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Referee #3

Evidence, reproducibility and clarity

Summary

The authors observe that proteasomal protein and activity is increased in skeletal muscle of mice fed a high fat diet. Concordant with this, they find increased expression of Nfe2l1 (NRF1), an ER localized protein that can be cleaved to produce a transcription factor that activates a set of genes that includes most proteasome subunits. To test the role of Nfe2l1 in the response to high fat feeding, the authors generated muscle specific KO of Nfe2l1 and characterized the muscles using fiber typing, proteomic, ubiquitinomic, RNAseq and metabolomic analysis on the muscle of these mice. Gastrocnemius muscle fast twitch fibers appeared most affected and modulated towards slow twitch phenotype, whilst soleus muscle appeared unaffected. Mitochondrial function was decreased as were levels of complex III. Ubiquitinome analysis showed differential ubiquitination of proteins involved in muscle structure and function and increased K48 ubiquitin chain linkages. Metabolomic studies showed altered amino acid metabolism, glucose metabolism and induction of a Warburg effect. Finally, upon high fat feeding, the Nfe2l1 mKO mice gained less weight, had higher energy expenditure, and were more insulin sensitive.

Major comments

1. The authors have conducted a multi-omics analysis of the skeletal muscle of mice bearing a muscle specific KO of Nfe2l1 and have attempted to integrate the findings. However, despite reading the manuscript several times, I have trouble trying to identify the key message of the paper and so feel that a lot of data was presented, but without a clear sense of how all the data (or some of it) really ties together. I suggest that the authors identify the main message, select the relevant data for the main body of the text and assign the remaining data to supplementary figures. The discussion should emphasize the main message.
2. Metabolically, the most impressive result was the minimal weight gain on high fat feeding. The authors vaguely suggest that Nfe2l1 might be a therapeutic target 'to preserve muscle mass and healthy metabolism in obesity and beyond'. Since the main effect of Nfe2l1 seemed to be downregulation of the proteasome, should the authors have tested the effects of low dose proteasome inhibitors in WT mice to mimic the partial loss of proteasome activity seen in the Nfe2l1 mKO on the response to high fat feeding? This could confirm or support the idea that the main effect is due to Nfe2l1 modulation of the proteasome.
3. The authors claim that there is rewiring of the UPS in obesity through the induction of Nfe2l1. What do the authors mean by rewiring? If the main effect of Nfe2l1 is to modulate proteasome activity, presumably all upstream processes (ubiquitination by various E3s) are affected. Indeed, in the ubiquitinomic analysis in figure 4F, there do not appear any pathways that are downregulated. Regardless, there is no data presented to show that specific pathways of ubiquitination are altered and therefore 'rewired'. The 'rewiring' strikes me as a fancy term used inappropriately here.
4. I was surprised that the authors did not use the tamoxifen inducible Cre to inactivate Nfe2l1 in adult muscle. As such, the interpretation of the results of their study is limited by the effects of loss of Nfe2l1 during development and so inhibit to some degree potential links to translation. The authors should note this limitation in their discussion.
5. Relevant to the above point about KO from development, in the first characterization of the mKO of Nfe2l1, (Figures 2G, 2I) the muscles actually look dystrophic. There appear to be central nuclei in the muscle of the mKO in Fig 2G and sarcomeric dysorganization in Fig 2I and the authors mention the presence of inflammatory cytokines and regenerative isoforms (Fig 2H) in the muscle. Are the mKO dystrophic, undergoing damage and regeneration? This is an important point to address with quantification of central nuclei, inflammatory cytokine expression, infiltration by mononuclear cells, fibrosis, blood levels of creatine kinase.

Minor comments

1. Abstract - the authors used the fancy term 'hormetic'. My understanding is that this refers to a phenomenon where effects at low dose (usually positive) are different or opposite from effects at high dose (usually negative). I didn't see such a biphasic phenomenon in the Nfe2li mKO mice. Also the authors should specify that it is a muscle specific KO.
2. Text on page 3 'In human muscle, we noted that NFE2L1 is highly expressed, at much higher levels compared to other established muscle regulators, such as NFE2L2 or PPARGC1A (Fig. 1K)'. Discerning the importance of a transcription factor by comparing its expression at the mRNA level is dubious. It is the protein that acts and the extent of gene transcriptional activity that is important.
3. Figure 2A-C - The mKO mice are smaller and have less lean mass and fat mass. Were the mKO mice born with smaller muscles and therefore had trouble feeding or competing for breast milk prior to weaning? This again relates to the issue of not having used a tamoxifen inducible KO. Are the muscle sizes proportionate to body weight or more importantly body length or tibial length?
4. Figure 2G - As mentioned in general comment 5, the mKO muscle looks dystrophic. Also the % fibers of each type should be quantified to demonstrate the fiber type shifting. This should ideally be done in the complex zone of the gastrocnemius where all the fiber types are present. Also, the fibers look bigger in the mKO. It is standard to do an analysis of the distribution of cross-sectional areas of the muscle fibers and this can be done in a fiber specific manner from the stained images in the middle panels (with laminin staining added to delineate the fibers).
5. Figure 2J - remarkably complex III (cytochrome C reductase) levels are significantly decreased. Any explanation for this? Does Nf2el1 bind to the promoter or regulate its transcription?
6. Figure 2H - state in legend whether the 'relative expression levels' are for protein or for mRNA.
7. Figure 3C, 3G - why does the trypsin-like activity of the proteasome go up when the other 2 activities of the proteasome go down?
8. Figure 4E - Why is there a set of proteasome genes that are upregulated in the mKO? Most of these (except Psmd9/Rnp4) encode subunits of the PA28 activator. Is this a compensatory response or a response to inflammation in the dystrophic muscle? This needs some comment in the paper.
9. Figure 5D, text page 8 - 'we found several genes to be oppositely regulated between soleus and GC'. What genes were these and are they enriched in a particular pathway e.g. one that modulates fiber type phenotype?
10. Figure 6D, 6E - The increased energy expenditure and increased food intake may simply be due to increased heat loss from the smaller mKO mice (they have a relatively larger body surface area).
11. Figures 7A, 7B - Was the body composition different in the mKO mice fed a high fat diet vis WT HFD mice?
12. Figure 7E - What is the insulin tolerance like when normalized to starting glucose?
13. Discussion - Please insert figure numbers in the discussion so reader can refer back to the data on which the conclusions in the discussion are being made.
14. Figure 1G and Discussion first paragraph - It would be more quantitatively precise to measure the ubiquitinated proteins by western blot (as done in Fig 3I) than to sum up the ubiquitin linkages.
15. Discussion para 2, ref 26. This reference is to a paper on effects of lipid peroxidation on muscle atrophy in aging or disuse and not to obesity. Revise to be more precise.
16. Discussion page 12 last para - 'some components of the proteasome'. As mentioned earlier, these appear to be mostly subunits of the PA28 proteasome activator. Should state this and discuss.
17. Discussion page 13, para 3 and extended data Fig 2A-2D. What is the significance of the higher FGF21 and GDF15 expression in mKO muscle? Could they be involved in the improved glucose tolerance or the decreased fat mass respectively?
18. Methods section 2.8 - many abbreviations for reagents that are not defined e.g. SDC, CAA, TCEP, etc
19. Methods 2.11 - the authors did whole muscle proteomics and ubiquitinomics which they recognized would be limited by the overwhelming representation by myofibrillar proteins. Did they try any manoeuvres to enhance detection of non-myofibrillar proteins?
20. Methods, section 2.13 - the mitochondria were quantified by protein assay. Since the 8000g pellet used to isolate the mitochondria may contain other proteins, should the mitochondria be quantified in a more specific way e.g. assaying several mitochondrial proteins or measuring mitochondria DNA content? This is important vis a vis figure 2L which showed decreased mitochondrial respiration in the mKO.
21. Extended data Fig 1D. Were these measures of markers of atrophy done at the protein level or mRNA level? They should be done at the mRNA level as this is a more sensitive and precise marker of atrophy than the protein levels (which don't change as much and for which many antibodies are not specific).
22. There is a lot of useful omics data here. Where will they be shared for use by the research community?

Referees cross-commenting

The overall tenor of the three reviews is similar. Comments are both overlapping and complementary. I realize that I forgot two other specific comments:

• (a) In extended fig 1C, the authors quantify the slower migrating LC3B-I band, but it is the faster migrating lipidated LC3B-II band that is a marker of autophagasomes that should have been quantified.
• (b) Some references e.g. 37, 40 are missing information.

Significance

The authors have carried out what appears to be a thorough multi-level omics study of a muscle specific KO of Nfe2l1. It appears to have been technically well done, but I do not have expertise in such analyses and so cannot be rigorously critical in this aspect. (My expertise is in UPS function in skeletal muscle.) The major limitations of the present manuscript are highlighted in my major comments.

In view of the important role of Nfe2l1 in regulation of expression of the proteasome, the muscle specific KO provided a partial inhibition of proteasome activity and therefore a unique view into the role of the proteasome in muscle particularly under the condition of high fat feeding. Therefore, the potential audience could be quite broad including researchers in muscle biology, UPS and obesity. However, Nfe2l1 has other effects besides induction of expression of proteasome genes, thereby limiting the confidence that all effects observed are related to the modulation of the proteasome and the consequences of such modulation on levels of UPS substrates

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Referee #2

Evidence, reproducibility and clarity

In this paper, Lemmer and colleagues explore the role of the endoplasmic reticulum (ER)-resident transcription factor Nfe2l1 in muscle metabolism in mice following high-fat diet (HFD). Here, the authors made the interesting observation that HFD is associated with increased proteasome activity in skeletal muscles (Fig.1), a process known to rely on Nfe2l1 and confirmed by Figs. 2 and 3. By using a tissue-specific Nfe2l1 knockout (KO) mouse model, the authors show that Nfe2l1 is also critical in preserving mitochondria and oxidative phosphorylation in muscles during HFD (Figs. 4, 5 and 6). Finally, the authors show that fast/glycolytic muscle fiber growth in Nfe2l1 KO mice is accompanied by reduced body weight and improved glucose tolerance (Fig. 7).

This paper is potentially interesting and addresses the important issue of energy metabolism regulation in diet-induced obesity (DIO) using an original mouse model. However, the argument presented in this paper has sometimes logical gaps, making it difficult for the reader to connect all the dots. For instance, what is the relationship between proteasome function and energy metabolism in DIO? Is there any relationship at all? Ultimately, Nfe2l1 has other target genes than the proteasome ones, particularly those related to mitophagy process (PMID: 30135079, this paper should be cited and discussed) which could easily explain the observations made by the authors regarding respiration and metabolism...

1. The authors failed to explain why muscle cells upregulate their proteasomes during HFD. My prediction is that this happening because of increased protein synthesis which itself occurs as a consequence of sustained mTOR signaling. Increased translation would then result in increased supply of defective ribosomal products (DRiPs) which need to be timely cleared by the ubiquitin-proteasome system (UPS). I leave to the authors the possibility to address this hypothesis experimentally.
2. The authors consistently show a correlation between HFD and increased Nfe2l1 expression. These observations, however, do not imply that Nfe2l1 is activated in DIO. The authors should assess Nfe2l1 processing - or at least nuclear translocation - in muscles over time
3. If Nfe2l1 is indeed activated by HFD, what would be the stimulus? Compromised proteasome function? Oxidative stress? Cholesterol changes? This point needs to be clarified.
4. Fig. 1C: the increased proteasome subunit expression in DIO seems minuscule... How about Western-blotting the native gel for proteasome subunits to check whether the observed proteasome activity matches the proteasomes amounts under these conditions?
5. Fig. 2J: a densitometry quantification of the WB would be welcome.
6. Fig. 2K. captions are incomplete. What is PMG, SUC or FCCP?
7. Discussion:" Furthermore, we found that some components of proteasome activity are higher in cells or tissues lacking Nfe2l1, indicating a potential compensatory posttranslational modification of proteasome function." What components?? Is it shown in the manuscript? Unclear.
8. Discussion: Next to changes in total amount and activity, we also found that proteasome subunits accumulated in a hyperubiquitylated state (Extended Data Fig. 1A), but the relevance of this observation will need further investigation. These proteasome subunits are not assembled ones, but likely derive from DRiPs, as a consequence of increased translation (see point 1).
9. Discussion: "Clearly, disturbances in UPS and ERAD cause ER stress and inflammation (10), which we also observe in our model." Where are the data in this regard? Do the authors mean Fig. 5B? I do not see any convincing data on inflammation here (BTW, what is Gm11517?).

Significance

General assessment:

As previously discussed, this work from Bartel's lab is interesting but not suitable for publication in its present form. It should be revised to clarify the role of Nfe2l1-induced proteasomes in DIO.

Advance

Although the role of Nfe2l in mitochondrial function is known (PMID: 30135079, this paper should be cited and discussed), the consequences on energy metabolism in skeletal muscles described in this paper are novel.

Audience

If appropriately revised, this manuscript should be of interest to a wide readership.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In the manuscript entitled "Nfe2l1-mediated proteasome function controls muscle energy metabolism in obesity", Lemmer and colleagues observe elevated 20S proteasome activity along with increased expression of the transcription factor Nfe2l1, a known stimulator of proteasome subunit biogenesis, in muscle tissue of diet-induced obese mice. To understand the role of Nfe2l1 in regulating skeletal muscle proteostasis, they use siRNA to knockdown Nfe2l1 in cultured C2C12 muscle cells and cross Nfe2l1 floxed mice with and Acta1-Cre line to KO Nfe2l1 specifically in muscle fibers. Nfe2l1mKO mice show reduced body and muscle size, impaired enzymatic activity of some proteasome subunits, an accumulation of ubiquitylated proteins, a fast-to-slow shift in muscle fiber phenotype and metabolic abnormalities, including impaired mitochondrial function and mild increases in relative energy expenditure. Multi-omics analysis at transcript, protein, ubiquitinated protein and metabolite levels indicate a strong influence of Nfe2l1 loss on muscle homeostasis. These affects appear to predominately affect fast-type (i.e. Gastrocnemius) rather than slow-type (i.e. soleus) muscles. Finally, Nfe2l1mKO mice fail to gain weight on a high fat diet and are therefore spared the typical metabolic alterations associated with obesity.

Major comments:

1. The authors push the idea that the UPS, via Nfe2l1, plays an 'adaptive' role in regulating muscle proteostasis, however, all signaling experiments investigating the effect of muscle fiber Nfe2l1 KO are performed under basal conditions.
2. Due to the use of ACTA1-Cre to conditionally KO Nfe2l1 in muscle fibers, Nfe2l1 is also absent during development. It is therefore difficult to distinguish the acute effects of Nfe2l1 on muscle proteostasis from those that may result from developmental impairment. It is conceivable that remodeling of muscle architecture would be more active during development than in mature muscle and therefore perhaps more sensitive to impairments in proteasome biogenesis. Use of an inducible Cre system (e.g. the tamoxifen inducible HSA-MerCreMer model) and/or the addition of acute Nfe2l1 overexpression experiments would be needed to dissociate acute, primary effects of Nfe2l1 from the secondary features of long term Nfe2l1 KO and disruption of proteostasis.
3. It is unclear what the HFD experiments reported in Figure 7 add to our understanding of the role of Nfe2l1 in skeletal muscle. I could understand if an inducible Nfe2l1mKO system was used to test the role of Nfe2l1 in already obese mice... but a failure of a mouse displaying myopathic features to put on weight is not the same as an alteration that improves metabolic health. As Nfe2l1mKO mice do not become obese, the authors are unable to directly test what role the upregulation of muscle Nfe2l1 plays in maintaining proteostasis in obesity. On the other hand, I find it hard to conclude that the absence of muscle Nfe2l1 is beneficial for metabolic health if fed a HFD, especially given the reported increase in p62 and LC3B (indicative of autophagy impairment) and the impaired muscle mitochondrial function. Further investigations in older mice would be required to determine the long-term impact of muscle Nfe2l1 KO on whole-body health under both normal and high-fat diet feeding conditions.
4. The authors note several interesting muscle phenotypes, including a fast-to-slow fiber type transition and an increased expression of neonatal myosin heavy chain isoforms (Myh3 & 8). The representative images seem to indicate that IIA (green) fibers are larger in Nfe2l1mKO mice. I would recommend quantifying fiber type-specific cross sectional area in Gastrocnemius muscle sections from these mice, as well as confirming the increased 'regeneration' phenotype by quantifying the prevalence of centralized nuclei.
5. Figure 3D: Why would Nfe2l1 KD lead to a larger increase in ubiquitylated proteins after proteasome inhibition? If Nfe2l1 KD reduces proteasome subunit gene expression (presumably also protein content) and proteasome activity (although this effect is rather mild), then blocking a proteasome with lower activity should lead to a lower accumulation of ubiquitylated proteins, despite an accumulation of ubiquitylated proteins under basal conditions.
6. Fig3C&G: The finding that Nfe2l1 KD/KO mildly reduces chymotrypsin-like and caspase-like (in mice) activity, but strongly increases trypsin-like activity is surprising. As these activities are mediated by different Beta subunits within the 20S core particle, it would be important to also test whether protein levels of PSMB5 (Chymotrypsin), PSMB6 (Caspase) and PSMB7 (trypsin) are altered by Nfe2l1 in accordance with differences in their measured activity.
7. The authors have a tendency to use vague terms to describe changes in proteostasis resulting from Nfe2l1 KO, for example: 'recalibration', 'adaptive', 'fine-tuning', 'remolding', 'remodeling', 'rewiring'. While it is understandable that Nfe2l1 and the UPS will have different roles under different conditions, the use of vague language makes it difficult to understand whether they are referring to reduced or increased proteasome activity. Please be clear and precise as the direction of the changes observed. The same goes for the extension of conclusions made on measures of proteasome activity to mean activity of the UPS / protein breakdown. Specific examples are described within the minor comments section.

Minor comments:

Introduction: Nfe2l1 does not restore proteasome activity per se, but stimulates proteasome subunit biogenesis and thereby increases proteasome content. This would not necessarily influence activity, which also relies on the presence of substrate/ubiquitination.

Introduction: 'we investigate remodeling of the muscle UPS in obesity and define the role of Nfe2l1 as a new regulator of muscle biology'. This statement is an overreach, particularly seeing as a role for Nfe2l1 has already been described in skeletal muscle, albeit under a different context (ref. 29).

Results: "Of note, leptin levels in chow-fed animals were indifferent". I guess this is a typo? Should be 'different' not 'indifferent'.

Results: "These global changes are in line with the notion that UPS is activity is rewired and metabolism impacted by HFD feeding." Please use specific language to describe the changes you see.

Results: "The data supported the hypothesis that Nfe2l1 stimulates protein degradation via the proteasome, as the dominant lysine-linkage was the proteasome-targeting linkage K48, accounting for more than 86 % and being significantly higher in muscle of mKO mice compared to tissue of WT controls (Fig. 4G)." While it is clear that depleting a protein contributing to proteasome biogenesis would impair proteasome function, this would not be sufficient to say that Nfe2l1 promotes protein degradation via the proteasome. So far, there is no evidence that increasing Nfe2l1 increases protein degradation.

Figure 1L: What is the unit of measurement for gene expression?

Figure 2G: There appears to be significant freeze damage in H&E and SDH sections from Nfe2l1mKO mice. Perhaps you can find better representative images.

Results: "In summary, these results establish Nfe2l1 as an adaptive regulator of proteasomal activity and ubiquitylation in cultured myocytes". Why do these results establish Nfe2l1 as an 'adaptive' regulator? These are steady state conditions. Results so far would only indicate that Nfe2l1 controls proteasome subunit biogenesis in myocytes, which is well known in other cell types and has also been shown in skeletal muscle tissue.

Results: "The proteome showed many significantly regulated proteins and in general a higher protein load in the mKO condition (Fig. 4A), potentially caused by impaired proteasomal protein degradation." What is meant by a 'higher protein load'

Discussion: "Here, we show that proteasomal activity and management of ubiquitin levels in muscle is a regulated and critical process in obesity, as proteasome levels and function are increased in obesity." This is actually not shown. As Nfe2l1 KO mice do not become obese, it is unclear what role this increase plays under the conditions of obesity.

Discussion: "Interestingly, at the same time, total ubiquitin levels are largely unchanged, which suggests a dynamic recalibration of the rates of protein synthesis and degradation, including the processes necessary for ubiquitylation and its targets". The authors seem to be interpreting ex vivo proteasome activity assays as a readout of protein breakdown rates in vivo. These Proteasome activity assays are only a readout of proteasome content, not activity, since substrate entry into the 26S proteasome is tightly controlled by its cap structure. Ex vivo, substrates able to independently access the inside of the 20S proteasome (and hence the active protease sites) are provided in abundance.

Discussion: "However, overall proteasomal activity was lower and ubiquitin levels higher, indicating the predominant role of Nfe2l1 determining rates of UPS in myocytes." The reduction in activity was not so strong that it could be considered predominant. Furthermore, proof is only provided for Nfe2l1 regulating proteasome content... not rates of UPS breakdown, which also relies on the ubiquitination part of the system.

Discussion: "There seems to be profound crosstalk between proteostatic mechanisms in muscle, as we found in the proteome of Nfe2l1 mKO muscle that autophagy pathways are markedly upregulated, including p62 and LC3B levels (Extended Data Fig. 1B-C)". This should be first introduced into the results section.

Discussion: "Uncoupling of mitochondria and loss of mitochondrial membrane potential in myocytes are associated with the induction of FGF21 (33), a myokine that is implicated in regulating energy metabolism. We find that FGF21 and GDF15 expression were higher in muscle of mKO mice compared to WT controls, and for GDF15 also plasma levels were elevated (Extended Data Fig. 2A-D)." This should be included in results section.

Significance

General assessment: after identifying increased proteasome activity and an associated increase in Nfe2l1 expression in the muscle of obese mice, this work provides strong evidence that muscle fiber Nfe2l1 expression is necessary for muscle fiber development / homeostasis, with wide ranging effects of muscle fiber Nfe2l1 KO, including on body and muscle size, fiber type composition and mitochondrial content and function. On the other hand, muscle fiber Nfe2l1 KO mice fail to become obese, making it hard to draw conclusions on the role of increased Nfe2l1 in the muscle of obese mice.

Advance: This study complements recent work showing a role for increased Nfe2l1 expression in maintaining proteostasis under a different proteostatic challenge, and suggests a role for muscle Nfe2l1 in response to obesity.

Audience: This study is likely to be of interest to readers interested in proteostasis, the UPS and muscle biology.

Expertise: Muscle proteostasis and aging.

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Reply to the reviewers

We thank the reviewers for their careful and constructive evaluation. We believe the requested revisions are feasible will substantially strengthen the manuscript.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, Halter and colleagues propose a novel approach to sample level analysis of single cell disease atlas by only considering cellular proportion. They perform an evaluation with several SOTA approaches including ones using both pseudo-bulk or combination of compositional and transcriptional changes. While bench-marking results are positive, the design of the study including selected data and evaluated statistics differs from previous studies possibly indicating some bias selections. The paper has also strong statements on the fact their method is not affected by batches, while this is only shown in a single data set and some of the evaluated data has batched samples removed. These results are very likely misleading and authors need to either remove such strong claims or show strong evidence supporting it.

