 for RNA-seq and DiffBind for HepG4-seq and HBD-seq. The statistical details have been described in the figure legends.

(7) The conclusion that Dhx9 regulates the self-renewal and differentiation capacities of mESCs is vague. Additional experiments are needed to elucidate the exact contribution of Dhx9.

In this study, we aimed to report new methods for capturing endogenous G4s and R-loops in living cells. In this study, we have shown that depletion of Dhx9 significantly attenuated the proliferation of the mESCs and also influenced the capacity of mESCs differentiation into three germline lineages during the EB assay. In addition, we showed that depletion of Dhx9 significantly reduced the protein levels of mESCs pluripotent markers Nanog and Lin28a. The comprehensive molecular mechanism of Dhx9 action is indeed not the focus of this study. We will work on it in the future studies. Thank you for the comments.

Reviewer #3 (Recommendations For The Authors):

The study on the involvement of native co-localized G4s and R-loops in transcriptional regulation further enriches the readers' understanding of genomic regulatory networks, and the functional dissection of Dhx9 also lays a good foundation for the study of the dynamic regulatory mechanisms of co-localized G4s and R-loops. Unfortunately, however, the authors lack a strong basis for questioning the widely used BG4 and S9.6 antibodies, and the co-localized G4s and R-loops sequencing data obtained by the developed and optimized method also lack parallel comparison with existing sequencing technologies, which cannot indicate that HepG4-seq and HBD-seq are more reliable and superior than BG4 and S9.6 antibody-based sequencing technologies. There are also some minor errors in the manuscript that need to be corrected.

Thank you for the constructive comments. We have added a new section (Comparisons of HepG4-seq and HBD-seq with previous methods) and a new figure 9 to parallelly compare our methods to other widely-used methods.

(1) This work mainly focuses on co-localized G4s and R-loops, but in the introduction section, the interplay between G4s and R-loops is only briefly mentioned. It is suggested that the importance of the interplay of G4s and R-loops for gene regulation should be further expanded to help readers better understand the significance of studying co-localized G4s and R-loops.

Thank you for the comments. The current studies about the interplay between G4s and R-loops are limited. We have summarized all we could find in the literatures.

(2) The authors mentioned that "a steady state equilibrium is generally set at low levels in living cells under physiological conditions (Miglietta et al., 2020) and thus the addition of high-affinity antibodies may pull the equilibrium towards folded states", in my understanding this is one of the important reasons why the authors optimized the G4s and R-loops detection assays, I wonder if there is a reliable basis for this statement. If there is, I suggest that the authors can supplement it in the manuscript.

The main reason we develop the new method is to develop an antibody-free method to label the endogenous G4s in living cells. We ever tried to capture endogenous G4s using the tet-on controlled BG4. Unfortunately, we found that even a short time induction of BG4 in living cells was toxic. The traditional antibody-based methos rely on permeabilizing cells first to let the antibodies enter the nuclei. In this case, it is easy to lost the physiological pictures of endogenous G4s. We will add more discussion about this point. For R-loops, we just further optimized the GST-2xHBD-mediated method to avoid the problem of GST-tag. GST-fusion proteins are prone to form variable high molecular-weight aggregates and these aggregates often undermine the reliability of the fusion proteins.

(3) Some questions about HepG4-seq:

Is there a difference in hemin affinity for intramolecular G quadruplexes, interstrand G quadruplexes, and their different topologies? If so, does this bias affect the accuracy of sequencing results based on G4-hemin complexes?

Thank you for pointing out this issue. In the in vitro hemin-G4 induced self-biotinylation assay, parallel G4s exhibit higher peroxidase activities than anti-parallel G4s (PMID: 32329781). Thus, the dynamics of G4 conformation possibly affect the HepG4-seq signals. In the future, people may need to combine HepG4-seq and BG4s-eq to carefully explain the endogenous G4s. We have discussed this point in the revised version.

HepG4-seq is based on proximity labeling and peroxidase activity of the G4-hemin complex. The authors tested and confirmed that the addition of hemin and Bio-An in the experiment had no significant influences on sequencing results, but the effect of exogenous H2O2 treatment may also need to be taken into account since ROS can mediate the formation of G4s.

For HepG4-seq protocol, we only treat cells with H2O2 for one minute. Thus, we thought that the side effect of H2O2 treatment should be limited in such a short time.

(4) As we know, there have been at least two structure data of the S9.6 antibody very recently, and the questions about the specificity of the S9.6 antibody on RNA:DNA hybrids should be finished. The authors referred to (Hartono et al., 2018; Konig et al., 2017; Phillips et al., 2013) need to be updated, and the author's bias against S9.6 antibodies needs also to be changed. However, as the authors had questioned the specificity of the S9.6 antibody, they should compare in parallel with the data they have and the data generated by the widely used S9.6 antibody.

Thank you for the updating information about the structure data of S9.6 antibody. We politely disagree the specificity of the S9.6 antibody on RNA:DNA hybrids. The structural studies of S9.6 (PMID: 35347133, 35550870) used only one RNA:DNA hybrid to show the superior specificity of S9.6 on RNA:DNA hybrid than dsRNA and dsDNA. However, Fabian K. et al has reported that the binding affinities of S9.6 on RNA:DNA hybrid exhibits obvious sequence-dependent bias from null to nanomolar range (PMID: 28594954). We have included the comparison between S9.6-derived data and our HBD-seq data in the Fig.9 and the section “Comparisons of HepG4-seq and HBD-seq with previous methods”.

(5) It is hoped that the results of immunofluorescence experiments can be statistically analyzed.

We have performed the statistical analysis and included the data in the new figure.

(6) Some minor errors:

Line 168, "G4-froming" should be "G4-forming";

Figure 5E, the color of the "Repressed" average signal at the top of the HepG4-seq heatmap should be blue;

Figure 7C, the abbreviation "Gloop" should be indicated in the text or in the figure caption.

Thank you for pointing out these issues. We are sorry for these mistakes. We have corrected them in the revised version.

Author Response

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

Reviewer #1 (Recommendations For The Authors):

Some sentences need to be clarified and some additional data and references could be added.

1) Line 18

SRY is the sex-determining gene

SRY is the testis-determining gene is more accurate as described in line 44

Modification done

2) Line 50

Despite losing its function in early testis determination in mice, DMRT1 retained part of this function in adulthood when it is necessary to maintain Sertoli cell identity.

Losing its function is misleading. The authors describe firstly that Dmrt1 has no obvious function in embryonic testis development but is critical for the maintenance of Sertoli cells in adult mice. The wording "losing its function in early testis" is confusing. Do the authors mean that despite the expression of Dmrt1 in early testis development, the function of Dmrt1 seems to be restricted to adults in mice? A comparison between the testis and ovary should be more cautious since GarciaAlonso et al (2022) have shown that the transcriptomics of supporting cells between humans and mice is partly different.

That’s what we thought, and the sentence has been changed as follow: “Although DMRT1 is not required for testis determination in mice, it retained part of its function in adulthood when it is necessary to maintain Sertoli cell identity.” (line 51 to 53)

3) Line 78

XY DMRT1-/- rabbits showed early male-to-female sex reversal.

Sex reversal indicates that there is no transient Sertoli cell differentiation that transdifferentiate into granulosa cells. This brings us to an interesting point. In the case of reprogramming, the transient Sertoli cells can produce AMH leading to the regression of the Mullerian ducts. In humans, some 9pdeleted XY patients have Mullerian duct remnants and feminized external genitalia. This finding indicates early defects in testis development.

Is there also feminized external genitalia in XY Dmrt1−/− rabbits. Can the authors comment on the phenotype of the ducts?

We proposed to add “and complete female genitalia” at the end of the following sentence: “Secondly, thanks to our CRISPR/Cas9 genetically modified rabbit model, we demonstrated that DMRT1 was required for testis differentiation since XY DMRT1-/- rabbits showed early male-tofemale sex reversal with differentiating ovaries and complete female genitalia.” (line 77 to 80)

Indeed, since the first stage (16 dpc) where we can predict the sex of the individual by observing its gonads during dissection, we always predict a female sex for XY DMRT1 KO fetuses. It is only genotyping that reveals an XY genotype. At birth, our rabbits are sexed by technicians from the facility and again, but now based on the external genitalia, they always phenotype these rabbits as female ones. In these XY KO rabbits, the supporting cells never differentiate into Sertoli, and ovarian differentiation occurs as early as in XX animals. Thus, these animals are fully feminized with female internal and external genitalia. Most of 9p-deleted patients are not homozygous for the loss-offunction of DMRT1, and the remaining wild-type allele could explain the discrepancy between KO rabbits and humans.

4) Line 53

In the ovary, an equivalent to DMRT1 was observed since FOXL2 (Forkhead family box L2) is expressed in female supporting cells very early in development.

Can the authors clarify what is the equivalent of DMRT1, is it FOXL2? DMRT1 heterozygous mutations result in XY gonad dysgenesis suggesting haploinsufficiency of DMRT1. However, to my knowledge, there is no evidence of haploinsufficiency in XX babies. Thus can we compare testis and ovarian genetics?

We agree, the term “equivalent” is ambiguous, and we changed the sentence as follows: “In ovarian differentiation, FOXL2 (Forkhead family box L2) showed a similar function discrepancy between mice and goats as DMRT1 in the testis pathway. In the mouse, Foxl2 is expressed in female supporting cells early in development but does not appear necessary for fetal ovary differentiation. On the contrary, it is required in adult granulosa cells to maintain female-supporting cell identity.” (line 53 to 56)

Regarding reviewer 2's question on haploinsufficiency in humans: the patient described in Murphy et al., 2015 is an XY individual with complete gonadal dysgenesis. But, it has been shown that the mutation carried by this patient leads to a dominant-negative protein, equivalent to a homozygous state (Murphy et al., 2022).

For FOXL2 mutation in XX females, haploinsufficiency does not affect early ovarian differentiation (no sex reversal) but induces premature ovarian failure.

We agree with the reviewer, we cannot compare testis and ovarian genetics considering two different genes.

5) Line 55

In mice, Foxl2 does not appear necessary for fetal ovary differentiation (Uda et al., 2004), while it is required in adult granulosa cells to maintain female-supporting cell identity (Ottolenghi et al., 2005). The reference Uhlenhaut et al (2009) reporting the phenotype of the deletion of Foxl2 in adults should be added.

The reference has been added.

6) Line 64<br /> These observations in the goat suggested that DMRT1 could retain function in SOX9 activation and, thus, in testis determination in several mammals.

Lindeman et al (2021) have shown that DMRT1 can act as a pioneer factor to open chromatin upstream and Dmrt1 is expressed before Sry in mice (Raymond et al, 1999, Lei, Hornbaker et al, 2007). Whereas additional factors may compensate for the absence of Dmrt1, these results suggest that DMRT1 is also involved in Sox9 activation.

Dmrt1 is indeed expressed before Sry/Sox9 in the mouse gonad. However, no binding site for DMRT1 could be observed at Sox9 enhancer 13 in mice. This does not support a role for DMRT1 in the activation of Sox9 expression in this species. Furthermore, in Lindeman et al 2021, the authors clearly state that DMRT1 acts as a pioneering factor for SOX9 only after birth. It does not appear to have this role before. One of the explanations put forward is that the state of chromatin is different during fetal development in mice: chromatin is more permissive and does not require a factor to facilitate its opening. This hypothesis is based in particular on the description of a similar chromatin profile in the precursors of XX and XY fetal supporting cells, where many common regions display an open structure (Garcia-Moreno et al., 2019). Once sex determination and differentiation are established, a sex-specific epigenome is set up in gonadal cells. Chromatin remodeling agents are then needed to regulate gene expression. We hypothesize that in non-murine mammals such as rabbits, the state of gonadal cell chromatin would be different in the fetal period, more repressed, requiring the intervention of specific factors for its opening, such as DMRT1.