Main points

Authors indicate only samples with 500 cells are included. How would the method work without such a filter? Evaluation should also be done on sparse data, as this might be frequent in single cell studies. Otherwise, tgus should be also discussed as a limitation of the study. Authors should discuss the potential risk of this variance-based thresholding inadvertently filtering out rare, low-variance cell populations that carry critical biological significance. Also, could it be that this filter simply selects condition specific cells (cancer cells in cancer samples?). Regarding the previous concern, it is unclear if this performance retention is unique to ECODA's log-ratio approach. For a fair comparison, the authors should benchmark the competing compositional methods using the exact same HVC subset to determine if the performance advantage stems from the algorithm itself or simply the feature selection. In this case, some methods, such as PILOT, need cell types. To comprehensively demonstrate ECODA's performance, the authors should compare their approach against recently introduced sample-level representation methods. QOT: https://academic.oup.com/bib/article/26/1/bbae713/7953914. Joodaki, M. (n.d.). PILOT-GM-VAE: patient-level analysis of single-cell disease atlas with optimal transport of Gaussian mixture variational autoencoders. Pang, K. (n.d.). PULSAR: a Foundation Model for Multi-scale and Multi-cellular Biology. Regarding the data selection, authors should include all the previous data as in previous studies. See PILOT, PILOT-GM-VEA or QOT for a larger selection of data sets. The current approach uses k-means but some of the evaluated methods are shown to work better with other clustering methods (Leiden) or similarity metrics (Cosine). Authors should improve the benchmarking to also include richer strategies on how to perform clustering and include metrics evaluating the distances directly (silhouette index). Data has very strong filters that remove confounding factors. For example, the authors handle demographic confounders (such as age) in the Gong & Sharma dataset by severely restricting the cohort (males <= 40 years), which limits real-world clinical applicability where cohorts have complex, overlapping covariates. Can ECODA deal with the data sets without any kind of filter on confounding factors?

In the Stephenson dataset, the authors manually restricted the data to a single clinical location ("Ncl site"). If ECODA is as robust to batch effects as claimed, manual exclusion of multi-center data should be unnecessary. The authors should explain why this pre-filtering was required and evaluate if ECODA can accurately stratify patients when all multi-center data is included. Another example of a batch rich data is the KPMP Kidney data, which include multicenter and multi protocols single nuc vs. single cell data. The claim that ECODA is robust to batch effects is currently supported only by ANOSIM scores on two datasets, which is insufficient by current single-cell benchmarking standards. To rigorously demonstrate that ECODA effectively resists batch effects while conserving biological variance, the authors should evaluate their sample-level embeddings by using more data and also utilizing metrics such as Silhouette batch, LISI, and so on (take a look at scvi-tools, https://docs.scvi-tools.org/en/1.3.3/tutorials/notebooks/scrna/harmonization.html). Besides, they need to drop all filters based on clinical variables and include additional data sets as previously discussed.

Referees cross-commenting

Reviewers do focus on distinct but non conflicting aspects, while some similar points regarding benchmarking are quite similar between us and reviewer 2. I would like however to stress the batch correction aspect, which is currently a big statement on the manuscript, but we could capture several design issues with this aspect.

Significance

The discussion on how to analyze single cell data of patients cohorts is of strong significance. Authors make an interesting point that cell frequencies can work well, but the results are clearly biased by data selection and experimental design. The study will have a greater value if authors can tune down most of their claims and instead have a more balanced analysis on when compositional analysis is best and when transcriptional signatures are best. This is likelly to be very study/data dependent.

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Referee #2

Evidence, reproducibility and clarity

This manuscript benchmarks scRNA-seq sample representation methods for unsupervised patient stratification. The authors demonstrate that centered log-ratio (CLR)-transformed cell-type proportions (ECODA) match or outperform more complex state-of-the-art methods while requiring orders of magnitude fewer computational resources. The accompanying scECODA R package facilitates practical adoption.

Software availability. scECODA, integrated into Bioconductor and Seurat workflows as an open-source R package, substantially increases the practical impact of this work. scECODA comes with proper documentation and meaningful tutorials.

Major Concerns

1. The benchmark conflates methods with fundamentally different objectives. Several benchmarked methods were not designed primarily for unsupervised patient stratification by clustering. MrVI, for instance, explicitly targets the identification of local gene expression shifts that would be missed by a composition-based approach (scPoli likely behaves similarly though this manuscript lacks analysis). These methods are likely complementary to ECODA rather than competing with it. This is already partly visible in the benchmark: MrVI performs superior to ECODA on the Adams and Stephenson datasets while underperforming elsewhere. The authors should investigate and discuss why ECODA underperforms in these specific cases for example, whether transcriptional reprogramming rather than compositional shifts dominates the biological signal in those datasets. Such an analysis would provide practical guidance for method selection and reframe the benchmark as a characterization of complementary use cases rather than a simple ranking.
2. The Leiden clustering benchmark requires clarification and extension. This concern has several distinct components that should each be addressed:
   • Batch correction dependency: ECODA's robustness to batch effects may derive partly from cell types being called in batch-corrected embedding spaces (e.g., Harmony or scVI), rather than from ECODA itself. The authors should clarify whether cell-typing in batch-corrected embeddings are a prerequisite for ECODA's batch robustness, and if so, make this explicit in the workflow recommendations.
   • Performance in challenging compositional scenarios: The Gong Sharma dataset, which requires fine-grained immune cell-type resolution to separate CMV-positive from CMV-negative individuals, is arguably the most demanding test case for Leiden-based annotation. Would unsupervised Leiden clustering achieve comparable performance to expert labels in this scenario? This is not addressed in the current analysis.
   • Resolution parameter guidance: The manuscript implies that higher Leiden resolutions are generally better for ECODA, but there must be practical limits to this - overclustering introduces noisy, sparsely populated clusters that destabilize CLR estimates. The authors should provide clearer guidance on how to select the resolution parameter in the absence of expert labels.
   • Stability of the identified marker cell types: Figure 3B shows that the top contributing cell types identified by ECODA differ substantially between HiTME and authors_HR annotations for the Adams dataset. How stable are these "marker" cell types across annotation strategies, and what are the implications for biological interpretation?
3. The range of zero-handling values tested is too narrow. The benchmarked pseudocount values are in a relatively small range, and performance differences among them are minimal. To establish that the recommended default (pseudocount of 0.5) is genuinely optimal rather than arbitrarily chosen, the authors should extend the analysis to much smaller values (e.g., 1×10⁻³) and much larger values (e.g., 100). This would demonstrate that performance degrades at the extremes and that the current default sits in a robust optimum.
4. The HVC analysis would benefit from a more rigorous feature selection framework. The current approach selects highly variable cell types based on unsupervised variance ranking. Since the goal is patient stratification, it would be informative to compare this approach against supervised feature selection methods (e.g., LASSO-penalized classification). This comparison would clarify whether the variance-based approach approximates supervised selection, or whether meaningful discriminative signal is being left on the table. Separately, the claim that HVC-based ratios are directly translatable to clinical platforms such as flow cytometry should be made more carefully: several of the identified marker cell types (e.g., KLRF1⁻ GZMB⁺ CD27⁻ memory CD4 T cells) require multi-parameter panels that are not routinely employed in clinical practice.
5. Cell-type annotation subjectivity introduces a potential source of bias not discussed. The authors evaluate annotation robustness across strategies but do not discuss a related concern: future studies may define cell types in a manner that, intentionally or not, introduces a desired sample stratification, while cell populations associated with unwanted variation (e.g., technical confounders) may be merged or excluded. This subjectivity could inflate ECODA's apparent performance in practice and should be acknowledged explicitly in the Discussion as a caveat of annotation-dependent methods.
6. The title and framing overstate a causal claim. "Cell type composition drives patient stratification" implies that compositional differences causally determine clinical phenotypes. The benchmark establishes that compositional representations perform well for stratification, not that composition causes the underlying biology. The title and several passages in the manuscript should be revised to reflect this distinction for example, replacing "drives" with "predicts" or "reflects."
7. Foundation model-based methods should be discussed and ideally benchmarked. PULSAR, which uses the Universal Cell Embeddings (UCE) foundation model as a basis for sample-level representations, was recently introduced and represents an emerging class of methods not covered in this benchmark. Including PULSAR would future-proof the comparison. If the computational burden of full benchmarking is prohibitive, it would be a valuable addition to the Discussion.
8. The benchmark should address large-scale and multi-study scenarios. Studies with thousands of samples (e.g., OneK1K) and multi-study atlases (e.g., the Human Lung Cell Atlas) represent the trajectory of the field. Including at least one such dataset would substantially strengthen the claim that ECODA is scalable and robust to batch effects. This is especially critical as deep-learning based methods might scale favorably with the number of samples.

Minor Points

• The number of nearest neighbors used for modularity computation is three, which is small and may introduce instability. A sensitivity analysis across a range of neighbor values is warranted.
• A comparison to the cLISI (cell-type Local Inverse Simpson's Index) metric, widely used in single-cell integration benchmarks, would be appreciated, though cLISI operates at the cell level rather than the sample level and adaptation for this setting might be necessary.

Significance

Given rapidly increasing scRNA-seq cohort sizes, rigorous evaluation of sample-level representation strategies is pressing. The field has invested heavily in complex methods, making this comparative analysis valuable.

This is a well-executed benchmarking study that delivers a clear and practically useful message: properly handled cell-type compositional data is a powerful and underappreciated representation for scRNA-seq cohort analysis.

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Referee #1

Evidence, reproducibility and clarity

This paper presents the ECODA method and scECODA package, which uses simple sample-level representations based on transformed cell-type abundances to recover biological stratification of the samples. This compares favourably to more complex embedding-based methods across 11 datasets.

I would like to congratulate the authors on a well written and interesting manuscript. My most important concern is that there is potentially some circularity in the labels and disease classifications used for evaluation. Some of this is mitigated by the cluster-derived cell labels, but not all of it, since part of the concern relates to how the sample-level disease labels were defined. A negative-control benchmark using labels not expected to be composition-driven would help clarify this.

The manuscript appears to motivate ECODA partly as a tool for de novo exploratory patient stratification, but the benchmark mainly evaluates recovery of known biological labels. This is a reasonable validation strategy, but it does not directly assess whether the method can discover previously unknown patient subgroups, or determine the number and clinical relevance of such groups without label guidance. This distinction should be made clearer early in the paper.

p3:

'across 11 patient cohorts' - are there common aspects to these? It would be good to indicate why these were chosen and what the strategy is.

p7, Fig 2 A:

The runtime for ECODA and GloProp seem to be significantly less than the shuffled baseline, but the implication is that they do more calculations, which seems surprising. Is this an artifact?

p8/9:

A possible limitation is that the benchmark may be enriched for studies where compositional shifts are already expected to be strong.

In a similar sense, for disease states that are conventionally defined in a specific cell type, the analysis could be recovering label-associated annotation structure rather than independent disease biology. This is especially relevant for high-resolution manual annotations, where disease-associated cell states may already encode part of the biological contrast being evaluated.

A negative-control or stratified benchmark on labels not expected a priori to be composition-driven, or on composition-matched sample groups, would be a useful cross-check here.

p10:

It would also be interesting to see the robustness to small sample sizes, as this isn't mentioned elsewhere, but potentially could be a confounder in many patient derived samples.

p11:

The distinction between ECODA and scECODA could be a little clearer here. As far as I understand scECODA is the R tool and ECODA is the general method?

p13:

The claim that inter-sample biological variation is largely explained by cell-type abundance may need some qualification, because some of the disease or disease-state labels may themselves be partly compositionally defined. If disease state was assigned or refined using histopathology, cellular composition, or the presence of particular cell populations, then a composition-based method is partly being evaluated against labels that already contain composition-like information. This might weaken the interpretation that composition is an independent driver of disease biology, rather than a correlate of how the disease category was operationally defined.

It would therefore be useful to give more detail on how these disease labels were derived. This concern is not removed by using cluster-derived cell labels, because the possible circularity is in the disease-state definition rather than the cell annotation procedure.

'For example, ratios...immunotherapy response.' - A citation here would be good.

'Cost effective diagnostic assays...' - Perhaps a bit of an overstatement. This would likely require validation across larger cohorts, clinical sample-processing conditions, sequencing depth/cell recovery difference, etc. This claim could be softened or framed as a future direction.

p14:

'Expert author annotations...' - this could be clarified. Were these all manually curated annotations from the original studies, or did some original studies use automated/reference-based annotation followed by curation?

p15:

'We further controlled...' - was the analysis also evaluated over these separate subsets (other than just males <= 40) as a cross check?

p19:

HVCs: Could you comment on this procedure, versus something more akin to highly variable gene selection?

Significance

This paper presents a fast and interpretable method for sample-level stratification of single-cell RNA-seq cohorts, based primarily on compositional differences in cell-type abundance. This makes it of broad interest to researchers performing cohort-level scRNA-seq analysis, since its speed and simplicity make it an attractive baseline even when more involved downstream analyses are planned. However, as presented, its performance is less well established for datasets without reliable high-resolution annotations, for settings where the relevant structure is not primarily compositional, and for genuine de novo discovery of patient subgroups rather than recovery of known labels.

My background is in computational biology and biophysics.

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The authors do not wish to provide a response at this time.

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Referee #3

Evidence, reproducibility and clarity

Summary

During mitosis transcription is silenced (except at centromeres) and the majority of chromatin-bound RNA is removed from chromosomes. Previous work has shown that retention of elongating RNAPII on mitotic chromosomes through a WAPL degron leads to transcription-dependent chromosome segregation errors. Additionally, retention of chromatin bound RNAs through mutation of HNRNPU/SAF-A also leads to chromosome segregation errors. However, the field lacks a complete understanding of the mechanisms that remove RNA from chromatin in mitosis. Previous work from the Oliveira lab (and others) demonstrated that depletion of Lds/TTF2 also leads to chromosome segregation errors, but it was not possible to directly link chromosome segregation defects to persistent mitotic transcription. In this current work the authors examine the role of TTF2 in mitosis in human cells. They nicely show that TTF2 is required to release transcripts from chromatin during mitosis and that retention of transcripts on chromatin leads to chromosome segregation errors. Interestingly the authors find that depletion of TTF2 leads to an increase in the number of R-loops present on mitotic chromosomes and that R-loop-containing DNA is a major component of anaphase bridges. The results presented in the manuscript are high quality and the data support the conclusions. This work is important because it provides further evidence that the removal of RNA and transcription complexes from mitotic chromosomes is important for accurate chromosome segregation. There are a couple of points that the authors should consider prior to publication listed below and some minor issues with data presentation that should be corrected.

Major points

1. The authors use RNAi to deplete TTF2 and examine mitosis following depletion. The authors state that TTF2 depletion requires 48 hours, or approximately 2 cell cycles. Since TTF2 is depleted for the entire cell cycle it is possible that transcription termination defects caused by TTF2 depletion during interphase causes defects in mitosis and that the observed phenotypes are not a result of mitotic function of TTF2. This concern is somewhat addressed by the observation where the authors inhibit transcription using triptolide and show that this treatment rescues chromosome segregation defects observed following TTF2 depletion. However, the TRP treatment is for 4 hours, which includes a substantial portion of interphase. The length of TTF2 depletion is a significant concern and I think there are two ways that this could be addressed:

a. Create a TTF2-AID (or dTAG) cell line and analyze chromosome segregation defects following TTF2 depletion only in mitosis. This is a difficult and time-consuming experiment but is also the most direct test of the role of TTF2 in mitosis. This experimental system would be required for publication in a high-impact journal.

b. Include a section in their discussion acknowledging that indirect effects could be a cause of the chromosome segregation errors observed following TTF2 depletion. 2. The authors nicely show that TTF2 depletion leads to a significant retention of EU-labeled RNA on mitotic chromosomes but do not address the nature of these transcripts. Additionally, the authors do not show that TTF2 depletion leads to changes in transcription in interphase cells. This work could be improved by the addition of EU-RNA sequencing data showing that TTF2 depletion leads to transcriptional changes in interphase (e.g. transcription past the normal termination site) and EU-RNA sequencing to identify that transcripts that are retained on mitotic chromosomes. Neither of these experiments are absolutely necessary for publication but would significantly improve the general interest of this work. 3. The authors show that TTF2 depletion leads to an increase of R-loops on anaphase bridges. Previous work has shown that R-loops are present at mitotic centromeres (29170278) and that activation of ATR through these R-loops is necessary for accurate chromosome segregation. This work is clearly relevant to the authors results and has not been cited or discussed. This previous work should be included in the discussion and interpretation of the authors' work.

Minor points

1. In Figure 1 the authors show a comparison of the levels of EU-labeled RNA in control and TTF2-depleted cells at each stage of mitosis. The graphs in B and D would be much easier to compare if these were combined into a single graph.
2. There are a number of quantitative plots that are lacking statistical comparisons between key groups. These are: Figure 1B and D, Figure 1F, S2B, Figure 4DE, S6C,

Significance

This advance is incremental but adds to accumulating evidence that transcription termination is important for normal chromosome segregation.

The strengths of this work are high quality data, careful analysis, and the fact that conclusions follow directly from the data presented.

The weaknesses are that the model system in not optimal to address the question being posed and that the authors have not completely characterized their model system.

This work will primarily be of interest to groups working on mitotic chromatin:RNA and transcriptional regulation.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this original article, authors attempt to define the molecular and cellular consequences of retaining spurious transcriptional activity in mitotic chromosomes. The study uses the depletion of TTF2 (transcription termination factor 4) in tissue culture of HeLa cells as a model. Results show the accumulation of nascent RNAs and R-loops as a product of such aberrant transcription which, strikingly, increases the incidence of chromosome segregation errors. Importantly, authors elegantly show that these errors are corrected by inhibition of RNA Polymerase2 activity with previously reported drugs. This reviewer finds the study very interesting and compelling, very well written and structured. However, I consider that the adjustment of several aspects might improve the manuscript:

Major comments.

1. The main limitation of the study relies on the approach followed to deplete TTF2. Authors used siRNAs in order to decrease the levels of this factor, which implies an incubation time of 48h. This might represent a limitation. Regarding this aspect, this referee request to show the proof of TTF2 depletion in the main figure with accurate quantification when possible.
2. Most of the main conclusions are very well supported by quantification of imaging data. However, this referee suggests the generation of superplots (ref) where values and average for each replicate can be clearly visualized. Statistical analyses comparing the median from each different conditions by t-student (unpaired test) will better support the outcome.
3. Authors show a beautiful correlation between the presence of R-loops and chromosome segregation errors (Figure 6). I request the authors to replicate the experiment with cn or TTF2 siRNAs in combination with the triptolide treatment. Additionally, and to provide further evidence about the functional consequences of retaining R-loops, I wonder if authors can drive specific R-loop depletion by using RNase H activity. This will definitely reveal whether transcription activity or/and its product underlies the chromosome segregation defect.

Minor comments.

1. I highly recommend to include the value of all the statistic tests in each plot.
2. I would suggest the incorporation of a final paragraph at the end of the introduction summarizing the most important results of the study.
3. In the introduction, and based on wide evidences showing transcriptional activity at centromere regions (Chan 2012, Liu 2016, Perea-Resa 2024), and to a much lower extend, at the chromosome arms of mitotic chromosomes (Palozola, 2017), I would rephrase to make clear that transcription is generally repressed rather than globally silenced in mitosis.

Referees cross-commenting

After reading the comments from the other two referees, I maintain my view about the quality/interest of the manuscript. I endorse the potential publication of this work, after addressing the recommendations, in a reasonable period of time.

Significance

Authors provide a compelling study addressing the functional relevance of repressing transcription early in mitosis to properly segregate chromatids to daughter cells. In addition, the study also pursuits to illuminate the molecular and cellular consequences of inactivating TTF2 function and to provide insight into the chromosome segregation defects found under TTF2 misfunction. The study considers and discusses the most important aspects of the literature relevant for the proposed questions. The results are very encouraging and mostly confirmed by several orthogonal approaches.

The major strength is the direct correlation found between R-loop retention and chromosome segregation defects. The major limitation is, however, the usage of slow siRNA-based strategies to deplete TTF2. The use of degron-protac alternatives would be very beneficial although I do not consider this an essential aspect.

The study is sound and address very interesting still open questions. The publication of the results will influence and benefit a wide audience specially researches working on the mitosis and transcription fields. Research on R-loops, a field full of open questions, would also acknowledge the insights from this study.

Overall, I consider the study very interesting and compelling. I support the evaluation and envision that its publication, once addressed the above described comments, will be feasible within roughly 3-6 months of revision.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Tovini and colleagues investigate the role of transcriptional silencing during mitosis using depletion of TTF2, a factor implicated in mitotic transcription termination. The authors show that TTF2 depletion leads to retention of elongating transcripts on mitotic chromatin, defects in chromosome organization and compaction, delayed mitotic progression, and increased chromosome segregation errors, particularly DNA bridges and UFBs. They further report accumulation of R-loops and demonstrate that transcription inhibition largely suppresses the observed segregation defects.

Overall, this manuscript is interesting and potentially important, and the study is technically sound. In particular, I liked the experiments showing continued transcript elongation during mitosis in TTF2-depleted cells. The rescue experiments with triptolide also support the conclusion that transcription contributes significantly to the observed phenotypes. The methods and statistical analyses appear generally appropriate and sufficient for reproducibility.

At the same time, I think that several aspects of the mechanistic interpretation are somewhat overstated, and some important alternative explanations remain insufficiently addressed. For these reasons, I believe the manuscript would benefit from substantial revision before publication.

Major comments

1. The authors favor a model where persistent transcription and R-loop accumulation interfere with Top2A-mediated sister chromatid resolution. While this is certainly possible, I do not think the presented data fully support such a specific interpretation. The authors demonstrate a pronounced chromosome organization phenotype. TTF2 depletion causes broadened metaphase plates and approximately 1.5-fold increased chromosome volume. These observations suggest a substantial defect in mitotic chromosome compaction. An important alternative possibility should be considered, namely that persistent mitotic transcription interferes with Condensin I and/or Condensin II loading and/or retention. Given the current understanding that chromosome condensation and loop organization are highly dynamic processes, it is conceivable that ongoing transcription could impair Condensin-mediated chromosome assembly. At minimum, the authors should assess chromosomal localization of Condensin I and II in mitotic cells after TTF2 depletion (for example CAP-H/CAP-D2 and CAP-H2/CAP-D3). Such analysis, ideally also including triptolide rescue, would substantially strengthen the mechanistic interpretation and help distinguish between a primarily transcription/R-loop-mediated defect and a more global chromosome assembly defect.
2. The authors conclude that kinetochore-microtubule attachments are largely normal, based on Mad2 localization, inter-centromere distance, and the absence of strongly uncongressed chromosomes. In my opinion, these measurements are indirect and do not sufficiently demonstrate robust mature end-on attachments. Given the observed metaphase spreading, mild congression defects, and SAC-dependent delay, it remains possible that TTF2 depletion causes more subtle defects in k-fiber stability or attachment robustness. I think a cold-stability assay of spindle microtubules would be important here. Such experiment would directly address whether cold-stable k-fibers are normally formed and maintained in TTF2-depleted cells. Ideally, this should be combined with kinetochore markers and quantification of k-fiber intensity. Without such analysis, the statement that KT-MT attachments are unaffected should be toned down.
3. The manuscript generally frames mitotic transcription as detrimental to chromosome segregation. However, several previous studies, including work from Hongtao Yu's lab, reported that localized centromeric/kinetochore transcription during mitosis contributes positively to chromosome segregation, including correct Sgo1 localization and centromeric function (this literature is not discussed, despite appearing conceptually relevant to the present study). This is not necessarily a contradiction; it seems possible that a limited and spatially restricted mitotic transcription program at centromeres may be beneficial, whereas persistent chromosome-wide elongation caused by TTF2 depletion becomes pathological. However, this distinction should be discussed explicitly. As currently written, the manuscript risks giving the impression that mitotic transcription is generally deleterious, which would not be fully consistent with the literature. The authors should check whether Sgo1 is localized correctly after TTF2 depletion in both Noc-arrested and metaphase (MG132- or ProTAME-arrested) cells.
4. I was somewhat confused by the interpretation of RPA70-positive fibers. The authors state that they "did not detect a major increase" in RPA70-coated UFBs, arguing against an important contribution of replication-associated intermediates. However, in the next sentence, they report that approximately 20% of TTF2-depleted anaphases display an RPA70-positive fiber and, importantly, this phenotype is largely reverted by triptolide. In my opinion, this is not a trivial observation and appears difficult to fully reconcile with the conclusion that replication-associated events contribute minimally to the phenotype. In principle, RPA70 positivity should not necessarily be interpreted exclusively as evidence of replication stress. Persistent transcription, R-loops, or transcription-associated topological stress could generate ssDNA intermediates that can recruit RPA. Do RPA-positive fibers co-localize with R-loops? Therefore, the Discussion would benefit from a more balanced interpretation of these findings.
5. The rescue experiments with triptolide are convincing and support a transcription-dependent contribution to the phenotype. However, because triptolide treatment was performed over several hours, these experiments do not formally distinguish between ongoing transcription elongation during mitosis and perturbations arising earlier in the cell cycle, including possible transcription-replication conflicts during late S/G2. This limitation should be acknowledged more clearly in the Discussion, especially given the recently described role of TTF2 in replisome eviction. It would be informative to perform a time-course analysis of triptolide rescue. Demonstration that the phenotype can be substantially reverted within ~30 minutes of treatment would strongly support the interpretation that persistent transcription during mitosis, as opposed to earlier cell-cycle perturbations, is the major contributor to the observed defects.