7) Figure 1

Most of the readers might not be familiar with the developmental stages of the gonad in rabbits. A diagram of the key stages in gonad development would facilitate the understanding of the results.

Thank you, it has been added in Figure 1.

8) Figure 2

Arrowheads are difficult to spot, could the authors use another color?

Done

9) Line 117: can the authors comment on the formation of the tunica albuginea? Do the epithelial cells acquire some specific characteristics?

The formation of the tunica albuginea begins with the formation of loose connective tissue beneath the surface epithelium of the male gonad. The appearance of this tissue is concomitant with the loss of expression of DMRT1 in the cell of the coelomic epithelium. Our interpretation is that the contribution of the cells from the coelomic epithelium and their proliferation stops when the tunica begins to form because the structure of the tissue beneath the epithelium change, and the cellular interactions between the epithelium and the tissue below remain disrupted. By contrast, these interactions persist in the ovary until around birth for ovigerous nest formation.

10) The first part of the results described DMRT1 expression in rabbits. With the new single-cell transcriptomic atlas of human gonads, it would be important to describe the pattern of expression in this species. This could be described in the introduction in order to know the DMRT1 expression pattern in the human gonad before that of the rabbit.

A comment on the expression pattern of DMRT1 in human fetal gonads has been added in the discussion section: “In the human fetal testis, DMRT1 expression is co-detected with SRY in early supporting gonadal cells (ESCGs), which become Sertoli cells following the activation of SOX9 expression (Garcia-Alonso et al., 2022) » (line 222 to 224)

11) Figure 3 supplement 3

Dotted line: delimitation of the ovarian surface epithelium. Could the authors check that there is a dotted line?

Done

12) Figure 5 and Line 186

Quantification is missing such as the % of germ cells, % of meiotic germ cells.

Quantification is not easy to realize in rabbits because of the size and the elongated shape of the gonad. Indeed, it’s difficult to be sure that both sections (one from WT, the other from KO) are strictly in a similar region of the gonad and that the section is perfectly longitudinal or not. See also our answer to reviewer 3 (point 7) on this aspect. Actually, we are trying to make a better characterization of this XX phenotype and to find a marker of the pre-leptotene/leptotene stage susceptible to work in rabbits (SYCP3 will be the best, but we encountered huge difficulties with different antibodies and even RNAscope probe!). So actually, the most convincing indirect evidence of this pre-meiotic blockage (in addition to HE staining at 18 dpp in the new Figure 6) is the persistence of POU5F1 (pluripotency), specifically in the germinal lineage of KO XX and XY gonads. In addition to the new figure supplement 5, we can show you in Author response image 1: (i) the gonadal section at a lower magnification, where it is evident that there is a big difference between WT and KO germ cell POU5F1-stainings; and (ii) POU5F1 expression from a bulk RNA-seq realized the day after birth at 1 dpp where the difference is also transcriptionally very clear.

Author response image 1.

13) Line 186,

E is missing at preleptoten

Added

14) Figure supplement 7.

A magnification of the histology of the gonads is missing.

This figure is only for showing the gonadal size, and there are the same gonads as in the new Figure 6. So, the magnification is represented in Figure 6.

15)Discussion

Line 201

SOX9, well known in vertebrates,

The references of the human DSD associated with SOX9 mutations are missing. Thank you, references have been added.

16) Line 286

One of the targets of WNT signaling is Bmp2 in the somatic cells and in turn, Zglp1, which is required for meiosis entry in the ovary as shown by Miyauchi et al (2017) and Nagaoka et al (2020). Does the level of BMP pathway vary in DMRT1 mutants?

At 20 dpc, the expression level of BMP2 in XY and XX DMRT1 mutants gonads is similar to the one of XX control which is lower than in XY control (see the TMP values from our RNA-seq in Author response image 2).

Author response image 2.

Reviewer #2 (Recommendations For The Authors):

Here are my minor comments:

1) Line 106- You mention that coelomic epithelial cells only express DMRT1. Please add an arrow to highlight where you refer to.

Done

2) Line 112: In mice, the SLCs also express Sox9 but not Sry apart from Pax8. You mention here that the SLCs are expressing SRY and DMRT1 in addition to PAX8. Could you perhaps explain the difference? Please refer to that in the results or discussion.

We add a new sentence at the end of this paragraph on SLCs: “As in mice, these cells will express SOX9 at the latter stages (few of them are already SOX9 positive at 15 dpc), but unlike mice, they express SRY.” (line 114 to 115)

We already have collaborations with different labs on these SLC cells, and we will certainly come back later on this aspect, remaining slightly off-topic here.

3) Could you please explain why did you chose to target Exon 3 of DMRT1 and not exons 1-2 which contain the DM domain? Was it to prevent damaging other DMRT proteins? Is there an important domain or function in Exon 2?

Our choice was mainly based on technical issues (rabbit genome annotation & sgRNA design), but also we want to avoid targeting the DM domain due to its strong conservation with other DMRT genes. Due to the poor quality of the rabbit genome, exons 1 and 2 are not well annotated in this species. We have amplified and sequenced the region encompassing exons 1 & 2 from our rabbit line, but the software used for sgRNA design does not predict good guides on this region. The two best sgRNAs were predicted on exon 3, and we used both to obtain more mutated alleles.