Minor comment:

It would be useful to check whether RHINO-positive/R-loop-associated structures preferentially localize to centromeric versus chromosome arm regions. Such information may help distinguish physiological mitotic transcription from pathological transcript retention.

Referees cross-commenting

I have carefully read the other reviews and they do not change my overall assessment of the manuscript or my recommendations.

Significance

General assessment:

This is an interesting and potentially important study addressing how transcriptional silencing contributes to mitotic fidelity. The strongest aspect of the work is the convincing demonstration that transcription elongation persists during mitosis after TTF2 depletion and contributes to chromosome segregation defects. The main limitation is that the mechanistic interpretation currently appears somewhat narrower than supported by the data.

Advance:

The study extends previous work on TTF2 by linking defective mitotic transcriptional silencing to chromosome organization and chromosome segregation defects. The demonstration of transcription elongation during mitosis after TTF2 depletion is particularly interesting.

Audience

The work will likely be of interest to researchers studying mitosis, chromosome biology, transcription, genome stability, and chromosome organization.

Expertise:

mitosis, chromosome organization, nuclear organization, cell biology, biochemistry. I do not consider myself an expert in R-loop biology or transcription-coupled repair.

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Reply to the reviewers

Reviewer #1:

Major comments:

1. Lines 103-116 (first paragraph of the results section) describe mainly published data that is more suitable for the introduction section. It is annoying to refer to different published articles in the Results section to strengthen the results instead of showing them. The same goes for paragraphs two and three. Why mention those data in the Results section if they are already published and known?

We have reorganized this material by moving some background information to the Introduction. Our intention was not to incorporate published data to strengthen our results, but rather to provide essential context for interpreting our findings. We have therefore left some of this foundational information in the results section to create a clear narrative flow, enabling readers to understand the basis for our experimental design and interpretations without needing to recall details from earlier paragraphs in the Introduction. For example, we considered it crucial to restate the earlier report of the BiP:sfGFP:HDEL phenotype in Atlastin mutants, since our results supporting luminal ER protein displacement contradict the previous fragmentation model.

The following concept was in line 103 in the Results section, and is now in the introduction in lines 82-92: "Conventional light microscopy, commonly used in studies of neuronal ER structure, lacks the resolution necessary to visualize individual ER tubules in small structures, such as presynaptic terminals. The ER is highly sensitive to fixation, and live imaging experiments in neurons in vivo have been conducted on upright microscopes using water dipping objectives with a typical axial resolution limit of >300 nm, which cannot distinguish the densely packed ER tubules at presynaptic terminals (3,8,21,28,39-42). Electron microscopy offers higher resolution, but cannot be used in live samples and has typically been limited to thin 2D sampling (in which it is difficult to distinguish ER cross-sections from synaptic vesicles) (8,20,22)."

Figure Legends-(in all Figures): The number of experimental repeats must be mentioned in the figure legends.

This information is provided in Supplementary Table 1, which contains detailed information about the genotype, statistical analysis, and number of larvae and NMJs analyzed. If the journal requires this information in figure legends, we can move it.

The way the figures are labeled is worrisome; supplementary figures are not ordered numerically.

We will be happy to rename supplementary figures according to journal guidelines.

The tubule extension in Figure 2D is not convincing. Is there a movie showing those changes? Better images are needed. It is essential to show which supplemental movie corresponds to which panel.

We have now included a corresponding video of the same neuron used as an example of tubule extension. We also added another frame to the figure to provide further information on the tubule event we captured. (Figure 2D, Movie S10)

This is unnecessary in the results section: "To investigate the relationship between ER structure and function at synapses, we examined mutants of Atlastin, a GTPase that regulates ER tubule fusion. Drosophila has a single homolog while mammals have three Atlastin homologs, with Atlastin-1 enriched in the brain (Rismanchi et al., 2008)."

This information was moved to the introduction.

"This reduction in ER membrane marker intensity has also been observed in other HSP mutants, suggesting this is a common feature of ER shaping mutants and could indicate changes in ER membrane composition, integrity, or tubule thickness (Perez-Moreno et al., 2023)." This comparison is important and should be shown in the same settings as for the Atlastin mutant rather than referring to published data.

We agree with the reviewer that it is important to determine whether other ER-shaping proteins, besides Atlastin, also show a decrease in tdTomato:Sec61b to support our claim that this could be a common feature among ER-shaping mutants. To do this, we examined mutants of another ER-shaping protein, Reticulon 1, which regulates membrane bending and stabilization in ER tubules. These loss-of-function mutants were a gift from Dr. Cahir O'Kane at the University of Cambridge and were used in his lab's Pérez-Moreno et al., 2023 publication. We found that in our hands tdTomato:Sec61b levels were reduced in Reticulon 1 mutants, consistent with the results reported by Pérez-Moreno et al. (2023). These results are in Figure 3E-F. We also examined the synaptic distribution of the luminal ER marker, BiP:sfGFP:HDEL, in Reticulon 1 mutants to see if it is displaced to the cytosol. Notably, it remained ER-associated, unlike in Atlastin mutants. These results are in Figure 6F-G, results lines 267-270, and discussion lines 542-545.

Does the distribution of the luminal ER marker in Figure 6F diffuse due to mislocalization or reflux after being localized to the ER and then refluxed to the cytosol as was previously shown for the ER to Cytosol signaling (ERCYS) mechanism? Could you assess other ER-luminal protein localization biochemically? It is highly recommended to look at another soluble ER-protein localization in the Atlastin mutant without overexpression, which can be an artifact.

ER stressors can induce ERCYS, in which some luminal proteins, including PDIA3, DNAJB11, ERp29, and an eroGFP reporter, reflux by 30-70% to the cytoplasm without subsequent degradation (unlike ERAD (ER-associated degradation). This phenomenon has only previously been observed in yeast and glioblastoma tumor cells from mice and human . We believe that our work provide the first suggestion that this may occur in neurons, and particularly in a neurological disease model.

We do not believe that the reflux phenotype for BiP:sfGFP:HDEL is due to its overexpression for two reasons: (1) we observe reflux in our neuronal Atlastin knockdown experiments, even when the levels of BiP:sfGFP:HDEL are significantly reduced artificially because of titration of the GAL4 between the RNAi and the reporter (Figure 7A), and (2) BiP:sfGFP:HDEL overexpression somewhat suppresses endogenous BiP upregulation ((Figure 10 and see Reviewer 1.10), arguing that the transgene does not induce ER stress). We included a new "limitations of the study" section to be transparent about the caveats of the BiP:sfGFP:HDEL reporter (lines 639-664).

Identifying potential endogenous neuronal ERCYS substrates in our in vivo preparation poses several challenges. First, biochemical approaches, such as fractionation, are not possible in our complex in vivo sample because neuronal ER proteins would mix with ER from other tissues upon homogenization. Second, detecting endogenous proteins with antibodies requires fixation and permeabilization, which notoriously disrupts ER structure and even causes our reporter BiP:sfGFP:HDEL to collapse from a smooth distribution, as visualized by live imaging and FRAP, to a punctate distribution. Third, using antibodies rather than neuronally restricted transgenes makes it challenging to determine whether the signal originates from the neuron or from dense ER structures in the surrounding muscle. Fourth, some ER luminal proteins can displace as little as 30% in the ERCYS examples cited above, and the sensitivity of our imaging assays may limit our ability to detect these small changes. Finally, the limited availability of tagged transgenes and antibodies specific to Drosophila luminal ER proteins (see next paragraph) poses additional challenges. These limitations highlight the need for future studies to develop novel tools and techniques to more definitively test whether we are indeed observing ERCYS. We have included a paragraph on these future challenges in our discussion in lines 639-664. Identifying endogenous targets of ERCYS in fly neurons is a worthwhile goal, but beyond the scope of the current study. These next steps will particularly benefit from identifying the machinery involved in the reflux of our BiP:sfGFP:HDEL reporter.

Tools we tested: We investigated several options: (1) a tagged PDI transgene (a gift from Karen Hibbard), which was not detectable at presynaptic terminals, (2) a tagged BiP (FlyORF; F000956) that did not localize to the ER, and (3) full-length endogenous BiP detected by antibody staining. We did not detect obvious reflux of endogenous BiP to the cytoplasm (Figure 9), with the caveat that in fixed samples, the BiP signal was not tightly co-localized with the ER marker even under control conditions. However, we did use this antibody to detect an increase in BiP in Atlastin mutant presynaptic terminals, indicating ER stress (see Reviewer 1.10).

Though we have not identified endogenous targets, we believe that our studies with the exogenous reporter will be of great interest to the field, as they clarify the previously reported Atlastin phenotype and provide the first report of a new defect in a human disease animal model.

In comparison to Summerville et al. (2016) in Figure 7, the experiment was not done in the same way. It is important to keep the same settings for comparison

In Figure 7D-E, we compare the distribution of BiP:sfGFP:HDEL in cell bodies, axons, and muscles between controls and Atlastin mutants. To clarify the experimental approach relative to Summerville et al. (2016): while both our studies examined the same cellular compartments (cell bodies, axons and nerve terminals) using the BiP:sfGFP:HDEL reporter, we employed super-resolution Airyscan microscopy. This enhanced resolution was critical for definitively demonstrating that this is a functional rather than a structural phenotype and that ER displacement is progressive, and repeating this experiment at lower resolution as previously reported does not provide any new information. We identified two distinct distribution phenotypes in Atlastin mutants expressing BiP:sfGFP:HDEL, which were not described in the Summerville et al., 2016 paper. From our manuscript (lines 249-251): "We identified two distinct ER network phenotypes in Atlastin mutants expressing BiP:sfGFP:HDEL: "Partial loss" NMJs retained both diffuse signal and identifiable ER network structures, while "Complete loss" NMJs showed no visible ER network structures. Note that the "Complete loss" phenotype in Atlastin mutants reflects the absence of detectable luminal marker signal in organized ER structures, but not the complete absence of ER membranes, as demonstrated by our ER membrane marker tdTomato:Sec61β results."

Does the Atlastin mutant induce the unfolded protein response and stress within the ER? It is necessary to look for UPR markers in those settings. It was shown previously that ER stress leads to protein reflux from the ER to the cytosol. Is there a difference in the ER stress markers in the presynaptic terminal?

The reviewer suggested that Atlastin mutant synapses may exhibit ER stress. To address this, we examined levels of the ER chaperone BiP, a well-established ER stress marker whose expression increases during UPR activation. We first validated that our BiP antibody can detect changes in ER stress by feeding control larvae with 50mM DTT for 24 hours. These results are in the new Figure 10A. Note that we were unable to test sensitivity to ER stress in this way in Atlastin mutant larvae because they did not consume the DTT-treated food, as assessed by blue food coloring in the larvae's guts.

Using this antibody, we measured baseline BiP levels at NMJs of Atlastin mutants on normal food, and found they were slightly increased compared to controls. We conclude from these experiments that Atlastin mutant synapses have mild ER stress. Notably however, Atlastin mutants co-expressing UAS-BiP:sfGFP:HDEL or UAS-tdTomato:Sec61b did not show significantly increased endogenous BiP levels, suggesting that transgene expression at least partly suppresses the mild ER stress response, even though there is extensive cytosolic displacement. These results argue (1) that the mild ER stress in Atl mutants does not strictly correlate with the reflux phenotype, and (2) that the reflux phenotype is not an artifact of overexpression-induced stress. These results are described on lines 430-436 in the results section and shown in Figure 10B-E, and their implications discussed on lines 585-598.

We also explored another strategy to detect ER stress by assessing eIF2α phosphorylation, a key event in the Unfolded Protein Response (UPR) pathway. We obtained a phospho-eIF2α antibody (Cell Signaling; #3597) that was reported to work in Drosophila. However, when we tested this antibody by Western blot, we were unable to detect a band at the expected molecular weight for phosphorylated eIF2α, even in positive-control samples treated with DTT to induce ER stress. We therefore concluded that this antibody is not suitable for reliably detecting ER stress in our experimental system. The failure of this antibody highlights the challenges of finding robust tools to measure ER stress in Drosophila.

It is important to add biochemical experiments to show that no fragmentation of the ER membrane occurred. It can be simply demonstrated by looking at the redox state of the ER, which would change if it were mixed with the reducing cytosol. Moreover, this can be shown by using an ER-targeted redox-sensitive fluorescent protein that is tethered to the ER membrane to follow changes in the redox state of the ER.

The reviewer asked us to test whether the redox state of the ER is disrupted, which could indicate exchange between the cytosol and ER due to membrane rupture. As noted above, biochemical approaches such as fractionation are not possible in this in vivo sample. We attempted to address this concern by creating a UAS-Sec61β:roGFP construct, using the roGFP sequence from Igbaria et al. (2019) to monitor the ER lumen redox environment in Atlastin mutants. Since Sec61β is membrane-tethered, it should remain in the ER and not undergo reflux, making it an ideal sensor for detecting any mixing between the reducing cytosolic environment and the oxidizing ER lumen that would occur if membrane fragmentation and/or ruptures were present. We tested this approach in wild-type Drosophila S2 cells and used the Gal4-UAS binary expression system to co-express Actin-Gal4 (to drive expression of UAS constructs), UAS-Sec61β:roGFP (redox sensor), and UAS-BiP:Halo:HDEL (as a control reporter insensitive to DTT treatment).

Our experiments showed no detectable changes in the fluorescent properties of UAS-Sec61β:roGFP following 30 min 10mM DTT treatment compared to DMSO vehicle control, including no increase in 405-nm excitation fluorescence or changes in 488nm/405nm excitation ratios. These results suggest that either the roGFP sensor requires further optimization for sensitivity in this cellular system or that additional controls and calibration steps are needed to establish the dynamic range of the assay. We believe this experiment falls beyond the scope of the current study, given the extensive optimization required. However, it represents an important future direction for testing membrane fragmentation as a mechanism underlying the phenotypes observed in Atlastin mutants. The possibility of ER integrity defects is mentioned in the discussion on lines 547-559.

Minor comments:

1. It is important to call figures by order. Figure 2C is called before 2A-B. Figure 2B is called before Figure 2A.

The revised manuscript has all figures in order of appearance in the text.

Figure legends (Figure 2): "The same control dataset used in E-G was used in Figure 5 and Figure 5_Supplement." Why is this relevant?

We wanted to be transparent about reusing the same control dataset across multiple figures to avoid any appearance of data duplication. This notation clarifies that, although the data appear in different contexts (Figures 2 and 5. This version does not contain a Figure 5_Supplement), it represents the same biological samples analyzed for different parameters, ensuring readers understand that these are not independent datasets.

Figure 4F is called before Figure-4D-E which are not called.

We revised our manuscript and reorganized Figure 4 to ensure that all figure panels are referenced in sequential order and that panels 4D-E, which were previously not cited in the text, are now properly referenced when discussing their corresponding results.

Figure 5B is called before the previous ones. Same for Figure 5A supplement.

We referenced Figure 5A in lines 211-212, which precedes our discussion of Figure 5B. To clarify the figure order, we removed the early references to Figures 2D-G and Movies 7-14, which were mentioned only to indicate that we were analyzing the same dataset in different ways.

The revised manuscript has all figures in order of appearance in the text.

Referees cross-commenting

I agree with the comments raised by reviewer2 and 3. Basically it is highly important to validate those data by genetic rescue. Moreover, it is essential to know the source of the displaced luminal marker to the cytosol. Is it mislocalization or it is a reflux of pre-existing protein to the cytosol after insertion to the ER. It is also recommended by me and the reviewers and me to test the endogenous protein rather than overexpression.

We have addressed these points in our responses to the following reviewer questions:

• Genetic rescue: Please see our responses to Reviewer 1/Question #10 and Reviewer 2/Question #1.
• Source of displaced luminal marker: We provide some evidence addressing this in our response to Reviewer 3/Question #1.
• Endogenous protein localization: We have examined this and detailed our findings in our responses to Reviewer 1/Question #7 and Reviewer 2/Question #6.

  Reviewer #1 (Significance (Required)):

General assessment: This interesting paper shows that proteins can escape the ER under special conditions. However, the authors need more evidence to show that and rely less on the overexpression system, especially of BIP-GFP, which can cause proteostasis stress within the ER. Advance: The results have been oversimplified in their explanations, and some points and complexities of the study need to be addressed further to make the most of them. These are often some of the more interesting concepts in the paper. I think many points can be addressed in the text by the authors being clear and concise with their reporting. At the same time, other experiments would turn this paper from an observational one into a very interesting mechanistic one. This paper is based on previously published articles from the group and other groups, and it is a nice progression. However, as mentioned, this paper depends primarily on published data, and the novelty is somehow lost between all the comparisons to other published data instead of emphasizing that. Without a substantial mechanistic improvement, the paper would remain observatory.

Audience: The microscopy tools can be great addition to researchers in the field to monitor protein trafficking especially Cell biologists (basic research)

My expertise: ER homeostasis, protein trafficking, cell biology

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

Summary The endoplasmic reticulum (ER) is a continuous organelle that extends throughout neurons to regulate fundamental processes. The analysis of ER dynamics at synaptic terminals is limited by the challenge of imaging these structures at high resolution. In this manuscript, the authors use super-resolution (~170 nm) live imaging and a combination of membrane and luminal ER markers at the Drosophila larval NMJ, an important model synapse, to investigate dynamic ER architecture in vivo. They report a detailed characterization of the presynaptic ER organization and dynamics at wild-type and GTPase Atlastin mutant NMJs. Their analysis using the ER membrane marker tdTomato:Sec61b reveals the presence of an intact ER network in Atlastin mutants. This contrasts with the apparent ER fragmentation phenotype previously reported and replicated here when using a luminal marker. Their findings instead point to the progressive displacement of luminal proteins to the cytosol in Atlastin mutants specifically at synapses. The authors propose that the disruption of ER protein dynamics at synapses is a compartment-specific ER stress response. The manuscript is well written, results are clearly presented, and experiments are technically rigorous.

Major comments

1. The baseline ER phenotypes in Atlastin mutants are mild with complete loss of ER network only observed in terminal boutons. This interesting and unexpected result should be further confirmed by genetic rescue. The authors can use a UAS rescue line previously reported in PMID: 19341724.

We tested the UAS-Atl-myc rescue line and unfortunately found that even in wild-type neurons, overexpression of Atlastin produced strong ER organization defects that precluded the rescue experiment. Instead, to confirm the cell autonomy of the phenotype and to test it wth an independent tool, we performed a presynaptic knockdown of Atlastin by RNAi and found that BiP:sfGFP:HDEL is displaced, as observed in the Atlastin null mutant. These results are in now shown in Figure 7A-C.

Lines 204-7: It's not clear how a greater coefficient of variation indicates that the marker is more concentrated in subsynaptic structures or what is meant by 'subsynaptic structures.'

We added the following text to explain, in lines 181-183: "A higher CoV indicates an uneven distribution of tdTomato:Sec61β within the presynaptic terminal, with some areas showing higher concentrations than others (in contrast to the uniform, diffuse signal expected from fragmentation)." To avoid confusion with postsynaptic structures called the subsynaptic reticulum, we have removed the term "subsynaptic". The intended meaning is distinct structures found within the presynaptic terminal.

There's a mistake in Figure 6C and the associated text. The summed percentage of the three phenotypic categories adds up to 110% for Atlastin mutants. *

The reviewer noted that the summed percentage of the three phenotypic categories in Figure 6C adds up to 110% for Atlastin mutants, which appears to be a mathematical error. However, this is not an error, but rather a reflection of our quantification methodology, in which a single bouton can exhibit more than one type of ER dynamics per movie recorded. Our quantification counts each phenotype independently, so boutons displaying multiple phenotypes contribute to more than one category. This approach provides a more comprehensive view of the range of ER dynamics present in Atlastin mutants, as restricting the analysis to mutually exclusive categories would underrepresent the complexity of the phenotypes observed. To make this point clear, we made the following change to the text in lines 257-259: "We note that the sum of these percentages exceeds 100% because one NMJ exhibited multiple phenotypes: one branch had a complete loss, while the other branch had no phenotype. These phenotypes were counted separately."

Figure 8: the ER looks fragmented in 1st instar controls and mutants. The authors should address this difference from more mature NMJs.

We would like to clarify that the bulk of experiments in this manuscript (including all ER dynamics, luminal marker redistribution, and membrane marker analyses discussed throughout the Results) were performed in 3rd instar larvae, which are more mature larval NMJ preparations standard in the field. Figure 8 was included specifically to test whether the Atlastin mutant phenotype we describe throughout the paper is also detectable at an earlier developmental stage, not to replace or reinterpret our primary findings.

Regarding the specific observation that the ER appears more fragmented in Figure 7F-H relative to the more mature NMJs shown elsewhere: this fragmentation, observed similarly in both control and Atlastin mutant 1st instar larvae, likely reflects technical challenges associated with dissecting these smaller, more delicate early-stage specimens rather than a genotype-specific effect. Because fragmentation occurred similarly in both genotypes, we could still reliably assess the redistribution of BiP:sfGFP:HDEL as our primary phenotypic readout in this experiment. We have added the following text (lines 306-309) to clarify this point: "Note that in 1st instar larvae, both normal networks in controls and residual networks in Atlastin mutants appeared more fragmented than in 3rd instar preparations, likely due to the technical challenges of dissecting these smaller, more delicate specimens. Since ER fragmentation occurred similarly in both genotypes, we could still reliably assess the redistribution of BiP:sfGFP:HDEL as our primary phenotypic readout.

The images in figure 9B do not seem representative of the quantification in Figure 9D. Specifically, the partial loss Atlastin NMJ appears to have recovered as fully as the complete loss Atlastin NMJ.

The images showed FRAP recovery across the entire bouton, but we photobleached only a small region within each bouton and quantified only this region. We have now added outlines to clearly delineate the specific FRAP regions that were analyzed in each image, which clarify that the partial loss Atlastin showed less recovery than the overall bouton. We have also reordered the figures to more clearly convey our message (Figure 9 is now Figure 8).

We also made a few changes to the paragraph on lines 347-350 to clarify our experimental reasoning: "We photobleached en passant boutons using a defined region of 6.8 x 7.8 microns (dashed box in Figure 8D) to ensure that BiP:sfGFP:HDEL could recover from the ER networks surrounding the FRAP region (Movies S20-S23)."

We also added this sentence to the figure legends of Figure 8: "The dashed boxes in (D) indicate areas that were photobleached and analyzed for recovery quantification in (E-F)."

Optional: An overexpressed luminal marker is displaced to the cytoplasm in Atlastin mutants. It would be interesting to know and increase the significance of the findings if the same is true of endogenous luminal proteins under biological stress conditions.

As noted in our response to Reviewer #1 suggested that Atlastin mutant synapses may exhibit ER stress. To address this, we examined levels of the ER chaperone BiP, a well-established ER stress marker whose expression increases during UPR activation. We first validated that our BiP antibody can detect changes in ER stress by feeding control larvae with 50mM DTT for 24 hours. We were unable to perform this experiment in Atlastin mutant larvae because they did not consume the DTT-treated food, as assessed by blue food coloring in the larvae's guts. These results are in Figure 10A. In the future, it will be of interest to establish a protocol to examine Atlastin mutants by feeding or treating larval fillets with DTT.

We measured BiP levels at NMJs of Atlastin mutants and found they were slightly increased compared to controls. Atlastin mutants co-expressing UAS-BiP:sfGFP:HDEL or UAS-tdTomato:Sec61b did not show significantly increased endogenous BiP levels, suggesting that transgene expression suppresses the mild ER stress response. We conclude from these experiments that Atlastin mutant synapses have mild ER stress. These results are in Figure 10B-E).

Optional: Applying this approach in stimulated conditions (high potassium, increased temperature) might reveal a greater activity-dependent role for Atlastin at synaptic terminals.

This is a very interesting idea, as we have only examined synapses at rest. However, this is beyond the scope of this paper.

Minor Comments

1. Line 16: Atlastin should be italicized.

Thank you for catching this typo. We have fixed it.

Figure 5A: Based on the relative intensities, it appears that control and mutant images are not contrast matched but this isn't stated.

Thank you for catching this omission. We added to the figure legend: "Control and Atlastin mutant images are not contrast matched."

Line 822: The number of static Atlastin mutant boutons used for analysis is missing.

Thank you for catching this omission. We have fixed this supplementary table.

Figure 9: The blue arrows are not annotated in the figure legend.

Thank you for catching this omission. We have fixed this figure legend.

Reviewer #2 (Significance (Required)):

Atlastin is linked to Hereditary Spastic Paraplegia (HSP) and this study changes our understanding of the compartment-specific impacts of its loss. This study reveals the importance of using both membrane and luminal ER markers to accurately interpret phenotypes as well as the importance of considering compartment-specific effects on ER. These findings represent significant mechanistic and conceptual advances. The lack of genetic rescue is a limitation and adding an investigation of an endogenous luminal protein under basal and stress conditions would add significantly to our understanding of Atlastin dysfunction in HSP. Notably, the in vivo imaging approach introduced here can be adapted broadly for live imaging of Drosophila larvae. Thus, this work will be of interest to both neuronal cell biologists and the wider Drosophila community. This review is based on our expertise in neuronal cell biology.

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

In this manuscript, the authors investigate the structural dynamics of the endoplasmic reticulum (ER) in Drosophila neurons and examine the role of the ER-shaping protein Atlastin in ER morphology. Their discovery on the neuromuscular junction (NMJ)-specific contribution of Atlastin to ER integrity is intriguing and may provide valuable insights into the pathological mechanisms underlying Atlastin mutations associated with hereditary spastic paraplegia (HSP) and hereditary sensory neuropathy. The key observation on ER protein showing an aberrant cytoplasmic localisation in mutant cells appears convincing. Though this phenomenon's characterisation stays at the point of primary observation with its mechanics unclarified, establishing this new and unexpected functional rather than structural Atl effect is important and useful for the field. The observation that ER is structurally preserved in this mutant with absolute lack of Atl are also extremely useful.

It is unclear if the cytoplasmic localisation affects an exogenous overexpressed ER marker or endogenous protein would also appear in cytoplams, the authors should consider adding an immunostaining data to test that.

Authors offer speculations on potential reasons for the cyto localisation of the ER marker suggesting that relocation at the cell periphery specifically combined with slow clearance there is the most likely explanation (still unclear what stops the marker from spreading through the entire cell). They suggest that decrease in cotranslational translocation is unlikely as this would result in somatic accumulation of the marker. However, if the clearance in the periphery is less efficient than in soma, the accumulation there might reflect a compromised translocation. Any clarifying experiments, if practical, to directly demonstrate how ER proteins in relocates to the cytoplasm in atl mutant would help understanding better the phenomenon. For example, would proteasomal inhibition make the marker accumulate more across the cell? Authors also suggest links to ER stress. Would stress induction phenocopy the mutant?

Reviewer #3 asked whether defective proteasomal clearance underlies the cytosolic accumulation of BiP:sfGFP:HDEL in Atlastin mutants. We addressed this directly. First, proteasome function appears intact in the mutants: baseline ubiquitinated protein levels (FK1 antibody) were comparable between control and Atlastin mutants, and MG132 treatment produced a similar increase in ubiquitination in both genotypes, confirming both antibody specificity and normal proteasome activity. We then examined BiP:sfGFP:HDEL directly. In controls, MG132 caused the marker to accumulate at axons and presynaptic terminals, showing that it is normally cleared from these compartments by the proteasome. Critically, this accumulated marker remained associated with intact ER networks: MG132 did not induce diffuse cytosolic BiP:sfGFP:HDEL in any compartment (cell bodies, axons, or presynaptic terminals), even where levels rose substantially. Thus, blocking proteasomal clearance raises ER-localized marker but does not generate the cytosolic pool seen in Atlastin mutants, indicating that impaired clearance is not sufficient to cause the displacement phenotype. We separately noted that BiP:sfGFP:HDEL was already elevated in Atlastin mutant axons without MG132, paralleling the axonal tdTomato:Sec61β accumulation in Figure 4, consistent with reduced baseline clearance specifically in mutant axons, but this does not lead to cytosolic displacement. This experiment is now shown in Figure 11, described in Results (lines 445-475), and discussed in lines 576-581.

Minor comments:

Line 146:

"fast dynamics (Thank you for catching this mistake. We have corrected it.

Fig. 2D: The data representation of "Tubule displacement" image is unclear. The ER tubule indicated by the red arrow does not seem to show any changes over time (like static). time 0 in stamp appears behind the image.

Thank you for catching the typo. We have fixed it. Additionally, we added black arrows to highlight a tubule that is not moving, allowing the reader to compare it with the moving tubule. We also included a video of all types of ER tubule dynamics to ensure the reader can also look at the raw data (Movies S9-11).

• • Line 157-158 (and relevant method sections):

The definition of static and dynamic boutons is ambiguous. The author should describe in more detail this point including how long they observed the structure to define the changes in ER tubule dynamics.

We provide in the methods (lines 779-791) a detailed explanation of how we categorized boutons as dynamic or static. In addition, we added the following to explain in the results section how we defined static vs dynamic:

Old sentence: We qualitatively categorized boutons as "static" if we observed no change in ER network structure or "dynamic" if we observed at least one change.

New sentence in lines 143-147: "We imaged boutons for 40 sec at 0.92 sec intervals to capture ER dynamics over this observation period. Boutons were qualitatively categorized as "static" if we observed no detectable changes in ER network structure throughout the entire 40 sec imaging session, or "dynamic" if we observed at least one of the three defined dynamic events during this time window."

Fig. 2E: What n=75 and n=29 represent is unclear, are these the number of boutons in en passant and terminal subjected for qualitative analysis?

We removed these n values from the figure and added this information to the Supplementary Table 1, which contains detailed information about the genotype, statistical analysis, and number of larvae and NMJs analyzed.

Fig. 2: What the qualitative analysis represents is unclear, are the points pulled from different experiments?

The data in Fig. 2 E-F comes from movies acquired in the same experiment. The number of independent animals and NMJs imaged is described in Table 1.

* *Line 231: Regarding "...we found a small but significant reduction in dynamic boutons in Atlastin mutants (76%), ...", how do the authors assess significance. If proportion of static/dynamic ER in boutons was obtained from multiple experiments, it should be presented e.g. as in average {plus minus} standard deviation, or clarify that the proportion is representative of x independent experiments.

The videos used for this figure were acquired from a single experiment. We use a chi-square test to determine significance relative to the "expected" distribution of dynamics types from controls, as these are categorical rather than continuous data (see PMID 31145670). Information regarding genotype, statistical analysis and number of larvae and NMJs can also be found in Supplementary Table 1.

Line 267-269 and Fig. 6B: The author's conclusion that "Complete loss of ER network structure in NMJ of BiP:sfGFP:HDEL overexpressing Atl mutant" seem to be based on the lack of signal from luminal marker, which may be undetectable due to changes to tubular volume or marker loss to the cytoplasm, as suggested by the authors, while the membranous ER structure is intact. It would be useful to discuss this point and potentially add ER membrane-stained control.

We agree with the reviewer that Atlastin mutants categorized as 'complete loss mutants' do not actually lack ER at synapses. We think this is an important point so we added the following to the results in lines 251-254: "Note that the "Complete loss" phenotype in Atlastin mutants reflects the absence of detectable luminal marker signal in organized ER structures, not the complete absence of ER membranes, as demonstrated by our ER membrane marker tdTomato:Sec61β results."

We attempted to co-label the ER membrane and ER lumen, but these crosses yielded very few live larvae (in either controls or Atlastin mutants, and those that survived had severely deformed NMJs. We added Figure 6-Supplement showing the results of this experiment, and described them on lines 270-273.

Fig. 6C: In Atl mutant, why does the total of the proportion exceed 100% (10 + 45 + 55)?

The reviewer noted that the summed percentage of the three phenotypic categories in Figure 6C adds up to 110% for Atlastin mutants. This is not an error, but rather a reflection of our quantification methodology because a single bouton can exhibit more than one type of ER dynamics per movie recorded. Our quantification counts each phenotype independently, so boutons displaying multiple phenotypes contribute to more than one category. This approach provides a more comprehensive view of the range of ER dynamics present in Atlastin mutants, as restricting the analysis to mutually exclusive categories would underrepresent the complexity of the phenotypes observed. To make this point clear, we made the following change to the text in lines 257-259: "We note that the sum of these percentages exceeds 100% because one NMJ exhibited multiple phenotypes: one branch had a complete loss, while the other branch had no phenotype. These phenotypes were counted separately."

Fig. 9C, line 342-344: In FRAP experiment using CD8, it seems that the Partial loss Atl mutant shows slower recovery that control. There seems to be a mismatch in triangle symbols of Partial loss Atl mutant between legend and plot (one is filled and the other is empty). This should be clarified.

Thank you for catching this mistake. We have fixed the figure.

fig. 10 is a clever way to verify the cytoplasmic localization of the ER marker; however, its description and annotation can be improved, and it would be stronger if 4 curves in F for mutant and controls with the trap and normal were shown.

The reviewer suggested merging our graphs but we believe that keeping them separate is clearer.

Line 495: Drosophila have ReepA and ReepB, but not Reep1-4. If the authors discuss their speculation based on their observation (using Drosophila), the gene names should be unified in the same species, and explain the corresponding genes to mammalian cells.

We made the following changes to address the reviewer's concern about gene nomenclature consistency (lines 502-506): "These ER-derived vesicles are likely to involve ReepA and ReepB, the Drosophila orthologs of mammalian REEP1-4, which regulate ER vesicle formation in mammalian cells (67). Notably, while overexpression of Atlastin can regulate REEP vesicle fusion in mammalian systems (67), it is not essential for vesicle formation, suggesting similar regulatory relationships may exist between Atlastin and Reep genes in Drosophila."

Line 548; should UPR be Unfolded Protein Response?

Thank you for catching the typo. We have fixed it.

Reviewer #3 (Significance (Required)):

This study advances the understanding of how ER morphogens affect neuronal cells specifically, the lack of which limits researchers ability to comprehend the neuronal pathologies associated with ER structure-function. The observation on ER content aberrant localisation caused by the lack of key structural protein should be of a great interest for cell and neuronal biologists and researchers of the associated diseases and shows the field a new direction. Though, mechanistic details remain to be unraveled, it constitutes a fundamental, conceptual advance.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors investigate the structural dynamics of the endoplasmic reticulum (ER) in Drosophila neurons and examine the role of the ER-shaping protein Atlastin in ER morphology. Their discovery on the neuromuscular junction (NMJ)-specific contribution of Atlastin to ER integrity is intriguing and may provide valuable insights into the pathological mechanisms underlying Atlastin mutations associated with hereditary spastic paraplegia (HSP) and hereditary sensory neuropathy. The key observation on ER protein showing an aberrant cytoplasmic localisation in mutant cells appears convincing. Though this phenomenon's characterisation stays at the point of primary observation with its mechanics unclarified, establishing this new and unexpected functional rather than structural Atl effect is important and useful for the field. The observation that ER is structurally preserved in this mutant with absolute lack of Atl are also extremely useful.

It is unclear if the cytoplasmic localisation affects an exogenous overexpressed ER marker or endogenous protein would also appear in cytoplams, the authors should consider adding an immunostaining data to test that.

Authors offer speculations on potential reasons for the cyto localisation of the ER marker suggesting that relocation at the cell periphery specifically combined with slow clearance there is the most likely explanation (still unclear what stops the marker from spreading through the entire cell). They suggest that decrease in cotranslational translocation is unlikely as this would result in somatic accumulation of the marker. However, if the clearance in the periphery is less efficient than in soma, the accumulation there might reflect a compromised translocation. Any clarifying experiments, if practical, to directly demonstrate how ER proteins in relocates to the cytoplasm in atl mutant would help understanding better the phenomenon. For example, would proteasomal inhibition make the marker accumulate more across the cell? Authors also suggest links to ER stress. Would stress induction phenocopy the mutant?

Minor comments:

Line 146: "fast dynamics (<1 sec)" a velocity should be presented as distance/time

Fig. 2D: The data representation of "Tubule displacement" image is unclear. The ER tubule indicated by the red arrow does not seem to show any changes over time (like static). time 0 in stamp appears behind the image.

Line 157-158 (and relevant method sections): The definition of static and dynamic boutons is ambiguous. The author should describe in more detail this point including how long they observed the structure to define the changes in ER tubule dynamics.

Fig. 2E: What n=75 and n=29 represent is unclear, are these the number of boutons in en passant and terminal subjected for qualitative analysis?

Fig. 2: What the qualitative analysis represents is unclear, are the points pulled from different experiments?

Line 231: Regarding "...we found a small but significant reduction in dynamic boutons in Atlastin mutants (76%), ...", how do the authors assess significance. If proportion of static/dynamic ER in boutons was obtained from multiple experiments, it should be presented e.g. as in average {plus minus} standard deviation, or clarify that the proportion is representative of x independent experiments.

Line 267-269 and Fig. 6B: The author's conclusion that "Complete loss of ER network structure in NMJ of BiP:sfGFP:HDEL overexpressing Atl mutant" seem to be based on the lack of signal from luminal marker, which may be undetectable due to changes to tubular volume or marker loss to the cytoplasm, as suggested by the authors, while the membranous ER structure is intact. It would be useful to discuss this point and potentially add ER membrane-stained control.

Fig. 6C: In Atl mutant, why does the total of the proportion exceed 100% (10 + 45 + 55)?

Fig. 9C, line 342-344: In FRAP experiment using CD8, it seems that the Partial loss Atl mutant shows slower recovery that control. There seems to be a mismatch in triangle symbols of Partial loss Atl mutant between legend and plot (one is filled and the other is empty). This should be clarified

fig. 10 is a clever way to verify the cytoplasmic localisatoin of the ER marker, however its description and annotation can be improved, and it would be stronger if 4 curves in F for mutant and controls with the trap and normal were shown.

Line 495: Drosophila have ReepA and ReepB, but not Reep1-4. If the authors discuss their speculation based on their observation (using Drosophila), the gene names should be unified in the same species, and explain the corresponding genes to mammalian cells.

Line 548; should UPR be Unfolded Protein Response?

Significance

This study advances the understanding of how ER morphogens affect neuronal cells specifically, the lack of which limits researchers ability to comprehend the neuronal pathologies associated with ER structure-function. The observation on ER content aberrant localisation caused by the lack of key structural protein should be of a great interest for cell and neuronal biologists and researchers of the associated diseases and shows the field a new direction. Though, mechanistic details remain to be unraveled, it constitutes a fundamental, conceptual advance.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary

The endoplasmic reticulum (ER) is a continuous organelle that extends throughout neurons to regulate fundamental processes. The analysis of ER dynamics at synaptic terminals is limited by the challenge of imaging these structures at high resolution. In this manuscript, the authors use super-resolution (~170 nm) live imaging and a combination of membrane and luminal ER markers at the Drosophila larval NMJ, an important model synapse, to investigate dynamic ER architecture in vivo. They report a detailed characterization of the presynaptic ER organization and dynamics at wild-type and GTPase Atlastin mutant NMJs. Their analysis using the ER membrane marker tdTomato:Sec61b reveals the presence of an intact ER network in Atlastin mutants. This contrasts with the apparent ER fragmentation phenotype previously reported and replicated here when using a luminal marker. Their findings instead point to the progressive displacement of luminal proteins to the cytosol in Atlastin mutants specifically at synapses. The authors propose that the disruption of ER protein dynamics at synapses is a compartment-specific ER stress response. The manuscript is well written, results are clearly presented, and experiments are technically rigorous.

Major comments

1. The baseline ER phenotypes in Atlastin mutants are mild with complete loss of ER network only observed in terminal boutons. This interesting and unexpected result should be further confirmed by genetic rescue. The authors can use a UAS rescue line previously reported in PMID: 19341724.
2. Lines 204-7: It's not clear how a greater coefficient of variation indicates that the marker is more concentrated in subsynaptic structures or what is meant by 'subsynaptic structures.'
3. There's a mistake in Figure 6C and the associated text. The summed percentage of the three phenotypic categories adds up to 110% for Atlastin mutants.
4. Figure 8: the ER looks fragmented in 1st instar controls and mutants. The authors should address this difference from more mature NMJs.
5. The images in figure 9B do not seem representative of the quantification in Figure 9D. Specifically, the partial loss Atlastin NMJ appears to have recovered as fully as the complete loss Atlastin NMJ.
6. Optional: An overexpressed luminal marker is displaced to the cytoplasm in Atlastin mutants. It would be interesting to know and increase the significance of the findings if the same is true of endogenous luminal proteins under biological stress conditions.
7. Optional: Applying this approach in stimulated conditions (high potassium, increased temperature) might reveal a greater activity-dependent role for Atlastin at synaptic terminals.

Minor Comments

1. Line 16: Atlastin should be italicized.
2. Figure 5A: Based on the relative intensities, it appears that control and mutant images are not contrast matched but this isn't stated.
3. Line 822: The number of static Atlastin mutant boutons used for analysis is missing.
4. Figure 9: The blue arrows are not annotated in the figure legend.

Significance

Atlastin is linked to Hereditary Spastic Paraplegia (HSP) and this study changes our understanding of the compartment-specific impacts of its loss. This study reveals the importance of using both membrane and luminal ER markers to accurately interpret phenotypes as well as the importance of considering compartment-specific effects on ER. These findings represent significant mechanistic and conceptual advances. The lack of genetic rescue is a limitation and adding an investigation of an endogenous luminal protein under basal and stress conditions would add significantly to our understanding of Atlastin dysfunction in HSP. Notably, the in vivo imaging approach introduced here can be adapted broadly for live imaging of Drosophila larvae. Thus, this work will be of interest to both neuronal cell biologists and the wider Drosophila community. This review is based on our expertise in neuronal cell biology.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

In the present manuscript, the authors address an important question related to the ultrastructure and the dynamics of the ER in HSP. In contrast to previous studies, the authors here show (by using a membrane and luminal protein markers) that in the presynaptic terminals, the overexpressed BIP "mislocalizes" to the cytosol without affecting (or with minimal effect) the integrity of the ER membrane. Although they used an artificial system by overexpressing (overexpression) of BIP-sfGFP-HDEL (fused protein), the findings lack validation of the endogenous protein by biochemical and fluorescent tools.

Concerns:

I am worried about how the article is presented, mainly in the results section, as most of it refers to published data. The Results section is reserved for presenting new findings without external interpretation or comparison. The paper is written mainly as a comparison paper with other studies or relies on previous studies to strengthen their findings rather than coming up with novel findings. Up to figure 4, I missed the relevance of the new findings. The manuscript needs rewriting to emphasize its novelty and significance without comparing it to previous data. Moreover, the manuscript emphasizes the technology and the findings of the localization of the ER luminal proteins to the cytosol (which is not novel and was previously reported in other settings). Those two aspects were not given enough focus. Here are the main major and minor comments:

Major comments:

1. Lines 103-116 (first paragraph of the results section) describe mainly published data that is more suitable for the introduction section. It is annoying to refer to different published articles in the Results section to strengthen the results instead of showing them. The same goes for paragraphs two and three. Why mention those data in the Results section if they are already published and known?
2. Figure Legends-(in all Figures): The number of experimental repeats must be mentioned in the figure legends.
3. The way the figures are labeled is worrisome; supplementary figures are not ordered numerically.
4. The tubule extension in Figure 2D is not convincing. Is there a movie showing those changes? Better images are needed. It is essential to show which supplemental movie corresponds to which panel.
5. This is unnecessary in the results section: "To investigate the relationship between ER structure and function at synapses, we examined mutants of Atlastin, a GTPase that regulates ER tubule fusion. Drosophila has a single homolog while mammals have three Atlastin homologs, with Atlastin-1 enriched in the brain (Rismanchi et al., 2008)."
6. "This reduction in ER membrane marker intensity has also been observed in other HSP mutants, suggesting this is a common feature of ER shaping mutants and could indicate changes in ER membrane composition, integrity, or tubule thickness (P.rez-Moreno et al., 2023)." This comparison is important and should be shown in the same settings as for the Atlastin mutant rather than referring to published data.
7. Does the distribution of the luminal ER marker in Figure 6F diffuse due to mislocalization or reflux after being localized to the ER and then refluxed to the cytosol as was previously shown for the ER to Cytosol signaling (ERCYS) mechanism? Could you assess other ER-luminal protein localization biochemically? It is highly recommended to look at another soluble ER-protein localization in the Atlastin mutant without overexpression, which can be an artifact
8. "(data not shown)" in line 288. This affects the process of judging those data.
9. In comparison to Summerville et al. (2016) in Figure 7, the experiment was not done in the same way. It is important to keep the same settings for comparison
10. Does the Atlastin mutant induce the unfolded protein response and stress within the ER? It is necessary to look for UPR markers in those settings. It was shown previously that ER stress leads to protein reflux from the ER to the cytosol. Is there a difference in the ER stress markers in the presynaptic terminal?
11. It is important to add biochemical experiments to show that no fragmentation of the ER membrane occurred. It can be simply demonstrated by looking at the redox state of the ER, which would change if it were mixed with the reducing cytosol. Moreover, this can be shown by using an ER-targeted redox-sensitive fluorescent protein that is tethered to the ER membrane to follow changes in the redox state of the ER.

Minor comments:

1. It is important to call figures by order. Figure 2C is called before 2A-B. Figure 2B is called before Figure 2A.
2. Figure legends (Figure 2): "The same control dataset used in E-G was used in Figure 5 and Figure 5_Supplement." Why is this relevant?
3. Figure 4F is called before Figure-4D-E which are not called.
4. Figure 5B is called before the previous ones. Same for Figure 5A supplement.

Referees cross-commenting

I agree with the comments raised by reviewer2 and 3. Basically it is highly important to validate those data by genetic rescue. Moreover, it is essential to know the source of the displaced luminal marker to the cytosol. Is it mislocalization or it is a reflux of pre-existing protein to the cytosol after insertion to the ER. It is also recommended by me and the reviewers to test the endogenous protein rather than overexpression.

Significance

General assessment: This interesting paper shows that proteins can escape the ER under special conditions. However, the authors need more evidence to show that and rely less on the overexpression system, especially of BIP-GFP, which can cause proteostasis stress within the ER.

Advance: The results have been oversimplified in their explanations, and some points and complexities of the study need to be addressed further to make the most of them. These are often some of the more interesting concepts in the paper. I think many points can be addressed in the text by the authors being clear and concise with their reporting. At the same time, other experiments would turn this paper from an observational one into a very interesting mechanistic one. This paper is based on previously published articles from the group and other groups, and it is a nice progression. However, as mentioned, this paper depends primarily on published data, and the novelty is somehow lost between all the comparisons to other published data instead of emphasizing that. Without a substantial mechanistic improvement, the paper would remain observatory.