4) Your scheme in Supp Figure 4 is not so clear. It is not clear that the black box between the two guides is part of Exon 3 (labelled in blue).

The scheme has been improved.

5) Did you only have 1 good founder rabbit in your experiment? Why did you choose to work with a line that had duplication rather than deletion?

Very good point! In the first version of this paper, we’d try to explain the long (around 2 years) story of breeding to obtain the founder animal. Here it is:

During the genome editing process, we generate 6 mosaic founder animals (5 males and 1 female), then we cross them with wild-type animals to isolate each mutated allele in F1 offspring used afterward to establish and amplify knockout lines. Unexpectedly, we observe a very slow ratio of mutated allele transmission (5 on 129 F1 animals), and only one mutated allele has been conserved from the unique surviving adult F1 animal. It consists of an insertion of the deleted 47 bp DNA fragment, flanked by the cutting sites of the two RNA guides used with Cas9.<br /> The main hypothesis to explain this mutation event is that in the same embryonic cell, the deletion occurs on one allele then the deleted fragment remains inserted into the other allele. Under this scheme, the embryonic cell carries a homozygous DMRT1 knockout genotype, albeit heterogeneous, with a deleted allele (del47) and the present allele (insertion of a 47 bp fragment leading to an in sense duplication). This may explain the very low frequency of transmission since all germ cells carrying a homozygous DMRT1-/- genotype will probably not be able to enter the meiotic process as suggested by our results on XX and XY DMRT1-/- ovaries. Finally, and under this hypothesis, the way we obtained this unique founder animal remains a mystery!

6) Figure 4- real-time data- where does it say what is a,b,c,d of the significance? It should appear on the figure itself and not elsewhere.

Modification done.

7) If I understand correctly, you were able to get the rabbits born and kept to adulthood (you show in supp figure 7 their gonads). What was the external phenotype of these rabbits? Did the XY mutant gonads have the internal and external genitals of a female (oviduct, uterus, vagina etc.)?

See our answer to Reviewer 1 on this question (point 3).

8) Line 20: It is more correct to write 46, XY DSD rather than XY DSD

Modification done.

9) Line 21: you can remove the "the" after abolished

Modification done.

10) Line 31: consider replacing the first "and" by "as well as" since the sentence sounds strange with two "and".

Modification done.

11) Line 212- Please check with the eLife guidelines if they allow "data not shown" in the paper.

This is unspecified.

Reviewer #3 (Recommendations For The Authors):

The following points should be addressed.

1) The in situ's in Fig 1 and 2 are very clear. Fig 1 and Fig 2, In situ hybridisation in tissue sections, it looked like DMRT1 could be expressed in some cells where SRY mRNA is absent @ E13.5dpc and 14.5 dpc. Do you think this is real, or maybe Sry is turned off now in those cells?

Based on the results of in situ hybridizations, DMRT1 appears to be expressed by both coelomic epithelium and genital crest medullar cells in a pattern that is actually broader than that of SRY. Moreover, in rabbits, SRY expression seems to start in the medulla of the genital ridge rather than in the surface epithelium, as described in mice (see Figure 1 at 12 and 13 dpc). Nevertheless, more detailed analyses are needed to ensure the lineage of cells expressing SRY and/or DMRT1, such as single-cell RNAseq at these key stages of sexual determination in rabbits (from 12 to 16 dpc).

2) It is curious that SRY expression is elevated in the DMRT1 KO (Knockout) rabbit gonads. Does this suggest feedback inhibition by DMRt1, or maybe indirect via effect on Sox9 (as I believe Sox9 feeds back to down-regulate Sry in mouse, for example).

The maintenance of SRY expression in the DMRT1 -/- rabbit testis seems to be linked to the absence of SOX9 expression. We believe that, as in mice, SOX9 would down-regulate SRY (even if, in rabbits, SRY expression is never completely turned off).

3) I suggest the targeting strategy and proof of DMRT1 knockout by sequencing etc. be brought out of the suppl. Data and shown as a figure in the text.

See also our answer to reviewer 2 (point 5). It has needed huge efforts to obtain these DMRT1 mutated rabbit line, and of course, it constitutes the basis of the study. But regarding the title and the main message of the article, we are not convinced that the targeting strategy should be moved into the main text.

4) Unless there are limitations imposed by the journal, I also feel that Suppl Fig 5 (the immunostaining) deserves to be in the paper text too. The Fig showing loss of DMRt1 by immunostaining is important.

We include the figure supplement 5 in the main text. So, Figure 4E and figure supplement 5 have been combined into a new Figure 5.

5) The RT-qPCR data should have the statistics clarified on the graphs. (e.g., it is stated that, although Sox9 mRNA is clearly down, there is a slight increase compared to control on KO XX gonads. Is this statistically significant? Figure legend states that the Kruskal-Wallis test is used, and significance is shown by letters. This is unclear. It would be better to use the more usual asterisks and lines to show comparisons.

Modification done.

6) Reference is made to DMRT1+/- rabbits having aberrant germ cell development, pointing to a dosage effect. This is interesting. Does the somatic part of the gonad look completely normal in the het knockouts?

DMRT1 heterozygous male rabbits have a phenotype of secondary infertility with aging, and we are trying now to better characterize this phenotype. The problem is complex because, as we cannot carry out conditional KO, it remains difficult to decipher the consequence of DMRT1 haploinsufficiency in the Sertoli cells versus the germinal ones. Anyway, the somatic part is sufficiently normal to support spermatogenesis since heterozygous males are fertile at puberty and for some months thereafter.

7) Can the authors indicate why meiotic markers were not used to explore the germ cell phenotype? It would be advantageous to use a meiotic germ cell marker to definitely show that the germ cells do not enter meiosis after DMRT1 loss. (Not just H/E staining or maintenance of POU). Example SYCP3, or STRA8 (as pre-meiotic marker) by in situ or immunostaining. Even though no germ cells were detected in adult KO gonads.