Audience: The microscopy tools can be great addition to researchers in the field to monitor protein trafficking especially Cell biologists (basic research)

My expertise: ER homeostasis, protein trafficking, cell biology

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Reply to the reviewers

1. __ General Statements__ We thank the reviewers for their thoughtful and constructive evaluations of our work. We are particularly encouraged that both recognize the value of this study as a scalable and systematic framework for the functional exploration of the human KZFP family and agree that the resource generated here will be of broad interest to the KZFP, transposable element, and genome regulation communities. Reviewer 1 explicitly notes that "the screening framework itself represents a potentially useful resource for prioritizing candidate KZFPs for downstream study" and that "the study may nonetheless serve as a useful starting point for future investigations into KZFP biology and transcriptional regulation." Reviewer 2 similarly emphasizes that "the authors provide an efficient and valuable screening platform that can identify promising candidates for further investigation" and that "the methodological advance represents the primary contribution of the work."

We can only concur with these assessments. The principal goal of this study was not to elucidate the physiological roles of all or even a subset of individual KZFPs, but rather to provide a scalable framework that enables their systematic prioritization and generates experimentally testable hypotheses regarding their functions. To support our argument, we ventured into some mechanistic analyses, but these could not pretend to be complete and definitive. In that respect, we hear the reviewers when they note that the original manuscript does not always sufficiently distinguish candidate discovery from mechanistic validation. In its revised version, we will therefore more clearly frame the inducible K562 overexpression assay as a standardized and sensitive readout of regulatory potency rather than as a direct surrogate of physiological function. Within this framework, K562 fitness defects are interpreted as a quantitative measure of the extent to which ectopic KZFP expression perturbs transcriptional homeostasis in a controlled cellular context, while the direct targets and transcriptional networks identified through our integrative analyses are presented as hypotheses to be tested in more physiologically relevant systems. Accordingly, the revised manuscript preserves the broad scope and resource aspect of the study while incorporating additional experimental validation, expanded methodological descriptions, and a more cautious interpretation of the proposed biological functions of the selected KZFPs.

__Although this document is submitted as a Revision Plan, we have already incorporated a substantial number of revisions into the transferred manuscript. In particular, we have implemented most of the presentation, methodological, and conceptual modifications requested by the reviewers, including clarification of the scope of the study, extensive revisions of the Results and Discussion, expanded Materials and Methods, and numerous figure and text corrections. These revisions are detailed in Section 3 ("Description of the revisions that have already been incorporated into the transferred manuscript"). __

The remaining points requiring additional experimentation or more extensive analyses are described in Section 2 ("Description of the planned revisions").

__ Description of the planned revisions__

Reviewer 1 Major comment 1

“Finally, several aspects of the data presentation are currently difficult to reconcile. In Fig. 1D, the meaning of the purple category is unclear, and the percentage scaling on the x-axis is difficult to reconcile with the cumulative values displayed. For instance, the sum of all the bars would not reach 100%, as the values of the bars span percentages up to 4% at most (for 105 MYO KZFPs) according to this plot. Similarly, the reported numbers of TE-binding KZFPs in Fig. 1E-F and Fig. S1D appear internally inconsistent and should be clarified. Specifically, 53+14=67 KZFPs are reported to bind TEs in total, yet a larger number of KZFPs appears associated with individual TE families (e.g., 86 for LTR.ERV1). If the values shown correspond to percentages rather than absolute counts, this should be explicitly clarified in both the figure and legend. In addition, Fig. S1D appears inconsistent with the counts reported in Fig. 1E-F, as only 5 out of the 53 toxic KZFPs displayed in the plot show no enrichment for any of the highlighted TE families.”

We thank the reviewer for this insightful comment, which has helped us identify areas where the presentation of our data can be substantially improved. We agree that the current presentation of the TE-binding analyses could be clearer and that revising these figures will improve both their readability and the overall consistency of the manuscript. In the revised manuscript, we will clarify the apparent inconsistencies in the presentation of the TE-binding KZFP analyses and revise the corresponding figures and legends accordingly. Importantly, these inconsistencies do not arise from errors in the underlying data but rather from an insufficient explanation of the statistical enrichment analyses and the way the results are represented. We will therefore redesign the relevant figures and expand their legends to more clearly describe the analytical approach, the enrichment criteria, and the interpretation of the results. We believe that these revisions will improve the clarity, transparency, and internal consistency of the manuscript, allowing readers to more readily interpret the TE-binding analyses. Minor comments of the reviewer 1 were extremely useful to detect mistakes and we are grateful for that. All the modifications that were asked see below were included in the manuscript.

Reviewer 1 Major comment 2

“Finally, while the proteomics results aimed at identifying SCAN-dependent interactors are of interest, several aspects of the experimental design and data analysis remain unclear. In particular, it is not specified whether the experiment was performed in biological replicates or as a single measurement. This is important, as it directly affects how the data can be interpreted and how stringent downstream filtering can be. In the Results section, the authors state that "we identified a set of SCAN-dependent interactors, i.e., proteins that co-immunoprecipitated with the full-length construct but were absent in controls and lost upon deletion of the SCAN domain," which suggests a relatively binary, "presence/absence" filtering strategy. However, this description does not specify whether any quantitative threshold (e.g., enrichment ratio) was applied when comparing full-length constructs to deletion mutants. In contrast, the Methods section states that "proteins lacking signal above background were excluded and proteins were additionally required to show stronger signal in at least one bait condition than in GFP controls based on heatmap clustering (see script)," which instead suggests that a threshold-based criterion was used to define enrichment relative to controls and deletion mutants. If this is the case, the exact criteria and thresholds used for filtering should be clearly stated and consistently reported between the Results and Methods sections. If replicate measurements were not performed, this should be explicitly acknowledged, as peptide-level variability may substantially influence the identification of high-confidence interactors, particularly if the applied cutoffs are not highly stringent.”

We agree that a more detailed description of the experimental design and analysis strategy, together with additional validation, will strengthen the interpretation of the proteomic data. In the revised manuscript, we expanded the Results and Materials and Methods sections to provide a clearer and more quantitative description of the filtering strategy, including the enrichment criteria and thresholds used to define SCAN-dependent interactors. To further strengthen these findings, we propose to perform an independent biological replicate of the co-immunoprecipitation mass spectrometry experiment. This additional experiment will increase confidence in the identified SCAN-dependent interactors and further support the conclusions drawn from the proteomic analysis.

Reviewer 1 Minor comments

• In Fig. 2A, readability could be improved by adjusting the layering of points, as the darker dots (in particular the red ones) are currently obscured by lighter ones. Alternatively, removing the outline of the points (which is not transparent) may also improve visibility, but in that case the legend for point size would need to be updated accordingly.

Thank you for this helpful suggestion. We will revise Figure 2A to improve its readability by reworking the layering of the points in accordance with the reviewer's recommendation. We will also evaluate the point outlines and, if appropriate, remove them and update the point-size legend accordingly to ensure the figure is clear and easy to interpret.

Reviewer 2 – Major comment

“- The authors looked at available chromatin data in either K562 cells or HEK293 cells, which I think is a very good way of utilizing publicly available data. Since the authors showed that different KZFPs might be functionally relevant in different cell types/tissues, I was wondering if they checked if there is available ChIP Seq or CUT&RUN data in those specific cell types/tissues. If yes, that data should be included in the manuscript.”

We agree that integrating KZFP binding data generated in biologically relevant cell types or tissues would further strengthen the proposed regulatory models. As described in the revised manuscript, we have already adopted this approach for ZNF43 by integrating chromatin landscape data from thymus and liver, where suitable datasets were available.

To further address this point, we propose to systematically explore publicly available ChIP-seq, CUT&RUN, CUT&Tag, and related chromatin profiling datasets for the other KZFPs investigated in this study. Where suitable datasets are available, these analyses will be incorporated into the revised manuscript to further support the proposed tissue-specific regulatory models and provide additional biological context for the identified target genes.

__ Description of the revisions that have already been incorporated in the transferred manuscript__

Reviewer 1 Major comment 1

“The large-scale overexpression screen represents the foundation of the manuscript and provides a potentially valuable resource for prioritizing candidate KZFPs for downstream study. However, several aspects of the experimental setup and data presentation currently limit the interpretation of the reported proliferation defects. First, key details regarding the screening workflow remain unclear. While the Methods section describes the overall procedure, it is difficult to determine when cells were seeded relative to doxycycline induction, in which plate format the cells were maintained throughout the experiment, and whether medium exchange was performed during the 9-day assay. These points are particularly relevant given the use of suspension K562 cells (which can complicate medium exchange in a 96-well plate format and make long-term culture more difficult to control) and a metabolic viability readout (PrestoBlue), as differences in nutrient depletion or overgrowth could also influence the signal independently of reduced proliferation or toxicity. Additional clarification regarding seeding density, timing of induction, plate format, culture handling throughout the assay, and whether cell morphology/density was visually monitored would substantially improve interpretability and reproducibility. Second, it is unclear whether the observed proliferation phenotypes may be influenced by differences in transgene expression levels or integration effects. Were all constructs validated for comparable expression following induction? In the absence of such controls, it remains difficult to determine whether the reported phenotypes reflect specific KZFP activities or differences in overexpression efficiency. While it may not be possible to conclusively distinguish KZFP-specific effects from toxicity associated with high transgene expression levels, this limitation should at least be acknowledged. In addition, the possibility that some phenotypes may be influenced by transgene integration effects should also be considered. Unless independent transductions were validated for the KZFPs classified as toxic, it remains difficult to exclude integration-site-specific contributions to the observed proliferation defects. Third, the normalization strategy would benefit from additional clarification. In Fig. S1A, the LacZ control appears variably affected by doxycycline treatment across plates, whereas the GFP control appears more stable. Since normalization relies on the mean behavior of both controls within each batch and condition, the authors should clarify whether this variability could influence hit calling.”

We agree that additional methodological details improve the clarity and reproducibility of the screening assay. Accordingly, we substantially expanded the Materials and Methods section to describe the experimental workflow, quality controls, data normalization, and hit-calling criteria. The revised paragraph is reproduced below.

Arrayed overexpression screen

To systematically assess the effect of human KZFP overexpression on cellular fitness, K562 cells were individually transduced with doxycycline-inducible lentiviral vectors encoding 366 human KZFPs. Lentiviral particles were produced as described above and used to transduce cells without MOI calculation. __Instead, a fixed volume of viral supernatant (200µL per × 104 cells in 48 well plate filled with 200ul of RPMI) was used for all transductions to ensure comparable experimental conditions. Transduced cells were selected with puromycin before doxycycline induction. Following puromycin selection (1µg/mL for 3 days), cells were seeded at 20 000 cells per well in 24-well plates filled with 1ml of medium in technical triplicate for each KZFP. Following puromycin selection and prior to doxycycline induction, cell survival was visually assessed as a quality control metric for each KZFP construct (Supp __Table 2____). Doxycycline (1µg/mL) was added immediately after cell seeding to induce expression of the HA-tagged KZFPs. At each time point, metabolic activity was measured using PrestoBlue™ reagent according to the manufacturer's instructions (10µL reagent added to 100µL culture medium, incubated for 3h in a 96 plates). Absorbance was recorded at 570 nm and 600 nm using a plate reader (Hidex Sense Microplate Reader), GFP- and LacZ-expressing control wells were included on every plate to account for plate-to-plate and batch-to-batch variability. Peripheral wells were filled with culture medium to minimize evaporation-induced edge effects. Cells were maintained in RPMI supplemented with 10% fetal bovine serum (FBS) and 1× penicillin–streptomycin, and splited (1/10) with aspiration of the surface medium every three days throughout the assay while maintaining doxycycline at 1µg/mL. Cell proliferation was assessed after 4, 7, and 9 days of induction. and the A570/A600 ratio was used as a surrogate measure of viable cell number and proliferative capacity. For computational normalization, raw A570/A600 values were first background-corrected by subtracting the signal from medium-only controls and then normalized in two steps. First, each value was divided by the mean signal obtained from the GFP and LacZ control wells from the corresponding batch and induction condition to correct for inter-batch variability. Second, the resulting value was normalized to the corresponding −Dox condition for the same KZFP and time point to correct for seeding variability, yielding a relative proliferation score that reflects the effect of KZFP induction. KZFPs with a normalized proliferation score ≤ 0.85 at day 9 were arbitrarily classified as proliferation-impairing hits in this screening framework.

After doxycycline induction, dot blot analysis using anti-HA and anti-actin antibodies was systematically performed to assess KZFP expression and sample loading, respectively (Supplementary DotBlot.pdf). The HA signal following doxycycline induction (HA_Dox) and actin signal following doxycycline induction (Actin_Dox) were visually scored from the dot blot signals (__Supp __Table 2).

In addition, to strengthen the methodological description and address these concerns more directly, we will:

1/ Include a supplementary table summarizing our experimental observations for each individual KZFP throughout the screening process (See preliminary Supp Table 2). -> See header here:

2/ Perform and include Dot Blot analyses, to assess and compare transgene expression levels across KZFP constructs. (Supplementary File DotBlot.pdf____). Generation of these files is in progress, with a few missing dot blots still being completed (we have done 303 over 366 already). However, preliminary versions have already been submitted. -> See header of the .pdf here:

In addition, we agree that a more explicit discussion of the limitations of our screening approach improves the interpretation of our findings. Accordingly, we expanded the Discussion to address the limitations associated with variable transgene integration, heterogeneous transgene expression, potential toxicity due to ectopic KZFP overexpression, and the use of K562 cells as a standardized rather than physiological cellular model.

“Several methodological considerations should be taken into account when interpreting these results. As with any lentiviral overexpression screen, three potential sources of technical variability may influence the observed phenotypes: differences in transgene integration sites, heterogeneity in transgene expression levels, and non-specific toxicity resulting from ectopic overexpression. Variable integration sites are unlikely to represent a major source of bias in the present study because all analyses were performed on polyclonal populations of transduced cells rather than individual clones, thereby averaging integration-site effects across many independent events. In contrast, heterogeneity in transgene expression levels is expected, as the abundance of each KZFP depends not only on transduction efficiency but also on intrinsic differences in mRNA stability, translational efficiency, and protein stability. To minimize these sources of variability, all constructs underwent systematic quality control, including assessment of cell survival following puromycin selection and evaluation of transgene expression by HA dot blot after doxycycline induction. Although transgene expression levels varied across KZFPs (Supplementary File DotBlot.pdf), this variability showed no systematic relationship with the proliferation phenotypes, suggesting that differences in overexpression efficiency are unlikely to be the primary determinant of toxicity. Nevertheless, ectopic expression exposes cells to supraphysiological concentrations of KZFPs capable of generating non-physiological interactions or regulatory effects. Therefore, while the screening strategy is well suited for identifying candidate functional regulators, independent validation under endogenous expression conditions remains essential to confirm KZFP-specific functions.”

Reviewer 1 Major comment 2:

“A central conceptual issue throughout the manuscript is that the downstream functional analyses of the selected KZFPs remain largely disconnected from the original screening phenotype. The four candidates were prioritized based on proliferation defects observed upon overexpression in K562 cells; however, the subsequent analyses (with the only exception being a more in-depth experimental analysis of ZNF498 in ciliogenesis, which stands out as comparatively more directly supported by experimental evidence) primarily rely on correlative expression patterns and KZFP ChIP-seq datasets to infer potential biological functions in unrelated cellular contexts. As a result, it remains unclear whether the proposed transcriptional programs are mechanistically linked to the proliferation phenotypes that motivated candidate selection in the first place. This issue is evident across multiple sections of the manuscript. For example, the proposed role of ZNF43 in regulating fatty acid metabolism and detoxification pathways is primarily inferred from tissue-level expression correlations. While these analyses focus on genes identified as potential ZNF43 targets, the underlying ChIP-seq datasets were themselves generated under ZNF43 overexpression conditions. Therefore, the current analyses do not establish whether ZNF43 regulates these pathways under physiological expression levels or within a relevant cellular context, nor how such regulation relates to the proliferation defect observed in K562 cells. Moreover, several proposed target genes remain substantially expressed in tissues where ZNF43 expression is not particularly low (e.g., kidney and heart muscle), suggesting that additional regulators are likely involved. Similarly, the proposed model of ZNF257-mediated regulation of MAGEA genes during spermatogenesis is intriguing but does not fully account for the expression behavior of all MAGEA family members, particularly MAGEA2B, which displays strong expression in spermatocytes despite high ZNF257 expression. This expression pattern should be acknowledged in the main text and reflected in Fig. 3K. In addition, the labels for MAGEA6 and MAGEA2B in Fig. 3C appear to be inverted. More broadly, the proposed regulatory model is difficult to reconcile with the generally restricted expression pattern of MAGEA genes across adult tissues, as their expression does not appear to consistently correlate with ZNF257 levels outside the germline context. Related concerns also apply to the analyses of ZNF498 and ZNF18, where the proposed functions in cilium formation and sperm maturation remain disconnected from the proliferation defects identified in the initial screen.”

We agree that this comment raises an important conceptual point and has helped us clarify the scope of the study and the interpretation of our findings. In the revised manuscript, we explicitly distinguish hypothesis generation from mechanistic validation by clarifying that the proliferation phenotype observed in K562 cells reflects the regulatory potential of ectopically expressed KZFPs rather than their physiological functions. We also adopted a more cautious interpretation of the functional analyses, emphasizing that the proposed regulatory networks are hypothesis-generating and that individual KZFPs are unlikely to act as sole regulators. More broadly, we emphasize that the primary objective of this study is to establish a scalable screening platform for prioritizing KZFPs and identifying biologically relevant contexts for future investigation, rather than to provide a comprehensive functional characterization of individual KZFPs. We agree that this comment highlights an important limitation of our proposed regulatory model. In the revised manuscript, we adopted a more nuanced interpretation by presenting ZNF257 as a contributor to, rather than the sole regulator of, the MAGEA transcriptional program, and by explicitly discussing the exceptions identified by the reviewer.

Modification in the revised manuscript:

1/

“Integrative transcriptomic, chromatin and proteomic analyses reveal diverse mechanisms, including transposable element–linked repression (ZNF43), promoter-proximal regulation (ZNF257), and SCAN domain–dependent transcriptional activation (ZNF498/ZSCAN25 and ZNF18).”

Is now:

“Integrative transcriptomic, chromatin and proteomic analyses identify distinct regulatory properties and generate testable hypotheses regarding diverse mechanisms, including transposable element-associated repression (ZNF43), promoter-proximal regulation (ZNF257), and SCAN domain-dependent transcriptional activation (ZNF498/ZSCAN25 and ZNF18).”

2/

“Detailed follow-up of four such candidates, ZNF43, ZNF257, ZNF498 and ZNF18, revealed as hypothesized distinct modes of action, ranging from TE-linked transcriptional repression to promoter-proximal gene silencing and SCAN domain-mediated transcriptional activation. These findings reinforce the view that KZFPs, while often viewed as a homogeneous family of TE-repressive TFs, are rather functionally diverse regulators with wide-ranging impacts on human biology.”

Is now:

“Detailed follow-up of four such candidates, ZNF43, ZNF257, ZNF498 and ZNF18, identified distinct regulatory properties and generated hypotheses regarding their physiological functions. By integrating overexpression-induced transcriptional responses, chromatin occupancy, proteomic analyses and tissue-specific expression data, we propose candidate biological contexts in which these KZFPs may operate. These hypotheses now provide a framework for future mechanistic studies performed under physiological conditions. Together, these findings reinforce the view that KZFPs, while often viewed as a homogeneous family of TE-repressive transcription factors, comprise functionally diverse regulators with broad potential roles in human biology.”

3/

“We conclude from these data that ZNF43 regulates a transcriptional program related to fatty acid metabolism and detoxification, allowing for the preferential expression of its effectors in the liver (Fig. 2G). Interestingly, neither expression nor chromatin state followed the same pattern at the functionally unrelated DNAI4 locus, indicating that this gene is subjected to other dominant regulators.”

Is now:

“Together, these observations identify a small set of candidates ZNF43 target genes involved in fatty acid metabolism and detoxification and suggest that ZNF43 may contribute to the regulation of these transcriptional programmes in appropriate physiological contexts (Fig. 2G). However, these conclusions are derived from overexpression-based datasets and tissue-level expression analyses and should therefore be considered hypothesis-generating. Interestingly, neither expression nor chromatin state followed the same pattern at the functionally unrelated DNAI4 locus, indicating that additional regulatory mechanisms contribute to the control of these genes.”

4/

“It strongly suggests that ZNF257 contributes to initiating the transcriptional repression of these two MAGEA genes during early spermiogenesis, after which their silencing may be stabilized through stable epigenetic mechanisms such as DNA methylation.”

Is now:

“These observations suggest that ZNF257 may contribute to the initiation of transcriptional repression of a subset of MAGEA genes during the spermatogonia-to-spermatocyte transition, after which their silencing may be stabilized through epigenetic mechanisms such as DNA methylation.”

5/

“Together, these results identify ZNF498 as a transcriptional activator of gene modules controlling cytoskeleton-dependent processes and suggest that this TF may act as a regulator of neuronal cytoskeletal architecture, warranting investigation in relevant neural models.”

Is now:

“Together, these results indicate that ZNF498 functions as a transcriptional activator in our overexpression system and support the hypothesis that it contributes to transcriptional programmes controlling cytoskeleton-dependent processes in physiologically relevant neural contexts, warranting further investigation in dedicated neural models.”

6/

“The co-expression of ZNF18 and its target genes at the spermatid stage suggests that ZNF18 activates a transcriptional program supporting these processes.”

Is now:

“The co-expression of ZNF18 and its candidate target genes at the spermatid stage is consistent with the hypothesis that ZNF18 contributes to transcriptional programmes supporting these processes.”

7/

“The four KZFPs characterised here illustrate this diversity. ZNF43 represses a coherent set of genes involved in fatty acid metabolism and detoxification through binding to nearby LTR/ERV1 integrants, with its expression anticorrelating that of its targets: i.e., highly expressed in thymus and bone marrow, where these metabolic genes are silent, and lowly expressed in liver, where they are most active. This represents a clear example of host genomes coopting TE-derived sequences and shaping their regulatory activities in a cell-type specific manner by the differential expression of KZFPs. ZNF257, by contrast, acts as a promoter-proximal repressor whose targets show accelerated sequence evolution at their promoters, consistent with integration into a KZFP-orchestrated GRN through rapid promoter diversification, a feature previously described for KZFPs (Farmiloe et al., 2023). Its regulation of the MAGEA gene cluster exemplifies a distinct evolutionary mechanism: an ancestral intronic binding site, present in MAGEA6 gene body, before ZNF257 emerged, was propagated across the cluster through tandem duplication, enabling coordinated regulation of multiple paralogs. Temporal expression analysis during spermatogenesis further suggests that ZNF257 initiates MAGEA repression at the spermatogonia-to-spermatocyte transition, after which silencing may be maintained through epigenetic mechanisms such as DNA methylation. ZNF498 and ZNF18, both SCAN-containing KZFPs with variant KRAB domains, on the other hand acted as transcriptional activators. ZNF498 activates a programme centred on microtubule cytoskeleton organisation, as demonstrated by the disruption of ciliogenesis upon its overexpression, and both ZNF498 and its targets are broadly expressed in the central nervous system, particularly in excitatory neurons where microtubule dynamics are essential for axonal architecture. ZNF18 similarly activates genes involved in chromatin remodelling and cytoskeletal reorganisation at the spermatid stage, processes that are hallmarks of spermiogenesis. Together, these case studies demonstrate that even within a single screen, KZFPs with fundamentally different regulatory logics can be identified through a single unifying phenotype and then mechanistically dissected to uncover their unique properties.”