The expression of pre-meiotic or meiotic markers is currently under study in DMRT1 -/- females. Transcriptomic data (RNA-seq) are also being analyzed. We are preparing a specific article on the role of DMRT1 in ovarian differentiation in rabbits. We felt it was important to reveal the phenotype observed in females in this first article, but we still need time to refine our description and understanding of the role of DMRT1 in the female.

8) What future studies could be conducted? In the Discussion section, it is suggested that DMRT1 could act as a pioneering factor to allow SRY action upon Sox9. How could this be further explored?

To explore the function of DMRT1 as a pioneering factor, it now seems necessary to characterize the epigenetic landscapes of rabbit fetal gonads expressing or not DMRT1 (comparison of control and DMRT1-/- gonads). Two complementary approaches could be privileged: the study of chromatin opening (ATAC-seq) and the analysis of the activation state of regulatory regions (CUT&Tag). The study of several histone marks, such as H3K4me3 (active promoters), H3K4me1 (primed enhancers), H3K27ac (enhancers and active promoters), and H3K27me3 (enhancers and repressed promoters), would be of great interest. However, these techniques are only relevant for gonads that can be separated from the adjacent mesonephros, which is only possible from the 16 dpc stage in rabbits. To perform a relevant analysis at earlier stages, a "single-nucleus" approach such as ATAC-seq singlenucleus or multi-omic single-nucleus combining ATAC-seq and RNA-seq could be used.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

UGGTs are involved in the prevention of premature degradation for misfolded glycoproteins, by utilizing UGGT-KO cells and a number of different ERAD substrates. They proposed a concept by which the fate of glycoproteins can be determined by a tug-of-war between UGGTs and EDEMs.

Strengths:

The authors provided a wealth of data to indicate that UGGT1 competes with EDEMs, which promotes glycoprotein degradation.

Weaknesses:

Less clear, though, is the involvement of UGGT2 in the process. Also, to this reviewer, some data do not necessarily support the conclusion.

Major criticisms:

(1) One of the biggest problems I had on reading through this manuscript is that, while the authors appeared to generate UGGTs-KO cells from HCT116 and HeLa cells, it was not clearly indicated which cell line was used for each experiment. I assume that it was HCT116 cells in most cases, but I did not see that it was clearly mentioned. As the expression level of UGGT2 relative to UGGT1 is quite different between the two cell lines, it would be critical to know which cells were used for each experiment.

Thank you for this comment. We have clarified this point, especially in the figure legends.

(2) While most of the authors' conclusion is sound, some claims, to this reviewer, were not fully supported by the data. Especially I cannot help being puzzled by the authors' claim about the involvement of UGGT2 in the ERAD process. In most of the cases, KO of UGGT2 does not seem to affect the stability of ERAD substrates (ex. Fig. 1C, 2A, 3D). When the author suggests that UGGT2 is also involved in the ERAD, it is far from convincing (ex. Fig. 2D/E). Especially because now it has been suggested that the main role of UGGT2 may be distinct from UGGT1, playing a role in lipid quality control (Hung, et al., PNAS 2022), it is imperative to provide convincing evidence if the authors want to claim the involvement of UGGT2 in a protein quality control system. In fact, it was not clear at all whether even UGGT1 is also involved in the process in Fig. 2D/E, as the difference, if any, is so subtle. How the authors can be sure that this is significant enough? While the authors claim that the difference is statistically significant (n=3), this may end up with experimental artifacts. To say the least, I would urge the authors to try rescue experiments with UGGT1 or 2, to clarify that the defect in UGGT-DKO cells can be reversed. It may also be interesting to see that the subtle difference the authors observed is indeed N-glycan-dependent by testing a non-glycosylated version of the protein (just like NHK-QQQ mutants in Fig. 2C).

We appreciate this comment. According to this comment, we reevaluated the importance of UGGT2 for ER-protein quality control. As this reviewer mentioned, KO of UGGT2 does not affect the stability of ATF6a, NHK, rRI332-Flag or EMC1-△PQQ-Flag (Fig. 1E, 2A, and 3DE). Furthermore, we tested whether overexpression of UGGT2 reverses the phenotype of UGGT-DKO regarding the degradation rate of NHK, and we found that it did not affect the degradation rate of NHK, whereas overexpression of UGGT1 restored the degradation rate to that in WT cells.

Author response image 1.

Collectively, these facts suggest that the role of UGGT2 in ER protein quality control is rather limited in HCT116 cells. Therefore, we have decided not to mention UGGT2 in the title, and weakened the overall claim that UGGT2 contributes to ER protein quality control. Tissues with high expression of UGGT2 or cultured cells other than HCT116 would be appropriate for revealing the detailed function of UGGT2.

To this reviewer, it is still possible that the involvement of UGGT1 (or 2, if any) could be totally substrate-dependent, and the substrates used in Fig 2D or E happen not to be dependent to the action of UGGTs. To the reviewer, without the data of Fig. 2D and E the authors provide enough evidence to demonstrate the involvement of UGGT1 in preventing premature degradation of glycoprotein ERAD substrates. I am just afraid that the authors may have overinterpreted the data, as if the UGGTs are involved in stabilization of all glycoproteins destined for ERAD.

Based on the point this reviewer mentioned, we decided to delete previous Fig. 2D and 2E. There may be more or less efficacy of UGGT1 for preventing early degradation of substrates.

(3) I am a bit puzzled by the DNJ treatment experiments. First, I do not see the detailed conditions of the DNJ treatment (concentration? Time?). Then, I was a bit surprised to see that there were so little G3M9 glycans formed, and there was about the same amount of G2M9 also formed (Figure 1 Figure supplement 4B-D), despite the fact that glucose trimming of newly syntheized glycoproteins are expected to be completely impaired (unless the authors used DNJ concentration which does not completely impair the trimming of the first Glc). Even considering the involvement of Golgi endo-alpha-mannosidase, a similar amount of G3M9 and G2M9 may suggest that the experimental conditions used for this experiment (i.e. concentration of DNJ, duration of treatment, etc) is not properly optimized.

We think that our experimental condition of DNJ treatment is appropriate to evaluate the effect of DNJ. Referring to the other papers (Ali and Field, 2000; Karlsson et al., 1993; Lomako et al., 2010; Pearse et al., 2010; Tannous et al., 2015), 0.5 mM DNJ is appropriate. In our previously reported experiment, 16 h treatment with kifunensine mannosidase inhibitor was sufficient for N-glycan composition analysis prior to cell collection (Ninagawa et al., 2014), and we treated cells for a similar time in Figure 1-Figure Supplement 4 and 5 (and Figure 1-Figure Supplement 6). We could see the clear effect of DNJ to inhibit degradation of ATF6a with 2 hours of pretreatment (Fig. 1G). Furthermore, our results are very reasonable and consistent with previous findings that DNJ increased GM9 the most (Cheatham et al., 2023; Gross et al., 1983; Gross et al., 1986; Romero et al., 1985). In addition to DNJ, we used CST for further experiments in new figures (Fig. 1H and Figure 1-Figure supplement 6). DNJ and CST are inhibitors of glucosidase; DNJ is a stronger inhibitor of glucosidase II, while CST is a stronger inhibitor of glucosidase I (Asano, 2000; Saunier et al., 1982; Szumilo et al., 1987; Zeng et al., 1997). An increase in G3M9 and G2M9 was detected using CST (Figure1-Figure Supplement 6). Like DNJ, CST also inhibited ATF6a degradation in UGGT-DKO cells (Fig. 1H). These findings show that our experimental condition using glucosidase inhibitor is appropriate and strongly support our model (Fig. 5). Differences between the effects of DNJ and CST are now described in our manuscript pages 8 to 10.

Reviewer #2 (Public Review):

In this study, Ninagawa et al., shed light on UGGT's role in ER quality control of glycoproteins. By utilizing UGGT1/UGGT2 DKO cells, they demonstrate that several model misfolded glycoproteins undergo early degradation. One such substrate is ATF6alpha where its premature degradation hampers the cell's ability to mount an ER stress response.

While this study convincingly demonstrates early degradation of misfolded glycoproteins in the absence of UGGTs, my major concern is the need for additional experiments to support the "tug of war" model involving UGGTs and EDEMs in influencing the substrate's fate - whether misfolded glycoproteins are pulled into the folding or degradation route. Specifically, it would be valuable to investigate how overexpression of UGGTs and EDEMs in WT cells affects the choice between folding and degradation for misfolded glycoproteins. Considering previous studies indicating that monoglucosylation influences glycoprotein solubility and stability, an essential question is: what is the nature of glycoproteins in UGGTKO/EDEMKO and potentially UGGT/EDEM overexpression cells? Understanding whether these substrates become more soluble/stable when GM9 versus mannose-only translation modification accumulates would provide valuable insights.

In the new figure 2DE, we conducted overexpression experiments of structure formation factors UGGT1 and/or CNX, and degradation factors EDEMs. While overexpression of structure formation factors (Fig. 2DE) and KO of degradation factors (Ninagawa et al., 2015; Ninagawa et al., 2014) increased stability of substrates, KO of UGGT1 (Fig. 1E, 2A and 3DF) and overexpression of degradation factors (Fig. 2DE) (Hirao et al., 2006; Hosokawa et al., 2001; Mast et al., 2005; Olivari et al., 2005) accelerated degradation of substrates. A comparison of the properties of N-glycan with the normal type and the type without glucoses was already reported (Tannous et al., 2015). The rate of degradation of substrate was unchanged, but efficiency of secretion of substrates was affected.

The study delves into the physiological role of UGGT, but is limited in scope, focusing solely on the effect of ATF6alpha in UGGT KO cells' stress response. It is crucial for the authors to investigate the broader impact of UGGT KO, including the assessment of basal ER proteotoxicity levels, examination of the general efflux of glycoproteins from ER, and the exploration of the physiological consequences due to UGGT KO. This broader perspective would be valuable for the wider audience. Additionally, the marked increase in ATF4 activity in UGGTKO requires discussion, which the authors currently omit.

We evaluated the sensitivity of WT and UGGT1-KO cells to ER stress (Figure 4G). KO of UGGT1 increased the sensitivity to ER stress inducer Tg, indicating the importance of UGGT1 for resisting ER stress.

We add the following description in the manuscript about ATF4 activity in UGGT1-KO: “In addition to this, UGGT1 is necessary for proper functioning of ER resident proteins such as ATF6a (Fig. 4B-F). It is highly possible that ATF6a undergoes structural maintenance by UGGT1, which could be necessary to avoid degradation and maintain proper function, because ATF6a with more rigid in structure tended to remain in UGGT1-KO cells (Fig. 4C). Responses of ERSE and UPRE to ER stress, which require ATF6a, were decreased in UGGT1-KO cells (Fig. 4DE). In contrast, ATF4 reporter activity was increased in UGGT1-KO cells (Fig. 4F), while the basal level of ATF4 in UGGT1-KO cells was comparable with that in WT (Figure 1-Figure supplement 2B). The ATF4 pathway might partially compensate the function of the ERSE and UPRE pathways in UGGT1-KO cells in acute ER stress. This is now described on Page 17 in our manuscript.