Is now:

“The four KZFPs characterized here illustrate the functional diversity that can be uncovered using this screening strategy. For ZNF43, integration of overexpression transcriptomics with ChIP-exo binding data identified a small set of candidate direct target genes located near LTR/ERV1 elements. Their tissue-specific expression patterns are consistent with the hypothesis that ZNF43 contributes to transcriptional programmes associated with fatty acid metabolism and detoxification, although these analyses, which rely on overexpression-derived datasets and tissue-wide correlations, do not establish physiological regulation or causality. Rather, they identify a candidate regulatory network whose functional relevance will require investigation in appropriate biological models. More generally, these observations support the concept that host genomes may exploit TE-derived regulatory sequences in a tissue-specific manner through differential KZFP expression, while recognizing that additional transcription factors almost certainly participate in controlling these gene expression programmes. Similarly, ZNF257 emerged as a promoter-associated transcriptional repressor in our overexpression system. Evolutionary analyses suggest that tandem duplication propagated an ancestral ZNF257-binding sequence across the MAGEA locus, generating the hypothesis that ZNF257 may contribute to coordinated regulation of this gene cluster during spermatogenesis. The temporal expression profiles of ZNF257 and the MAGEA genes are compatible with such a model but remain correlative and therefore require direct functional validation. ZNF498 and ZNF18, two SCAN-containing KZFPs with variant KRAB domains, displayed transcriptional activation rather than repression following overexpression. For ZNF498, the integration of transcriptomic analyses with expression profiling pointed to microtubule cytoskeleton organization as a candidate biological process, a prediction that was further supported experimentally by the marked impairment of ciliogenesis following ZNF498 overexpression in hTERT-RPE1 cells. This represents the strongest functional validation presented in this study and supports the biological relevance of the analytical framework developed here. For ZNF18, the co-expression of the KZFP and its candidate target genes during spermatogenesis is consistent with the hypothesis that it contributes to transcriptional programmes involved in chromatin remodelling and cytoskeletal reorganization during spermatid differentiation. Together, these case studies illustrate how a standardized overexpression screen can identify KZFPs with distinct regulatory properties and generate biologically coherent hypotheses regarding their physiological functions. Rather than establishing definitive functions for individual KZFPs, this framework prioritizes candidates, proposes relevant cellular contexts, and provides a foundation for future mechanistic studies performed under physiological conditions.”

“In addition, interpretation of the SCAN-deletion experiments is complicated by the reduced expression levels of the deletion constructs relative to the corresponding full-length proteins, making it difficult to determine whether the observed proliferation phenotypes are pathway-specific or partially driven by differential expression.”

We thank the reviewer for this important observation and agree that differences in expression levels between the full-length and ΔSCAN constructs could complicate the interpretation of the observed phenotypes. To address this concern, we performed a quantitative comparison of the expression levels of full-length and ΔSCAN proteins using both western blotting and transgene expression using RNAseq, while accounting for differences in transgene length. This result are now added in (Fig S6C, D).

With modification of the legend:

• HA signal after OE of HA-tagged ZNF18, ZNF18∆SCAN, ZNF498, ZNF498∆SCAN or GFP in K562 cells. Actin as control.
• Quantification of ZNF18, ZNF18∆SCAN, ZNF498, ZNF498∆SCAN It appears that the difference is small (Minor comments of the reviewer 1

“- In the Abstract and in the "Limitations of the study" section, the term "annotation" is used. It would be preferable to specify "functional characterization" instead of "annotation".

Done as suggested by the reviewer.

• In the Introduction, there may be a minor citation confusion. Following the sentence: "Characterized by an N-terminal KRAB domain and a C-terminal tandem array of C2H2 zinc fingers, KZFPs primarily target transposable element (TE)-embedded sequences," the cited references are predominantly experimental studies supporting this statement. However, the inclusion of the review "Bruno, Mahgoub and Macfarlan, 2019" appears less appropriate in this context, as it does not directly present ChIP-seq data supporting this claim. More relevant primary studies from the same research area include "Wolf et al. 2020" and "Bruno et al. 2025.".

Done as suggested by the reviewer.

• In Fig. 1A, "D10" appears inconsistent with the text and other figures (Fig. 1B, 1G, 1H), which refer to 9 days post-induction.

Done as suggested by the reviewer.

• In Fig. S1, there may be a mismatch in the highlighted plate: the zoomed image appears to correspond to the first plate from the top. The correct plate should be highlighted for consistency.

Done as suggested by the reviewer.

• In Fig. 1B, there is a typographical error ("K ZFPs" instead of "KZFPs").

Done as suggested by the reviewer.

• In Fig. S1E, it is unclear what "other" refers to. Please clarify whether this represents the mean of all remaining KZFPs or a defined subset, ideally in the figure description.

Done as suggested by the reviewer.

• In Fig. S2E, "SetDB1" should be corrected to "SETDB1".

Done as suggested by the reviewer.

• In Fig. 3B, it is unclear what distinguishes the upper and lower "Diverse REs". A brief clarification in the figure legend would improve interpretability, particularly regarding the transposable element families included.

Done as suggested by the reviewer.

• In Fig. S3C, the x-axis labels appear slightly misaligned and shifted to the right.

Done as suggested by the reviewer.

• In Fig. 3C, the labels for MAGEA6 and MAGEA2B appear to be inverted.

Done as suggested by the reviewer.

• In Fig. 3K, "MAGE3" should be corrected to "MAGEA3".

Done as suggested by the reviewer.

• In the ZNF498 section, line 4, the punctuation should be corrected so that the period appears after the figure reference ("promoters (Fig. S1E).").

Done as suggested by the reviewer.

• In the final sentence of the ZNF498 section, a noun appears to be missing after "cytoskeleton-dependent," possibly "processes".

Done as suggested by the reviewer.

• In the last section of the Results and corresponding figures and their descriptions, "SCAN dependant" should be corrected to "SCAN-dependent".”

Done as suggested by the reviewer.

Major comments of the reviewer 2

“- The authors chose four KZFPs to study in detail, but why they chose these 4 candidates is unlcear to me. It would be nice to add a more detailed description of the process by which they chose the four candidates.”

We agree that the rationale for selecting the four KZFPs should be presented more explicitly. Accordingly, we revised the manuscript to clarify the selection criteria.

“However, a modest correlation was noted between the number of transcription start sites (TSS) bound by KZFPs and the drop in PrestoBlue signal induced by their overexpression (Fig. 1G), and SCAN-containing KZFPs (SKZFPs) tended to induce proliferation defects more frequently than family members lacking this domain (Fig. 1H).”

Is now:

“However, a modest correlation was noted between the number of transcription start sites (TSS) bound by KZFPs and the drop in PrestoBlue signal induced by their overexpression (Fig. 1G), and SCAN-containing KZFPs (SKZFPs) tended to induce proliferation defects more frequently than family members lacking this domain (Fig. 1H). These observations indicated that KZFPs affecting proliferation do not constitute a homogeneous functional group, prompting us to select representative candidates spanning the evolutionary, structural, and genomic diversity of the KZFP family for mechanistic characterization.____”

“- The materials and methods part of the manuscript is not detailed enough for other researchers to reproduce the study. They should add more details to both experiments and data analysis part of this section. Below I highlight some examples for sake of clarity, but the authors should revise the whole materials and methods section and add more details keeping these examples in mind:

• The authors do not state the titer of lentiviral vectors they generate nor the MOI or amount of virus they use to transduce the cells

• In many cases, the specific softwares and the software version is not stated e.g., the analysis of the Gene Ontology Biological Processes

• It would be beneficial for the readers to get more details about the construct they used, for example a map of the plasmid.

• It is unclear how many cells were used for RNA extraction

• It is unclear which microscopes were used for imaging.

• The concentration of antibodies used for staining and the product number, and provider of the antibody is not always depicted.”

We agree that the additional methodological details requested by the reviewer will improve the reproducibility and transparency of the study. Accordingly, we have expanded the Methods section to provide a more detailed description of the experimental procedures and data analysis workflow.

“Lentiviral particles were produced in HEK293T cells by transient co-transfection of transfer, packaging and envelope plasmids. Cells were transfected at approximately 70–80% confluence using a standard lipid-based transfection reagent. Viral supernatants were collected 48 h after transfection, cleared by centrifugation, filtered through 0.22-µm membranes, and used fresh or stored appropriately until use. Recipient K562 or hTERT-RPE1 cells were transduced under conditions optimized for efficient gene delivery.”

Is now:

“Lentiviral particles were produced in HEK293T cells. 105 cells were seeded in 24 well plates filled with 1ml DMEM the day before transfection. Cells were co-transfected individually with 0.15ug of each plasmids encoding KZFPs tagged with HA (pTRE-KZFPX-HA-PGK-puro), 0.1ug of the packaging plasmid (pR8.74) and 0.07ug of the envelope plasmid (pMD2G) using TransIT®-LT1 Transfection Reagent (MIR 2306), according to the manufacturer's instructions. Viral supernatants were harvested 24h after transfection, clarified by centrifugation, filtered through 0.45-µm filters and used immediately.”

“Coding sequences were cloned into doxycycline-inducible lentiviral transfer vectors designed to express N-terminally HA-tagged proteins.”

Is now:

“Coding sequences corresponding to 366 human KZFP open reading frames were codon-optimized for human expression and cloned into doxycycline-inducible lentiviral transfer vectors expressing C-terminal HA-tagged proteins under the control of a tetracycline-responsive promoter pTRE-KZFPX-HA-PGK-puro. All expression constructs used in the primary overexpression screen have been deposited and are publicly available (De Tribolet et al., 2023). A schematic representation of the lentiviral expression cassette, including the promoter, HA tag, cloning site, antibiotic resistance cassette, and regulatory elements, is provided in Supplementary file. Selected constructs encoding ZNF43, ZNF257, ZNF498 and ZNF18 were used for follow-up mechanistic studies. For SCAN-domain functional analyses, deletion constructs lacking the SCAN domain (ΔSCAN) were generated for ZNF18 and ZNF498 in the same lentiviral backbone. Deletion were done using In-Fusion cloning with specific primers. PCR was performed with high-fidelity polymerase, followed by gel purification and recombination with the linearized plasmid using the In-Fusion HD Cloning Kit (Takara Bio©) according to the manufacturer’s protocol. The product was transformed into HB101 Escherichia coli cells, and colonies were screened by PCR. Positive clones were verified by Sanger sequencing, and confirmed plasmids were propagated and purified for further use.”

“Total RNA was extracted...”

Is now:

“For each biological replicate, approximately 1 × 10⁶ K562 cells were harvested 72 h after doxycycline induction. Total RNA was extracted…”

“Images were acquired by fluorescence microscopy under identical conditions across samples.”

Is now:

“Images were acquired using a confocal microscope Leica-SP8 (Leica Biosystems) with an objective HC PL APO 63x/1.40 and a pinhole size of 1 AU, using identical acquisition settings for all conditions. Images were processed using Fiji/ImageJ (version 2.9.0) without nonlinear intensity adjustments.”

“Cells were fixed and stained with antibodies against ciliary markers (ARL13B)”

Is now:

“Cells were fixed in 4% paraformaldehyde, permeabilized with 0.1% Triton X-100, blocked with 2% BSA, and incubated with rabbit anti-ARL13B (Proteintech, Cat. No. 17711-1-AP, 1:200) followed by Alexa Fluor 568-conjugated donkey anti-rabbit IgG (Thermo Fisher Scientific, Cat. No. A-10042, 1:1000). Nuclei were stained with Hoechst (1 µg/mL).”

“- The authors mention that KZFPs are usually expressed at a low level in the K562 cell line they use, but there is no figure showing the expression level of KZFPs in this cell type. It would be important to see the baseline KZFP expression in these cells, the level of overexpression and compare it to the endogenous expression levels they show in different cell types/tissues, at least for the four candidates studied more in depth. This would help to understand whether this level of activity is something that could occur naturally in a physiologically relevant context.”

We thank the reviewer for this insightful suggestion and fully agree that providing additional context regarding endogenous and ectopic KZFP expression levels will help readers better assess the physiological relevance of our findings. As suggested, we included data showing the baseline expression levels of the four selected KZFPs in K562 cells together with the expression levels achieved following doxycycline-induced overexpression. We also compared these values with publicly available transcriptomic data from cell lines. Importantly, only cell lines are assessed as we need ground through (K562) to estimate transgene expression. We modified Fig. S2, Fig. S3, Fig. S4 and Fig. S5 to add the results of these analysis. Here is ZNF43 as an example:

With the following legend:

“(C) Distribution of endogenous expression levels, (using GFP control cells), of all expressed genes (light grey) and all KZFPs (dark grey) in K562 cells. The solid red line indicates endogenous ZNF43 expression in GFP control cells, whereas the dashed red line indicates the corrected transgene expression following doxycycline induction.

(D) Endogenous ZNF43 expression across Human Protein Atlas cell lines, (https://www.proteinatlas.org/about/download#cell_line), following normalization to the local RNA-seq dataset. K562 cells are highlighted in red. The dashed red line indicates the corrected transgene level measured following doxycycline-induced overexpression in K562 cells overexpressing ZNF43.”

Modified the result section:

“ZNF43 is a ~43-million-year-old KZFP with a canonical TRIM28-recruiting KRAB domain and 19 zinc fingers that preferentially recognize an LTR/ERV1-embedded sequence (Fig. S1F). We first verified that ZNF43 overexpression impaired the growth of K562 cells (Fig. S2A, B). Endogenous ZNF43 expression was readily detectable in K562 cells and across human cell lines (Fig. S2C, D). Following doxycycline induction, transcript abundance markedly increased and exceeded the highest endogenous expression level observed among the analyzed cell lines (Fig. S2C, D).”

We also updated the Methods section:

“Quantification of endogenous and transgene expression levels

Endogenous KZFP expression in K562 cells was estimated from GFP control RNA-seq samples using normalized mean expression values obtained from the differential expression analyses. For ZNF18, whose transgene sequence is identical to the endogenous coding sequence (i.e., not codon-optimized), transgene-derived expression was estimated directly by subtracting the endogenous transcript abundance measured in GFP controls from the total transcript abundance measured following doxycycline induction (OE − GFP). For ZNF43, ZNF257 and ZNF498, the overexpression constructs were synthesized using codon-optimized coding sequences. RNA-seq reads were therefore additionally aligned against the codon-optimized transgene reference sequences to specifically quantify exogenous transcripts without interference from endogenous reads. Because these codon-specific counts are generated through an independent alignment strategy, they are not directly comparable to the endogenous RNA-seq expression values. To calibrate these measurements, a scaling factor was derived from the ZNF18 dataset by comparing the codon-specific read counts with the transgene abundance estimated from the differential expression analysis (OE − GFP). This empirically determined correction factor was subsequently applied to all codon-optimized constructs, thereby expressing transgene abundance on the same scale as the endogenous RNA-seq measurements. Corrected transgene expression values were then used for all downstream comparisons. To compare endogenous expression across physiological contexts, publicly available RNA-seq datasets from the Human Protein Atlas (cell lines) were downloaded and normalized to the local RNA-seq scale. A normalization factor was calculated from the median expression ratio of KZFPs detected in both the Human Protein Atlas K562 dataset and the local K562 GFP control RNA-seq dataset, and subsequently applied uniformly to all Human Protein Atlas datasets. This normalization enabled direct comparison of endogenous expression across biological contexts with the corrected transgene expression values. Global KZFP expression was calculated as the median normalized expression of all annotated KZFPs within each biological context. For the four KZFPs selected for detailed characterization, endogenous expression across Human Protein Atlas cell lines was compared with corrected transgene expression following doxycycline induction. Expression distributions of all genes and KZFPs were visualized using ranked expression plots and density histograms. All analyses were performed in R using the tidyverse package.”

We fully acknowledge that the overexpression system used in this study was primarily designed as a discovery platform to identify candidate functions, targets, and interaction partners of KZFPs that are otherwise expressed at lower levels in K562 cells. As the reviewer correctly points out, determining whether these regulatory effects occur at endogenous expression levels in physiologically relevant cellular contexts represents an important next step. We Thereby also clarified this in the “Limitations to this study” paragraph:

“To better place our experimental system into a physiological context, we compared endogenous KZFP expression in K562 cells with publicly available transcriptomic datasets from the Human Protein Atlas. These analyses showed that K562 cells do not exhibit unusually low global KZFP expression compared with other human cell lines. However, consistent with the restricted expression patterns of this protein family, KZFPs as a whole are expressed at substantially lower levels than the average human gene. For the four KZFPs characterized in detail, doxycycline induction produced transcript levels that exceeded the highest endogenous expression observed across the analyzed human cell lines. Accordingly, the overexpression system used in this study was not designed to recapitulate physiological expression levels but rather to maximize the identification of candidate target genes, interacting partners, and regulatory pathways for KZFPs that are otherwise expressed at low endogenous levels. Consequently, the molecular interactions identified here should be considered as hypotheses requiring validation under endogenous expression conditions in physiologically relevant cellular models.”

“- RNA seq analysis: It is unclear how many cells were used in the RNA seq analysis, I would like to ask the authors to clarify that. Moreover, from my understanding the RNA seq analysis was done on day 3, while the Presto Blue analysis was done on days 4, 7 and 9. I would like to kindly ask the authors to motivate their choice for the day of the RNA sequencing analysis.”

We agree that this information required clarification. The Methods section has been revised to specify the number of cells used for RNA-seq library preparation and to explain the rationale for performing RNA-seq after 3 days of doxycycline induction, before measurable proliferation defects emerge, in order to capture primary transcriptional responses to KZFP overexpression. The corresponding modification has also been added to the Results section when introducing the RNA-seq analyses.

“For transcriptome profiling, K562 cells expressing the indicated inducible constructs were treated with doxycycline for 72 h before harvest. Total RNA was extracted using the NucleoSpin RNA plus kit (Macherey-Nagel) according to the manufacturer’s recommendations. RNA quantity and purity were assessed by spectrophotometry, and RNA integrity was evaluated before library preparation.”

Is now:

“For transcriptome profiling, 1 × 10⁶ K562 cells expressing the indicated inducible constructs were treated with doxycycline for 72 h before harvest. RNA was collected after 3 days of induction to capture the primary transcriptional responses to KZFP overexpression before substantial differences in proliferation became apparent. This early time point was chosen to minimize secondary transcriptional changes resulting from altered cell growth, cell-cycle distribution, or cellular stress, which become detectable in the proliferation assays performed after 4, 7, and 9 days of induction. Total RNA was extracted using the NucleoSpin RNA plus kit (Macherey-Nagel) according to the manufacturer’s recommendations. RNA quantity and purity were assessed by spectrophotometry, and RNA integrity was evaluated before library preparation.”

“We then profiled the transcriptome of K562 cells overexpressing ZNF43 by deep RNA sequencing (RNA-seq)”

Is now:

“We then profiled the transcriptome of K562 cells overexpressing ZNF43 by deep RNA sequencing (RNA-seq) after 3 days of doxycycline induction, a time point selected to capture primary transcriptional responses before the onset of measurable proliferation defects.”

Minor comments of the reviewer 2

“- Figure S1D is not mentioned in the text before figure S1E. The order of the panels should be changed in the figure.

Done as suggested by the reviewer.

• "We selected genes that were downregulated upon ZNF43 overexpression and harboured a ZNF43 binding site within 10kb of their TSS (Fig. 1A) - don't the authors mean Fig. 2A?

Done as suggested by the reviewer.

• In Figure 4D, the GO terms cannot be read, as the sentences seem to be cut.

Done as suggested by the reviewer.

• All figures and figure legends need to be revised. In some cases, the letter size is too small, or the legend and explanation of colours is missing. Please see some examples below: Fig. S6C, Fig 6C, Fig S4C, Fig S5C (letter size too small) Fig S6G, Fig 4E (label/scale is missing)”

Homogenized to Arial 6 by default as requested by most of journal guidelines

__ Description of analyses that authors prefer not to carry out__

We think that by proceeding as described above we will have addressed all major conceptual issues raised by the reviewers.

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Referee #2

Evidence, reproducibility and clarity

Summary

Foley et al establishes a scalable framework to probe KZFP function. They performed an array of inducible overexpression screen of 366 human KZFPs in K562 cells. This screen, together with the analysis of transcriptomic and available chromatin and proteomic datasets revealed that KZFPs regulate many different mechanisms, highlighting the functional diversity of KZFPs. Understanding this functional diversity is a very interesting, timely and relevant question, but it is also challenging to study. Therefore, the approach the authors develop is promising. While the quality of the experiments and data analysis is high, the weakness I see in the manuscript is the lack of major biological insights in relevant model systems. Please see my detailed comment in the significance part.

Major comments

• The authors chose four KZFPs to study in detail, but why they chose these 4 candidates is unlcear to me. It would be nice to add a more detailed description of the process by which they chose the four candidates.
• The materials and methods part of the manuscript is not detailed enough for other researchers to reproduce the study. They should add more details to both experiments and data analysis part of this section. Below I highlight some examples for sake of clarity, but the authors should revise the whole materials and methods section and add more details keeping these examples in mind:
  • The authors do not state the titer of lentiviral vectors they generate nor the MOI or amount of virus they use to transduce the cells
  • In many cases, the specific softwares and the software version is not stated e.g. the analysis of the Gene Ontology Biological Processes
  • It would be beneficial for the readers to get more details about the construct they used, for example a map of the plasmid.
  • It is unclear how many cells were used for RNA extraction
  • It is unclear which microscopes were used for imaging.
  • The concentration of antibodies used for staining and the product number, and provider of the antibody is not always depicted.
• The authors looked at available chromatin data in either K562 cells or HEK293 cells, which I think is a very good way of utilizing publicly available data. Since the authors showed that different KZFPs might be functionally relevant in different cell types/tissues, I was wondering if they checked if there is available ChIP Seq or CUT&RUN data in those specific cell types/tissues. If yes, that data should be included in the manuscript.
• The authors mention that KZFPs are usually expressed at a low level in the K562 cell line they use, but there is no figure showing the expression level of KZFPs in this cell type. It would be important to see the baseline KZFP expression in these cells, the level of overexpression and compare it to the endogenous expression levels they show in different cell types/tissues, at least for the four candidates studied more in depth. This would help to understand whether this level of activity is something that could occur naturally in a physiologically relevant context.
• RNA seq analysis: It is unclear how many cells were used in the RNA seq analysis, I would like to ask the authors to clarify that. Moreover, from my understanding the RNA seq analysis was done on day 3, while the Presto Blue analysis was done on days 4, 7 and 10. I would like to kindly ask the authors to motivate their choice for the day of the RNA sequencing analysis.

Minor comments

• Figure S1D is not mentioned in the text before figure S1E. The order of the panels should be changed in the figure.
• "We selected genes that were downregulated upon ZNF43 overexpression and harboured a ZNF43 binding site within 10kb of their TSS (Fig. 1A) - don't the authors mean Fig. 2A?
• In Figure 4D, the GO terms cannot be read, as the sentences seem to be cut.
• All figures and figure legends need to be revised. In some cases, the letter size is too small, or the legend and explanation of colours is missing. Please see some examples below: Fig. S6C, Fig 6C, Fig S4C, Fig S5C (letter size too small) Fig S6G, Fig 4E (label/scale is missing)

Significance

Understanding the diverse roles of KZFPs is an important and interesting research question. However, studying KZFPs is challenging, as many KZFP-mediated effects appear to be highly cell type- and tissue-specific. This complexity is also highlighted by the findings of the current manuscript.

A major strength of this study is the development of a scalable system that enables the simultaneous investigation of the entire KZFP family. Performing such analyses on an individual basis would be extremely time-consuming. Therefore, the authors provide an efficient and valuable screening platform that can identify promising candidates for further investigation. In this regard, the methodological advance represents the primary contribution of the work.

At the same time, the study lacks a clear biological conclusion. While the screen identifies KZFPs with potential functional effects, it would substantially increase the impact of the manuscript if the authors selected at least one candidate for in-depth characterization in a biologically relevant cellular context. The current study is still of high quality and importance without these experiments, but such follow-up analyses would greatly strengthen the biological significance of the findings.

Another limitation is that the experiments were performed in a cell type in which many of the investigated KZFPs are not normally expressed. As a result, the forced overexpression strategy may not accurately reflect physiological conditions and could potentially generate false-positive results. This concern is particularly relevant in light of the authors' statement that "KZFPs with sufficient regulatory potency to perturb cellular fitness outside of their normal setting are strong candidates for playing important roles within it." While this may indeed be true for some KZFPs, it is also possible that certain observed phenotypes simply arise from ectopic expression in an inappropriate cellular environment.