The discussion section is brief and could benefit from being a separate section. It is advisable for the authors to explore and suggest other model systems or disease contexts to test UGGT's role in the future. This expansion would help the broader scientific community appreciate the potential applications and implications of this work beyond its current scope.

Thank you for making this point. The DISCUSSION part has now been separated in our manuscript. We added some points in the manuscript about other model organisms and diseases in the DISCUSSION as follows: “ Our work focusing on the function of mammalian UGGT1 greatly advances the understanding how ER homeostasis is maintained in higher animals. Considering that Saccharomyces cerevisiae does not have a functional orthologue of UGGT1 (Ninagawa et al., 2020a) and that KO of UGGT1 causes embryonic lethality in mice (Molinari et al., 2005), it would be interesting to know at what point the function of UGGT1 became evolutionarily necessary for life. Related to its importance in animals, it would also be of interest to know what kind of diseases UGGT1 is associated with. Recently, it has been reported that UGGT1 is involved in ER retention of Trop-2 mutant proteins, which are encoded by a causative gene of gelatinous drop-like corneal dystrophy (Tax et al., 2024). Not only this, but since the ER is known to be involved in over 60 diseases (Guerriero and Brodsky, 2012), we must investigate how UGGT1 and other ER molecules are involved in diseases.”

Reviewer #3 (Public Review):

This manuscript focuses on defining the importance of UGGT1/2 in the process of protein degradation within the ER. The authors prepared cells lacking UGGT1, UGGT2, or both UGGT1/UGGT2 (DKO) HCT116 cells and then monitored the degradation of specific ERAD substrates. Initially, they focused on the ER stress sensor ATF6 and showed that loss of UGGT1 increased the degradation of this protein. This degradation was stabilized by deletion of ERAD-specific factors (e.g., SEL1L, EDEM) or treatment with mannose inhibitors such as kifunesine, indicating that this is mediated through a process involving increased mannose trimming of the ATF6 N-glycan. This increased degradation of ATF6 impaired the function of this ER stress sensor, as expected, reducing the activation of downstream reporters of ER stress-induced ATF6 activation. The authors extended this analysis to monitor the degradation of other well-established ERAD substrates including A1AT-NHK and CD3d, demonstrating similar increases in the degradation of destabilized, misfolding protein substrates in cells deficient in UGGT. Importantly, they did experiments to suggest that re-overexpression of wild-type, but not catalytically deficient, UGGT rescues the increased degradation observed in UGGT1 knockout cells. Further, they demonstrated the dependence of this sensitivity to UGGT depletion on N-glycans using ERAD substrates that lack any glycans. Ultimately, these results suggest a model whereby depletion of UGGT (especially UGGT1 which is the most expressed in these cells) increases degradation of ERAD substrates through a mechanism involving impaired re-glucosylation and subsequent re-entry into the calnexin/calreticulin folding pathway.

I must say that I was under the impression that the main conclusions of this paper (i.e., UGGT1 functions to slow the degradation of ERAD substrates by allowing re-entry into the lectin folding pathway) were well-established in the literature. However, I was not able to find papers explicitly demonstrating this point. Because of this, I do think that this manuscript is valuable, as it supports a previously assumed assertion of the role of UGGT in ER quality control. However, there are a number of issues in the manuscript that should be addressed.

Notably, the focus on well-established, trafficking-deficient ERAD substrates, while a traditional approach to studying these types of processes, limits our understanding of global ER quality control of proteins that are trafficked to downstream secretory environments where proteins can be degraded through multiple mechanisms. For example, in Figure 1-Figure Supplement 2, UGGT1/2 knockout does not seem to increase the degradation of secretion-competent proteins such as A1AT or EPO, instead appearing to stabilize these proteins against degradation. They do show reductions in secretion, but it isn't clear exactly how UGGT loss is impacting ER Quality Control of these more relevant types of ER-targeted secretory proteins.

We appreciate your comment. It is certainly difficult to assess in detail how UGGT1 functions against secretion-competent proteins, but we think that the folding state of these proteins is improved, which avoids their degradation and increases their secretion. In Figure 1-Figure supplement 2E, there is a clear decrease in secretion of EPO in UGGT1-KO cells, suggesting that UGGT1 also inhibits degradation of such substrates. Note that, as shown in Fig. 3A-C, once a protein forms a solid structure, it is rarely degraded in the ER.

Lastly, I don't understand the link between UGGT, ATF6 degradation, and ATF6 activation. I understand that the idea is that increased ATF6 degradation afforded by UGGT depletion will impair activation of this ER stress sensor, but if that is the case, how does UGGT2 depletion, which only minimally impacts ATF6 degradation (Fig. 1), impact activation to levels similar to the UGGT1 knockout (Fig 4)? This suggests UGGT1/2 may serve different functions beyond just regulating the degradation of this ER stress sensor. Also, the authors should quantify the impaired ATF6 processing shown in Fig 4B-D across multiple replicates.

According to this valuable comment, we reevaluated our manuscript. As this reviewer mentioned, involvement of UGGT2 in the activation of ATF6a cannot be explained only by the folding state of ATF6a. Thus, the part about whether UGGT2 is effective in activating ATF6 is outside the scope of this paper. The main focus of this paper is the contribution of UGGT1 to the ER protein quality control mechanism.

Ultimately, I do think the data support a role for UGGT (especially UGGT1) in regulating the degradation of ERAD substrates, which provides experimental support for a role long-predicted in the field. However, there are a number of ways this manuscript could be strengthened to further support this role, some of which can be done with data they have in hand (e.g., the stats) or additional new experiments.

In this revision period, to further elucidate the function of UGGT, we did several additional experiments (new figures Fig. 1H, 2DE, 4G and, Figure 1-Figure Supplement 6). We hope that these will bring our papers up to the level you have requested.

Reviewer #1 (Recommendations For The Authors):

Minor points:

(1) Abbreviations: GlcNAc, N-acetylglucosamines -> why plural?

Corrected.

(2) Abstract: to this reviewer, it may not be so common to cite references in the abstract.

We submit this manuscript to eLife as “Research Advances”. In the instructions of eLife for “Research Advances”, there is the description: “A reference to the original eLife article should be included in the abstract, e.g. in the format “Previously we showed that XXXX (author, year). Here we show that YYYY.” We follow this.

(3) Introduction: "as the site of biosynthesis of approximately one-third of all proteins." Probably this statement needs a citation?

We added the reference there. You can also confirm this in “The Human Protein Atlas” website. https://www.proteinatlas.org/humanproteome/tissue/secretome

(4) Figure 1F - the authors claimed that maturation of HA was delayed also in UGGT2 cells, but it was not at all clear to me. Rescue experiments with UGGT2 would be desired.

We agree with this reviewer, but there was a statistically significant difference in the 80 min UGGT2-KO strain. Previously, it was reported that HA maturation rate was not affected by UGGT2 (Hung et al., 2022). We think that the difference is not large. A rescue experiment of UGGT2 on the degradation of NHK was conducted, and is shown in this response to referees.

(5) Figure 4A, here also the authors claim that UGGT2 is "slightly" involved in folding of ATF6alpha(P) but it is far from convincing to this reviewer.

Now we also think that involvement of UGGT2 in ER protein quality control should be examined in the future.

(6) Page 11, line 7 from the bottom: "peak of activation was shifted from 1 hour to 4 hours after the treatment of Tg in UGGT-KO cells". I found this statement a bit awkward; how can the authors be sure that "the peak" is 4 hours when the longest timing tested is 4 hours (i.e. peak may be even later)?

Corrected. We deleted the description.

(7) Page 11, line 4 "a more rigid structure that averts degradation" Can the authors speculate what this "rigid" structure actually means? The reviewer has to wonder what kind of change can occur to this protein with or without UGGT1. Binding proteins? The difference in susceptibility against trypsin appears very subtle anyway (Figure 4 Figure Supplement 1).

Let us add our thoughts here: Poorly structured ATF6a is immediately routed for degradation in UGGT1-KO cells. As a result, ATF6a with a stable or rigid structure have remained in the UGGT1-KO strain. ATF6a with a metastable state is tended to be degraded without assistance of UGGT1.

(8) Figure 1 Figure supplement 2; based on the information provided, I calculate the relative ratio of UGGT2/UGGT1 in HCT116 which is 4.5%, and in HeLa 26%. Am I missing something? Also significant figure, at best, should be 2, not 3 (i.e. 30%, not 29.8%).

Corrected. Thank you for this comment.

Reviewer #2 (Recommendations For The Authors):

(1) The effect in Fig. 2B with UGGT1-D1358A add-back is minimal. Testing the inactive and active add-back on other substrates, such as ATF6alpha, which undergoes a more rapid degradation, would provide a more comprehensive assessment.

To examine the effect of full length and inactive mutant of UGGT1 in UGGT1-KO and UGGT2-KO on the rate of degradation of endogenous ATF6a, we tried to select more than 300 colonies stably expressing full-length Myc-UGGT1/2, UGGT1/2-Flag, and UGGT1/2 (no tag), and their point mutant of them. However, no cell lines expressing nearly as much or more UGGT1/2 than endogenous ones were obtained. The expression level of UGGT1 seemed to be tightly regulated. A low-expressing stable cell line could not recover the phenotype of ATF6a degradation.

We also tried to measure the degradation rate of exogenously expressed ATF6a. But overexpressed ATF6a is partially transported to the Golgi and cleaved by proteases, which makes it difficult to evaluate only the effect of degradation.

(2) In reference to this statement on pg. 11:

"This can be explained by the rigid structure of ATF6(P) lacking structural flexibility to respond to ER stress because the remaining ATF6(P) in UGGT1-KO cells tends to have a more rigid structure that averts degradation, which is supported by its slightly weaker sensitivity to trypsin (Figure 4-figure supplement 1A). "

The rationale for testing ATF6(P) rigidity via trypsin digestion needs clarification. The authors should provide more background, especially if it relates to previous studies demonstrating UGGT's influence on substrate solubility. If trypsin digestion is indeed addressing this, it should be applied consistently to all tested misfolded glycoproteins, ensuring a comprehensive approach.

We now provide more background with three references about trypsin digestion. Trypsin digestion allows us to evaluate the structure of proteins originated from the same gene, but it can sometimes be difficult to comparatively evaluate the structure of proteins originated from different genes. For example, antitrypsin is resistant to trypsin by its nature, which does not necessarily mean that antitrypsin forms a more stable structure than other proteins. NHK, a truncated version of antitrypsin, is still resistant to trypsin compared with other substrates.

(3) Many of the figures described in the manuscript weren't referred to a specific panel. For example, pg. 12 "Fig. 1E and Fig.5," the exact panel for Fig. 5 wasn't referenced.

Thank you for this comment. Corrected.

(4) For experiments measuring the composition of glycoproteins in different KO lines, it is necessary to do the experiment more than once for conducting statistical analysis and comparisons. Moreover, the authors did not include raw composition data for these experiments. Statistical analysis should also be done for Fig. 4E-F.

Our N-glycan composition data (Figure 1-Figure supplement 5 and 6C) is consistent with previous our papers (George et al., 2021; George et al., 2020; Ninagawa et al., 2015; Ninagawa et al., 2014). We did it twice in the previous study and please refer to it regarding statistical analysis (George et al., 2020). We add the raw composition data of N-glycan (Figure 1-Figure supplement 4 and 6B). In Fig. 4D-F, now statistical analysis is included.

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