More generally, the observation that KZFPs can have functions beyond TE repression is already established in the literature. Therefore, the manuscript provides limited new biological insight into this concept. The authors could potentially strengthen the novelty of the study by placing greater emphasis on specific KZFP subfamilies, such as SCAN-containing zinc finger proteins, which are a novel direction and have been implicated in non-canonical regulatory roles.

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Referee #1

Evidence, reproducibility and clarity

Summary

In the manuscript "An overexpression platform reveals the functional diversity of human KRAB-Zinc Finger Proteins in maintaining cellular homeostasis", the authors describe a scalable framework aimed at prioritizing individual KZFPs for functional characterization. The study is centered on a large-scale screening approach in which human erythroleukemia K562 cells were transduced with inducible constructs enabling the overexpression of 366 individual KZFPs. The effects of KZFP overexpression on cellular proliferation were then assessed using a cell viability assay comparing induced and non-induced conditions.

Based on the results of this primary screen, the authors selected four KZFPs for further investigation among those whose overexpression was associated with proliferation defects. Follow-up analyses integrated tissue- and cell type-specific expression patterns of these KZFPs with expression analyses of putative target genes identified from previously published ChIP-seq datasets, with the aim of inferring potential biological functions. On the basis of these analyses, the authors propose that the selected KZFPs may regulate distinct gene networks involved in processes including fatty acid metabolism, spermatogenesis, and other aspects of cellular homeostasis.

The study spans multiple biological contexts, but the evidence supporting several of the individual conclusions remains relatively preliminary, and the breadth of the manuscript often comes at the expense of mechanistic depth.

Major comments

1. Interpretation and robustness of the initial overexpression screen

The large-scale overexpression screen represents the foundation of the manuscript and provides a potentially valuable resource for prioritizing candidate KZFPs for downstream study. However, several aspects of the experimental setup and data presentation currently limit the interpretation of the reported proliferation defects. First, key details regarding the screening workflow remain unclear. While the Methods section describes the overall procedure, it is difficult to determine when cells were seeded relative to doxycycline induction, in which plate format the cells were maintained throughout the experiment, and whether medium exchange was performed during the 9-day assay. These points are particularly relevant given the use of suspension K562 cells (which can complicate medium exchange in a 96-well plate format and make long-term culture more difficult to control) and a metabolic viability readout (PrestoBlue), as differences in nutrient depletion or overgrowth could also influence the signal independently of reduced proliferation or toxicity. Additional clarification regarding seeding density, timing of induction, plate format, culture handling throughout the assay, and whether cell morphology/density was visually monitored would substantially improve interpretability and reproducibility. Second, it is unclear whether the observed proliferation phenotypes may be influenced by differences in transgene expression levels or integration effects. Were all constructs validated for comparable expression following induction? In the absence of such controls, it remains difficult to determine whether the reported phenotypes reflect specific KZFP activities or differences in overexpression efficiency. While it may not be possible to conclusively distinguish KZFP-specific effects from toxicity associated with high transgene expression levels, this limitation should at least be acknowledged. In addition, the possibility that some phenotypes may be influenced by transgene integration effects should also be considered. Unless independent transductions were validated for the KZFPs classified as toxic, it remains difficult to exclude integration-site-specific contributions to the observed proliferation defects. Third, the normalization strategy would benefit from additional clarification. In Fig. S1A, the LacZ control appears variably affected by doxycycline treatment across plates, whereas the GFP control appears more stable. Since normalization relies on the mean behavior of both controls within each batch and condition, the authors should clarify whether this variability could influence hit calling. Finally, several aspects of the data presentation are currently difficult to reconcile. In Fig. 1D, the meaning of the purple category is unclear, and the percentage scaling on the x-axis is difficult to reconcile with the cumulative values displayed. For instance, the sum of all the bars would not reach 100%, as the values of the bars span percentages up to 4% at most (for 105 MYO KZFPs) according to this plot. Similarly, the reported numbers of TE-binding KZFPs in Fig. 1E-F and Fig. S1D appear internally inconsistent and should be clarified. Specifically, 53+14=67 KZFPs are reported to bind TEs in total, yet a larger number of KZFPs appears associated with individual TE families (e.g. 86 for LTR.ERV1). If the values shown correspond to percentages rather than absolute counts, this should be explicitly clarified in both the figure and legend. In addition, Fig. S1D appears inconsistent with the counts reported in Fig. 1E-F, as only 5 out of the 53 toxic KZFPs displayed in the plot show no enrichment for any of the highlighted TE families. 2. Relationship between the screening phenotype and the proposed biological functions of selected KZFPs

A central conceptual issue throughout the manuscript is that the downstream functional analyses of the selected KZFPs remain largely disconnected from the original screening phenotype. The four candidates were prioritized based on proliferation defects observed upon overexpression in K562 cells; however, the subsequent analyses (with the only exception being a more in-depth experimental analysis of ZNF498 in ciliogenesis, which stands out as comparatively more directly supported by experimental evidence) primarily rely on correlative expression patterns and KZFP ChIP-seq datasets to infer potential biological functions in unrelated cellular contexts. As a result, it remains unclear whether the proposed transcriptional programs are mechanistically linked to the proliferation phenotypes that motivated candidate selection in the first place.

This issue is evident across multiple sections of the manuscript. For example, the proposed role of ZNF43 in regulating fatty acid metabolism and detoxification pathways is primarily inferred from tissue-level expression correlations. While these analyses focus on genes identified as potential ZNF43 targets, the underlying ChIP-seq datasets were themselves generated under ZNF43 overexpression conditions. Therefore, the current analyses do not establish whether ZNF43 regulates these pathways under physiological expression levels or within a relevant cellular context, nor how such regulation relates to the proliferation defect observed in K562 cells. Moreover, several proposed target genes remain substantially expressed in tissues where ZNF43 expression is not particularly low (e.g. kidney and heart muscle), suggesting that additional regulators are likely involved.

Similarly, the proposed model of ZNF257-mediated regulation of MAGEA genes during spermatogenesis is intriguing but does not fully account for the expression behavior of all MAGEA family members, particularly MAGEA2B, which displays strong expression in spermatocytes despite high ZNF257 expression. This expression pattern should be acknowledged in the main text and reflected in Fig. 3K. In addition, the labels for MAGEA6 and MAGEA2B in Fig. 3C appear to be inverted. More broadly, the proposed regulatory model is difficult to reconcile with the generally restricted expression pattern of MAGEA genes across adult tissues, as their expression does not appear to consistently correlate with ZNF257 levels outside the germline context.

Related concerns also apply to the analyses of ZNF498 and ZNF18, where the proposed functions in cilium formation and sperm maturation remain disconnected from the proliferation defects identified in the initial screen. In addition, interpretation of the SCAN-deletion experiments is complicated by the reduced expression levels of the deletion constructs relative to the corresponding full-length proteins, making it difficult to determine whether the observed proliferation phenotypes are pathway-specific or partially driven by differential expression. Finally, while the proteomics results aimed at identifying SCAN-dependent interactors are of interest, several aspects of the experimental design and data analysis remain unclear. In particular, it is not specified whether the experiment was performed in biological replicates or as a single measurement. This is important, as it directly affects how the data can be interpreted and how stringent downstream filtering can be. In the Results section, the authors state that "we identified a set of SCAN-dependent interactors, i.e. proteins that co-immunoprecipitated with the full-length construct but were absent in controls and lost upon deletion of the SCAN domain," which suggests a relatively binary, "presence/absence" filtering strategy. However, this description does not specify whether any quantitative threshold (e.g. enrichment ratio) was applied when comparing full-length constructs to deletion mutants. In contrast, the Methods section states that "proteins lacking signal above background were excluded and proteins were additionally required to show stronger signal in at least one bait condition than in GFP controls based on heatmap clustering (see script)," which instead suggests that a threshold-based criterion was used to define enrichment relative to controls and deletion mutants. If this is the case, the exact criteria and thresholds used for filtering should be clearly stated and consistently reported between the Results and Methods sections. If replicate measurements were not performed, this should be explicitly acknowledged, as peptide-level variability may substantially influence the identification of high-confidence interactors, particularly if the applied cutoffs are not highly stringent.

Overall, many of the proposed biological functions are currently supported primarily by correlative analyses and would benefit either from additional functional validation or from a more cautious framing of the conclusions.

Minor comments

• In the Abstract and in the "Limitations of the study" section, the term "annotation" is used. It would be preferable to specify "functional characterization" instead of "annotation".
• In the Introduction, there may be a minor citation confusion. Following the sentence: "Characterized by an N-terminal KRAB domain and a C-terminal tandem array of C2H2 zinc fingers, KZFPs primarily target transposable element (TE)-embedded sequences," the cited references are predominantly experimental studies supporting this statement. However, the inclusion of the review "Bruno, Mahgoub and Macfarlan, 2019" appears less appropriate in this context, as it does not directly present ChIP-seq data supporting this claim. More relevant primary studies from the same research area include "Wolf et al. 2020" and "Bruno et al. 2025.".
• In Fig. 1A, "D10" appears inconsistent with the text and other figures (Fig. 1B, 1G, 1H), which refer to 9 days post-induction.
• In Fig. S1, there may be a mismatch in the highlighted plate: the zoomed image appears to correspond to the first plate from the top. The correct plate should be highlighted for consistency.
• In Fig. 1B, there is a typographical error ("K ZFPs" instead of "KZFPs").
• In Fig. S1E, it is unclear what "other" refers to. Please clarify whether this represents the mean of all remaining KZFPs or a defined subset, ideally in the figure description.
• In Fig. 2A, readability could be improved by adjusting the layering of points, as the darker dots (in particular the red ones) are currently obscured by lighter ones. Alternatively, removing the outline of the points (which is not transparent) may also improve visibility, but in that case the legend for point size would need to be updated accordingly.
• In Fig. S2E, "SetDB1" should be corrected to "SETDB1".
• In Fig. 3B, it is unclear what distinguishes the upper and lower "Diverse REs". A brief clarification in the figure legend would improve interpretability, particularly regarding the transposable element families included.
• In Fig. S3C, the x-axis labels appear slightly misaligned and shifted to the right.
• In Fig. 3C, the labels for MAGEA6 and MAGEA2B appear to be inverted.
• In Fig. 3K, "MAGE3" should be corrected to "MAGEA3".
• In the ZNF498 section, line 4, the punctuation should be corrected so that the period appears after the figure reference ("promoters (Fig. S1E).").
• In the final sentence of the ZNF498 section, a noun appears to be missing after "cytoskeleton-dependent," possibly "processes".
• In the last section of the Results and corresponding figures and their descriptions, "SCAN dependant" should be corrected to "SCAN-dependent".

Significance

General assessment

This study presents a large-scale inducible overexpression platform aimed at systematically exploring the functional diversity of human KZFPs. The screening framework itself represents a potentially useful resource for prioritizing candidate KZFPs for downstream investigation and may be of interest to researchers studying KZFPs, transcriptional regulation, and transposable element biology. A notable strength of the study is the breadth of the screening effort and the attempt to integrate multiple orthogonal datasets to generate functional hypotheses for relatively understudied KZFPs. The more in-depth experimental analysis of ZNF498-mediated ciliogenesis also provides an example of how the platform may be used to identify biologically relevant candidates for further characterization. At the same time, many of the functional conclusions currently remain preliminary and are supported primarily by correlative analyses integrating overexpression phenotypes, expression datasets, and KZFP binding preferences also determined by overexpressing KZFP constructs. In several cases, the proposed biological functions remain insufficiently connected to the original proliferation phenotype used for candidate prioritization. As a result, the current study is best viewed as an exploratory and hypothesis-generating framework rather than a definitive functional characterization of the selected KZFPs. Clarifying these limitations and moderating some of the broader conclusions would substantially strengthen the manuscript.

Advance

The principal advance of the work is therefore primarily technical and resource-oriented, providing a scalable experimental framework for systematic KZFP prioritization and downstream functional exploration. While the study does not yet provide extensive mechanistic validation for most proposed functions, it may nonetheless serve as a useful starting point for future investigations into KZFP biology and transcriptional regulation.

Audience

The manuscript will likely be of greatest interest to a specialized basic research audience working on KZFPs, transposable element regulation, epigenetic regulation, and transcriptional control. Researchers interested in large-scale functional screening approaches may also find the methodological framework useful.

Field of expertise: transposable elements, KRAB-zinc finger proteins, epigenetic regulation, functional genomics, genome regulation.

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

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Reply to the reviewers

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

This interesting manuscript uses single cell RNAseq of developing C. elegans larvae to identify temporal pulses or oscillations in gene expression within glia and many other epithelial cell types - mostly in genes related to cuticle synthesis or remodeling. It identifies different sets of genes that oscillate within different cell types, and identifies many apparent oscillatory genes that were missed in prior studies because they are expressed in smaller populations of cells (whereas bulk data mainly report on oscillations within the major hypodermis).

A second major contribution of this manuscript is to pioneer analysis methods for detecting oscillatory gene expression in scRNAseq datasets. That said, it's important to state that the methods for estimating phase coherence, GAM, perplexity, etc. make sense to me intuitively but I can't assess the math and other details, which are outside of my expertise.

Most of my comments are minor ones about suggested clarifications to the text or figures. Some may require additional analyses, but none should require additional data collection.

1. The manuscript focuses much of its analysis on one specific glial cell type (ILso), yet the authors tell us almost nothing about this cell type or why they would care about it. It would be helpful to include just a little more background on glial biology and the epithelial-like characteristics of socket glia.

We added the following to the second paragraph of Results:

"To this end, we used C. elegans strains expressing GFP specifically in ILso glia or in all glia (grl-18pro::GFP or mir-228pro::GFP, respectively). In C. elegans, all glia are found in sense organs. Most sense organs consist of one or more sensory neurons – each of which is specialized to detect different types of stimuli – and exactly two glia, called the sheath and socket. The sheath and socket glia form an epithelial tube continuous with the skin, through which the ciliated dendritic endings of sensory neurons protrude to sense cues in the external environment. In prior work we found that, in some sense organs, the socket glia produce cuticle specializations around specific sensory neuron cilia, but how these are coordinated with general cuticle synthesis was unknown (Fung et al. 2023)."

Many transcriptomic studies of epithelia (including the Purice et al study of adult glia) use single NUCLEI RNAseq rather than single cells because of the challenges in separating cells connected by tight junctions. In C. elegans there are also various epithelial syncytia to contend with. In text or Methods, the authors should comment on why they think cells were appropriate to look at in this instance, and whether there are certain cell types that were missed or could only be obtained as cell fragments based on that choice.

We added the following to the Methods section:

"Presumably, fine cellular projections such as axons or glial processes are lost during cell dissociation, leaving mainly cell soma with nuclei. There is a risk that some cell types could be undersampled in cell sorting, as compared to sorting isolated nuclei, due to differences in how readily they undergo dissociation. On the other hand, retention of cytoplasmic material in this approach may better represent the total mRNA complement of the cell"

1. Related to above, the authors do not mention any detection or exclusion of likely doublets. Is there reason to think that doublets were not present in any substantial numbers? I'm not super concerned about this since doublets containing hyp7 fragments should have worked against them in detecting glia-specific oscillations, but I do think the issue should be addressed in the text or Methods.

We added the following in Methods:

"Ambient RNA was subtracted using SoupX (Young and Behjati 2020). Potential doublets were assessed using DoubletFinder (McGinnis et al. 2019), but no cells were excluded on this basis. "

1. p. 4 "previously unappreciated local differences in cuticle patterning." This statement should be tempered since many stage- or tissue-specific differences in cuticle patterning have been described previously (including in papers from the Heiman lab and others that are cited here). This study uncovers many additional examples but it's not a completely new finding.

We have revised this:

"Surprisingly, most pulsatile genes are specific to small sets of cell types, suggesting that previously unappreciated local differences in cuticle patterning are more widespread than previously recognized."

1. Table 1 and text: the distinction between pulsatile and oscillatory should be explained more at the outset. These terms sometimes seem to be used interchangeably, but then Table 1 seems to make a distinction, not discussed until the final "limitations" section.

We added the following definition to the Introduction:

"Within a single larval stage, oscillatory genes display a characteristic sharp single peak of expression and we define rigorous metrics for identifying this signature, which we call "pulsatile expression."

• *

We also added a further clarification in the Results section under "De novo identification of pulsatile genes":

"We reasoned that for individual genes, if gene expression in a given cell type were plotted as a function of pseudotime, oscillatory genes would display a distinct peak because they are expressed at a particular pseudotime (Fig. 4A). We refer to this transcriptional signature as "pulsatile" when viewed in a single developmental stage; genes with pulsatile expression are predicted to be oscillatory when viewed across all of larval development, but there may be important exceptions (see "Limitations of the study")."

1. Figure 1 and Figure 3A,B. These UMAPs look very unusual, with no discernable individual dots. Is this just a resolution issue? Or, if relevant, please add info to legend and/or Methods explaining what data smoothing was done here to make them look this way and why.

We have reduced the size of the dots (to point size 1 from point size 2) in the UMAPs in Fig. 1 and Fig. 3 to make individual dots more apparent. The noted effect is due only to the size of the dots; the UMAPs are plotted in the conventional way. The effect of different point sizes on the Fig. 3 UMAP is shown below [IMAGE CANNOT BE ATTACHED HERE]

1. Figure 2C and Figure 6B. In the pseudotime plots, it would be natural for readers to assume that 0 is the beginning of the larval stage and 360 is the end, but that is not actually the way the Meeuse 2020 phase angles work - instead the beginning of the larval stage falls around 160. Please make sure this is made clear, especially when referring to "early and late groups" of TF targets. In Fig 6B, Early and Late categories appear reversed because of the way the data are plotted.

We have replotted Fig. 6B using percent of larval stage progression rather than phase angles in degrees, with 0% corresponding to the peak of dpy-6 expression, to make the timing more intuitive. We have revised the description of the early and late groups in the Discussion.

As Fig. 2C compares our data directly with the phases defined by Meeuse et al., we prefer to keep it consistent with that publication.

1. Figure 3B and Figure 5D-G. The authors group many unidentified clusters into the catchall "skin" category but don't clearly define it in the main text. Table S2 suggests this category includes anterior and posterior skin cells but possibly also other cuticle-lined tubular epithelia that aren't properly referred to as skin (e.g. vulva cells, excretory socket or pore cells). It may also include things like rectum, buccal cavity, excretory duct. Please define your criteria for "skin" more precisely in the main text (any cuticle-lined cell type that is not glia?), and perhaps a more general term such as external epithelia would be more appropriate.

We have changed this in the text to "skin-related cell types" to clarify that it includes hyp, seam, and some unidentified skin-related clusters (which may include some of the cell types you mention, for example the "skin_5" cluster may include vulval epithelia or their precursors as shown in Table S2).

1. Also related to cluster assignments: please specify if "excretory" category includes canal, duct, pore, gland all together, or only a subset of these. Only the duct and pore are cuticle lined and therefore expected to have oscillatory matrix gene expression.

We have changed this to "excretory cell" (or "exc cell") for clarity. We did not examine markers for the excretory duct, pore, or gland.

1. Figure 5. This figure feels disjointed and could be broken up into two figures (panels A-C and panels D-G). The first 3 panels seem more related to Figures 3 & 4 - identifying which cell types have strong pulsatile gene expression - whereas the later panels get into the degree of cell type specificity in matrix gene expression.

We appreciate the merit of this point and in fact we strongly considered splitting up this figure (in various ways) while writing. While we agree that the figure covers a lot of ground in this format, we feel that the subparts do not hold up as their own independent figures on equal footing with the other figures in the manuscript.

1. Figure 5D-E. The very low degree of sharing is fascinating but could be an underestimate that depends on the thresholds chosen for calling a gene "pulsatile". It may be helpful to test a range of thresholds to see how much this matters. For those ~2,500 genes that appear pulsatile in just one cell type, are they called expressed but non-pulsatile in other cell types? That would seem odd to me biologically and most likely a threshold artifact.

We have added the following caveat to the Results:

"Put another way, 45% (2,390 of 5,268) of the genes we identified were expressed and pulsatile exclusively in a single cell type while only 17% (915 of 5,268) were pulsatile in five or more cell types (Fig. 5E). A potential caveat to this conclusion would be if some genes are not categorized as pulsatile in particular cell types due to lower expression (e.g., falling into Cluster 7 with high peak amplitude in one cell type, and Cluster 8 with low peak amplitude in other cell types; see Fig. 4B-C). However, if this occurs, it affects only a minority of cases: among genes categorized as pulsatile in only one cell type, 82% are not detected as expressed in any of the other oscillatory cell types, indicating that the apparent specificity most likely reflects cell-type-specific gene expression rather than thresholding effects."

1. Figure 5F and p.21 Methods, the authors analyze only 140 collagen genes and 38 ZP domain genes retrieved from InterPro, but there are at least 173 cuticle collagen genes and 43 ZP domain genes described in the literature. Therefore, their lists are incomplete and the Methods should say so.

Thank you for pointing this out. We changed the gene list to the cuticular collagens listed in Teuscher (2019). This did not affect the figure in a major way. We retrieved 44 ZP domain genes from InterPro, which match the ones listed by Cohen (2019) with the addition of cutl-19.

1. If most oscillatory gene expression is truly a function of the molt cycle, as suggested by the matrix gene families in Figure 5, then one might expect that most of the detected oscillatory genes would no longer be expressed in adults, or at least wouldn't appear "pulsatile" in adults. Is this true? There now are a variety of published adult data sets, including the Purice et al data on glia, that could be examined to address this.

PCA of adult cells does not exhibit the circular structure necessary to assess pulsatile expression. Previous work showed that most oscillatory genes are not expressed in adults, as expected (Meeuse et al. 2020).

**Referees cross-commenting**

I agree with the other reviewers' critiques, including the point of Reviewer #2 that orthogonal confirmation methods (such as by imaging) could have been nice but are not necessary. The question of Reviewer #3 about tissue synchrony/asynchrony is a very important one but I am not confident it can be addressed with these types of data.

Reviewer #1 (Significance (Required)):

As a molting invertebrate, C. elegans must build and shed its protective cuticle at multiple times across its life cycle, and this requires temporal control of many genes involved in matrix structure and processing. Although temporal oscillations were already well documented from bulk RNAseq data, this manuscript extends those prior findings by showing that different sets of genes oscillate within different cell types (including sensory glia), and by identifying many apparent oscillatory genes that were missed in prior studies because they are expressed in smaller populations of cells (whereas bulk data mainly report on oscillations within the major hypodermis). These data about cell-type specific temporal programs and gene sets emphasize the exquisite specificity of apical matrix and will be broadly useful to researchers in the C. elegans community.

A second major contribution of this manuscript is to pioneer analysis methods for detecting oscillatory gene expression in scRNAseq datasets, even where bulk temporal data may not exist. This will be valuable for others doing sRNAseq studies in nematodes but also in other systems where cells may have molt cycle- or circadian-regulated oscillations.

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

SECTION A - Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors use single cell sequencing (scRNA-Seq ) of cells obtained from larval stages of C elegans -- primarily the L4 stage, but also the L2. Worms are disrupted and individual cells are sorted by expression of fluorescent markers specific to glial cells, a cell type that is relatively rare in the population, and of particular interest to the focus of the study. In this fashion, the samples were enriched for glial cells but, bedcause the soting is not perfect, also contain representations of other cell populations, including hypodermal (skin) and other epithelial cells, muscles, and neurons. 2D representation of the scRNA-Seq data in principle component (PC) space reveals sets of cells of the same cell type (for example glia or skin cells) arranged in roughly circular patterns, indicative of rhythmic gene expression in those cell types. Much of this circular PC behavior is shown to be driven by genes that had previously been shown, by bulk RNAseq of staged larvae, to undergo rhythmic gene expression in conjunction with the larval stages and the molts that punctuate the larval stages. Based on the previously published relative timing of expression of these cycling genes, and the pattern of peak expression of each gene in the scRNA-Seq 2D PC space, the authors could calculate a phase angle of expression of each gene relative to its peak in each cell, and thereby calculate an average phase angle of all cycling gene for each cell, and place that metric in register with the roughly circular pattern of cell types in the 2D PC plot.

The authors show that many of these rhythmic genes encode extracellular matrix (ECM) proteins or other proteins related to cuticle synthesis and assembly, or molting. Cell types exhibiting cyclic gene expression included skin, pharyngeal epithelial, as well as several types of glia, notably socket glia, which synthesize a specialized ECM that surrounds and protects sensory neurons.

Finally, the authors analyze the patterns of cyclic gene expression in several cell types with respect to the expression of transcription factors (TFs) that are expressed in the cell type, including TFs that appear to likewise cycle, and whose predicted targets are enriched for cycling genes. From this computational analysis, the authors derive sets of hypothetical transcriptional regulatory circuits underlying phased expression of cycling genes.

Major comments:

• Are the key conclusions convincing?

1) Yes, the data support the conclusion that the authors' approach and methodology can take a list of genes known to cycle in expression level at larval stages and identify the cycling gene expression profiles of those genes in single cell sequencing datasets. It is also convincing that the authors' data analysis methods can identify cycling genes from the scRNA-Seq data that had not been previously identified as cycling from bulk RNAseq. Furthermore, the enrichment of genes encoding collagens and other ECM components is clear from the data.

2) The above being said, it is noteworthy that the conclusions of the manuscript - including the sets of predicted novel cycling genes, and the predicted transcription factor-target circuits -- were not confirmed experimentally using independent samples or orthogonal methodology. I think it is OK for the authors to leave these predictions for later experimental confirmation, but it would be appropriate for the authors to discuss this caveat about the need for strategic experimental tests to confirm the more novel findings presented here, while at the same time pointing out predictions from their analysis that fit with previous experimental findings (for example cases such as NHR-85 and NHR-23 where previous studies support that the relevant TF is involved in regulating molting-associated transcriptional activity.)

We have added the following sentence to "Limitations of the study":

"Further, while our results are consistent with other studies (Meeuse et al. 2020; Gaidatzis et al. 2025) and successfully identify known regulators such as NHR-23 and NHR-85, it will be important in future work to test expression of the novel oscillatory genes and the roles of novel regulators we have predicted."

3) There is an issue of concern that is perhaps about terminology, and not necessarily conceptual: Throughout the manuscript the authors variously use the terms, "oscillatory", "transient", and "pulsatile" to refer to cyclic gene expression. It seems that each of these terms could have distinct meanings, based on their English usage: The term "oscillatory" gene expression would seem to be a general term for gene expression that varies in a regular, rhythmic fashion. "Transient" gene expression seems like a general term for ON/OFF dynamics, albeit not necessarily oscillatory. "Pulsatile" gene expression implies oscillatory dynamics where the rise and fall of gene expression is relatively abrupt and might also imply ON/Off dynamics (between zero to some positive value). These terms are used seemingly interchangeably in the early parts of the manuscript, and then later, "pulsatile" is used increasingly, so the reader starts to wonder why. The authors should define these terms precisely and use the terminology deliberately and consistently.

We have clarified the important point about oscillatory vs. pulsatile in the text. Please see our response to Reviewer 1, Point 5. Additionally, we have removed the use of "transient" except in the context of the phrase "transient aECM" that has been established in the literature.

4) Related to the above, the authors should address how lowly-expressed genes behave in scRNA-Seq data, where the transcriptome is not fully sampled in each cell, and how that phenomenon could affect the apparent variation of gene expression within a population. My understanding is that if the expression level of a gene goes below some threshold percentage of the total transcriptome, it may not show up at all in the reads from that cell, even though the gene may still be expressed. Therefore, a gene can display apparent on/off behavior within a population of cells whilst the underlying variation in mRNA levels for that gene may be far less abrupt. How might this phenomenon affect the interpretation of a gene's dynamics as "pulsatile"?

We added the following to clarify that sampling variation among cells was mitigated by applying a smoothing function based on each cell's five nearest neighbors in PCA space:

"We then fitted the expression pattern of each gene with a generalized additive model (GAM) to obtain smoothed expression profiles. Because the GAM is fitted across many cells ordered along pseudotime, it captures the underlying expression trend even when individual cells show zero counts due to incomplete transcriptome sampling (e.g., Fig. 4A, black dots at y = 0)."

As further described in Methods, our pipeline also incorporates several features that mitigate this valid concern:

• First, before fitting gene-level dynamics, we retain only genes detected in at least 20 cells and in at least 5% of cells of a given cell type (Methods). While this filter may exclude some genuinely low-expressed oscillating genes, it ensures that pulsatile calls are made on genes where expression is reliably measurable.
• Second, we apply two levels of smoothing. Prior to PCA, k-nearest-neighbor smoothing ensures that each cell's expression profile reflects a local average of transcriptionally similar cells rather than a single noisy measurement. When modeling gene expression along pseudotime, we fit a generalized additive model (GAM) with cyclic cubic splines, pooling information across many cells. The curves we score as pulsatile therefore reflect averaged expression across neighborhoods of cells, rather than raw per-cell counts subject to dropout.
• Critically, dropouts arising from incomplete transcriptome sampling are independent of pseudotime (e.g., see dnj-1 in Fig. S3A). Our pulsatility criterion explicitly requires a low baseline combined with a well-shaped, high-amplitude peak in a specific pseudotime window, which dropout noise alone cannot generate. Indeed, as shown in Fig. 4A, the method readily identifies peaks even when many individual cells have zero detected reads (black dots at y = 0), demonstrating that the smoothed fit recovers the underlying dynamics from sparse data.
• Finally, during development we also tested a logistic GAM that models the probability of detecting at least one read per cell, rather than read counts directly, which produced comparable results, though it saturated for highly expressed genes.

  • Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

5) Page 12: "Taken together, our results suggest that cuticle formation is the main commonality among pulsatile genes, and that distinct cell types use very different gene expression programs during this process. Thus, while cuticle aECM is typically perceived as a single homogeneous meshwork, our results suggest that the cuticle is actually a patchwork matrix with different patterning and composition contributed by distinct cell types."

It is not necessarily surprising that the cuticle made by skin cells could have composition non-identical to the cuticle made by glial cells or pharyngeal cells. But by describing the cuticle as a 'patchwork' elicits in the reader's mind an image of the skin of the animal (seam + Hyp) being mosaic for distinct cuticle compositions. Is that what the authors intend to say? It would be interesting if there were differences in composition of cuticle between skin cell types, and so it would be helpful if the authors could comment on how the transcript profiles compare for hypodermal seam cells vs multinucleate Hyp cells.

We have expanded on this idea:

"Taken together, our results suggest that cuticle formation is the main commonality among pulsatile genes, and that distinct cell types use very different gene expression programs during this process. Classical work showed that the cuticle exhibits regionalized specializations – for example, alae are present only over seam cells; annuli and struts are present over hyp7 but not near the nose; the vulval cuticle is thought to present structural or chemical signatures for recognition during mating; and the pharyngeal cuticle exhibits three short projections in the buccal cavity, sieve-like fingers between the metacorpus and isthmus, and grinder elements in the posterior bulb. However, the extent to which these structural differences correspond to distinct molecular composition was not known. Thus, while cuticle aECM is typically perceived as a single homogeneous meshwork, our Our results suggest that the cuticle is actually a patchwork matrix with different patterning and molecular composition contributed by distinct cell types."

• Would additional experiments be essential to support the claims of the paper?

6) The data here are mostly from L4 stage larvae, with a possible (but unknown) contribution from L2 larvae. It would be helpful, in terms of broader understanding of their roles in larval progression, if some of the oscillatory genes identified here (especially the novel ones) were tested by orthogonal methodology (such as fluorescent protein tagging) for oscillatory expression at other stages. However, these experiments are arguably beyond the scope of this paper, and as long as the authors note the importance of such confirmatory experiments in their Discussion, I don't think that further experimentation is critical for this paper.

We agree about the importance of these confirmatory experiments, and have added a comment in the Discussion (see response to Point 2 above).

• Are the data and the methods presented in such a way that they can be reproduced?

7) In general, yes.

• Are the experiments adequately replicated and statistical analysis adequate?

8) Yes.

Minor comments:

• Specific experimental issues that are easily addressable.

9) Page 4: Regarding the single cell sequencing approach, the authors should comment on the extent to which mRNAs are efficiently recovered from hypodermal syncytial cells (Hyp), which are multinucleate. Could the data from Hyp be chiefly from nuclear transcripts? If so, how might that affect the interpretation of the data?

We have added a comment in Methods related to caveats of cell sorting vs. nuclei sorting (see response to Reviewer 1, Point 2). As the proportion of immature (unspliced) mRNA and reads corresponding to the mitochondrial genome are not noticeably different in the hypodermal cells than in other cell types, we do not think the data are chiefly from nuclear transcripts.

10) It is confusing that Table S1 lists male-enriched samples that were apparently sequenced, but only hermaphrodite data were analyzed for the paper. To prevent confusion, the male samples should not be listed.

We have clarified in the Methods that these samples are included in Table S1 because we wanted to share the datasets with the community:

"(Supp. Table S1; note this table includes related samples that were not used in the present analysis but that are deposited in the Gene Expression Omnibus (GEO) repository as a public resource)"

11) Page 5, bottom: The following analysis requires clarification (at least for this reader): "To test if such oscillatory gene expression is present in ILso glia, we computed the average phase of each cell (Fig. 2B). Specifically, for each cell, we computed a weighted circular average of the peak phases of oscillating genes (derived from the previous bulk RNA-Seq data), using the gene expression levels in that cell as weights."

In reading this part of the main text, this reader struggled to understand how one can compute the phase angle for a given gene in a cell by comparing its level of expression in that cell to measurement of the level of that gene in previous bulk RNA-Seq data. Of course, there is far more to the analysis than that, which the Methods and Materials section on page 18 describes in more detail, where one learns that the level if each gene in each cell is scaled to its maximum expression across all the cells analyzed, and that the previous bulk sequence analysis is used to simply provide a phase angle for the gene's peak expression relative to an arbitrary framework (which corresponds to a larval stage, one assumes). The presentation of this analysis on Page 5 in the main text should be revised to include a full description of what was done so the reader can follow along and understand it without having to read the Methods section. But moreover, the Methods section treatment of this analysis is still not entirely clear; for example, certain variables (W, s, and c) are not defined. The presentation of the mathematics should be clarified so that the reader can understand the analysis without having to look up scTransform-normalization.

We have expanded and clarified this section:

"To test if such oscillatory gene expression is present in ILso glia, we computed the average phase of each cell (Fig. 2B). Specifically, for each cell in our dataset, we considered its expression level of each of the 3,739 previously described oscillatory genes (Meeuse et al. 2020). To avoid biasing towards inherently highly-expressed genes (e.g., those encoding structural proteins), the expression of each gene in a given cell was scaled to its maximum expression across all cells. We then computed the average phase of each cell by taking the known phase for each gene (Meeuse et al. 2020) and calculating a weighted circular average, using the scaled expression of each gene in that cell as weights (Fig. 2B; each colored line represents one oscillatory gene with its angle representing its known phase and its length representing its scaled expression in that cell). we computed a weighted circular average of the peak phases of oscillating genes (derived from the previous bulk RNA-Seq data), using the gene expression levels in that cell as weights. This average results in a vector whose direction reflects the average phase of genes expressed in that cell, and whose length reflects how consistently the genes’ peak times align in that cell (Fig. 2B, black arrow)."

In the Methods, we have moved the definitions of W, s, and c so that they precede the formula for the average angle .

• Are prior studies referenced appropriately?

12) yes

• Are the text and figures clear and accurate? - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

13) Figure S3 Panel A: What does the green line mean? Figure S3 Panel C: The use of the "predictors" tem is confusing because on page 8, the part of the narrative referring to Figure S3, the term used is "descriptors". Is that an meningful switch in terminology?

We have expanded and clarified the Supp. Fig. S3 legend. For simplicity, we now use the term "metrics" to refer to the parameters used for hierarchical clustering of pulsatile expression (peak amplitude, baseline, fit, shape). This replaces our previous uses of "predictors" and "descriptors".

14) The legend to Figure S3 requires more details to enable the reader understand the Figure. The same critique applies to most of the Supplemental Figure legends, where more details are required to allow the reader to understand each Figure without having to refer back to the main text.

Thank you for pointing this out. We have revised and expanded all of the Supplemental Figure legends.

15) Page 19: "The cells were grouped by cell type independent of the stage of collection (L2 or L4), and each cell type was processed individually."

Why were L2s and L4s pooled? How does this affect the analysis and/or the outcomes? Could there be confounding effects from pooling the samples that could affect the analysis or the conclusions?

We added the following clarification in the main text:

"Because we found that cells clustered together based on their cell type rather than developmental stage, L2 and L4 cells of the same cell type were pooled for all downstream analyses (see Methods)."

as well as the following explanation in the Methods:

"The cells corresponding to the same cell type at different stages were then merged for subsequent analysis. After annotation, cells of the same cell type from L2 and L4 datasets were pooled for downstream analysis, such that each cell type is represented as a single combined cluster across stages. This provides two advantages: it increases statistical power by increasing the number of cells, and it favors genes that are oscillating in both larval stages. Because L2 representation is more limited (Table S1), the pooled pseudotime is dominated by L4 dynamics, ensuring that L2 cells are anchored on the L4-defined trajectory."

**Referees cross-commenting**

There is substantial agreement amongst all three reviewers, regarding the signifcance of the findings and that the conclusions are well enough supported by the data such that no additional experiments are required. We all recommend revisions to clarify or expand the description of the experiments and/or analysis. Many comments are reiterated by more than one Reviewer. I agree with all the other reviewers' critiques.

Reviewer #2 (Significance (Required)):

SECTION B - Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

The finding of oscillatory and molting-related gene expression patterns in glial cells emphasizes the importance of molting-related ECM/cuticle production by these sensory-accessory cells and will serve as a platform for further studies and further understanding the structural and molecular basis of glial cell support functions, especially in the context of changing roles for sensory neurons during developmental progression.

The methodology and data analysis of C. elegans scRNA-Seq data presented here offers several significant advances, especially since it had been known that thousands of genes cycle in rhythm with the C. elegans molting cycle, yet that was based on previous bulk sequencing, so it was not possible to resolve cell-type specific expression. This paper presents methods for analysis of cycling gene expression in specific cell types.

The manuscript derives hypothetical TF-target regulatory interactions that are proposed do underly cyclic gene expression in specific cell types. This is a significant resource for future work to explore and delineate upstream oscillator mechanisms, and answer questions such as, Is there a central oscillator for all of larval stage rhythmic gene expression? and, How are different genes expressed with different phases of the larval stages? etc.

• Place the work in the context of the existing literature (provide references, where appropriate).

The authors cite important previous studeis that used scRNA-Seq to profile gene expression in specific C. elegans cell type in various developmental and physiological settings, and previous studies that used bulk RNAseq to identify genes whose transcripts cycle along with the larval stages. This manuscript reports the first study to examine cyclic gene express in C. elegans on the single-cell level.

• State what audience might be interested in and influenced by the reported findings.

Moderately broad audience of biologists interested in biological oscillators; developmental biologists interested in gene regulatory control of developmental cell fate timing and reiterative developmental processes; neurobiologists interested in glial cell function in developmental contexts.

• Define your field of expertise with a few keywords to help the authors contextualize your point of view.

• C. elegans larval development; temporal control of cell fate progression. Are there are any parts of the paper that you do not have sufficient expertise to evaluate.

Honestly, some of the mathematical analysis is beyond my ability to judge whether the chosen approach is the best choice for the particular setting.

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

This study describes both new scRNA-seq data from C. elegans, targeting glia/epidermal cell types and especially the ILso glial cell, and analytical approaches to identify periodically expressed genes in the dataset. Overall the data appear of high quality so have value as a resource, and the analysis provides a substantial improvement in our understanding of how different cell types vary in their cyclic expression across the molt cycles. While I have make many suggestions, overall this is a very nice study as is and definitely seems likely to be an impactful publication.

Major

Figure 2:

• The dataset includes cells from multiple stages (L2 and L4 mentioned in the text, adult as well listed in Supplemental Table 1). There is a superficial display in Figure S1 which seems to imply that whether the same cell type clusters together across stages vs making stage specific clusters might be complex. But this isn't really discussed at all in the paper. For Figure 2 specifically it seems critical to know whether stages were pooled or separated for this analysis, and the question of whether the cyclic program varies across stages (at least for well sampled cells like ILso) is important.

Please see our response to Reviewer 2, Point 15.

Figure 3

• This approach overall is good for cells that cycle in a way their signature comes up in Meeuse but would it detect rare cell type cycles? Maybe the PCA space velocity approach could be a way to screen for cell types that cycle in a way that isn't detected in the whole organism time course data (or rule out the presence of large cycling gene sets)? For example "pharyngeal gland" seems to have a weak cycling signature using the Meeuse gene set (Fig. 3D) but fairly clear "circular UMAP" structure (Fig 3B).

We added the following to emphasize that our rationale for developing the perplexity metric is to identify oscillatory cell types de novo, i.e. without relying on the Meeuse et al. dataset:

"We hypothesized that this [perplexity] metric would distinguish between pulsatile cell types (corresponding to relatively high perplexity) and non-pulsatile cell types (corresponding to low perplexity), without relying on prior bulk annotations that may be insensitive to rare cell types."

Consistent with the reviewer's intuition, this approach does identify cell types missed by the Meeuse-based local phase coherence analysis, specifically coelomocytes and PHsh glia, which have perplexity >30 but did not reach significance by phase coherence (Fig. 5C).

Regarding the pharyngeal gland, this cell type has intermediate scores by both metrics and falls below our conservative thresholds (Fig. 5C). It is possible that it has a genuine but weak oscillatory program that our methods are underpowered to detect given the number of cells recovered for this cell type.

We considered using RNA velocity, but we have not succeeded in developing a satisfying quantitative score; therefore, the perplexity metric serves this role in our current analysis.

• Do these data say anything about the question of whether all cell types in an organism are synchronized in the same phase as each other, or whether some might be systematically earlier or later in the cycle at a given time? It seems like if individual samples have enough stage bias (as an illustrative but made up example, if sample "230421_AM" has mostly early L4 while "230421_PM" has mostly late L4), then these data could be used to see if for example ILso cells tend to have earlier or later phases in the same sample compared to hyp cells. In my view, this is an important enough general question in the field to be worth addressing if the data are sufficient. And it could also provide an independent way to support/refute the presence of additional cycling cells (see Fig. 5 comments)

This is an interesting idea, but unfortunately our synchronization at the population level is not sufficiently precise, and each sample contains cells spanning nearly the full phase range (shown below [IMAGE CANNOT BE ATTACHED HERE]). Under these conditions, between-sample phase offsets are dominated by within-sample dispersion, and we cannot reliably estimate systematic phase differences between cell types.

Figure 5

• This seems a nice approach to address the earlier question about detecting cell type specific oscillations. But then only results for the cell types previously identified as oscillatory are reported. It seems important to report the potential cycling genes for the other cell types (PHsh, Coelomocytes, maybe Pharyngeal Gland) so their cycling status could be tested by others in the future.

We revised the text to highlight that these gene lists are in Supp. Tables S3 and S4.:

"We limit our subsequent analyses to the 17 high-confidence cell types that appear oscillatory using both approaches (local phase coherence and perplexity), which together contain 5,268 pulsatile genes. Pulsatile gene lists for these and other cell types are provided in Supp. Tables S3 and S4 to facilitate independent assessment of their cycling status. A summary of pulsatile genes in these 17 cell types is shown in Table 1."

• Regarding the last section ("only 17% were pulsatile in five or more cell types", "only 10 genes were pulsatile in all 17 oscillatory cell types" etc) - thresholding of a dataset like this can lead to false negatives resulting from incomplete (and cell type specific differences in power) which is a common source of technical non-overlap in this type of comparison. Indeed it is notable that the highest overlap was with ILso (specific sort target, likely to be especially well powered) and CEPso. There are various approaches to estimate not just confident overlap but also confident non-overlap, for example the "irreproducible discovery rate" (IDR) approach commonly used for ChIP-seq data. While clearly based on gene set enrichment there is cell type specificity, I'd suggest toning down the interpretation of the fractional overlap in the text if this can't be resolved.

We toned down the interpretation of the fractional overlap:

"To what extent are the same sets of pulsatile genes shared between cell types? To address this question, we examined the overlap between the pulsatile genes we identified in each cell type (Fig. 5D), noting that because power to detect pulsatile expression varies across cell types, the overlap values we report are likely to underestimate the true sharing between cell types.

[…]

Put another way, 45% (2,390 of 5,268) of the genes we identified were detected as expressed and pulsatile exclusively in a single cell type while only 17% (915 of 5,268) were pulsatile in five or more cell types (Fig. 5E)."

Minor

Figure 1:

• I was a little unclear about the coloring in Fig 1C (are the colors by annotated tissue or something else like clusters?) - suggest specifying in the legend.

We updated the legend: "UMAP of the same cells as in B, with each cell colored by its annotated tissue identity."

• More details on clustering and annotations approaches in the methods would be useful.

We have substantially expanded the corresponding section.

• I have mixed feelings about the word "skin" in the figure panels - while more accessible to a broad audience, hypodermis or hyp subset labels (hyp 7 etc) might be more precise.

We have changed many of these to "skin-related." We cannot use the anatomical terms because we cannot confidently distinguish, for example, hyp1 vs hyp2, due to the lack of known markers for each cell type. We therefore refer to skin-related cluster 3 as "skin 3," because calling it "hyp 3" would lead to confusion with the anatomical term.

• Table S2 would benefit from including the number of cells annotated with each cell type name

We have added the number of cells per cell type to Supp. Table S2, with separate columns for L2, L4, and the total.

Figure 2

• Fig 2B is nice - clearly shows the difference in expression of phase specific genes in the two example cells and conceptual framework for averaging. I was struck by the relatively broad range of phase values though (For example the bottom cell has highly expressed genes with phases ranging from ~100 degrees to ~280). It seems this could reflect technical noise in the single cell data or imprecision in the phase calls in Meeuse. But there is also the interesting possibility that there is biological flexibility in the order/expression of phased genes at this single cell level. Not sure if there is an obvious way to address this or whether it should be in the scope of this work but maybe at least worthy of a mention

A parsimonious explanation for the broad range of phase values in a single cell is the shape of the peak: examining the data from Meeuse et al, oscillatory genes do not generally display a sharp peak, but rather elevated expression over a span of ~3h (out of a larval stage of ~8h), which would correspond to expression over 100°. Indeed, the decentered genes in Fig. 2B correspond to the genes F53F4.2 and cutl-10 which have their peak expression at ~135° (26 h of larval development in the Meeuse dataset) but are still expressed at ~180° (28 h of larval development in the Meeuse dataset). Importantly, expression peaks tend to be roughly symmetric around the cell's true phase and therefore reduce the length of the phase vector but do not affect the average phase itself.

Figure 3

• The class Alter et al SVD paper https://www.pnas.org/doi/full/10.1073/pnas.97.18.10101 was the first use case of SVD/PCA in genome wide expression data and used (cell cycle) periodic expression as the main use case. The plots in Figures 2 and 3 are very similar to that approach, which basically used the relevant (~sin and ~cos correlated) principle components to define phases of both samples and genes. I mention this mostly in case it is useful to see how they approached the question and maybe as a relevant citation.

We added the citation.

Figure 4

• Minor method clarification - how was DTW adapted to deal with circular data, specifically to identify cases where the peak is centered at pseudotime == 0/1? It seems from the figures that maybe some approach was used to center the raw data on the peak but I didn't see a description of how this was done (apologies if I missed it)

We edited the Methods to make the connection with the previous section more explicit:

"We used the trained model to predict expression of each gene along a grid of 128 regularly spaced pseudotime values, resulting in a smoothed expression profile. Further, for each gene, we shifted the pseudotime values to center the maximal expression value, and fitted a GAM as described above. To facilitate comparison of profile shapes across genes with different peak times, we additionally produced a centered version of each profile. For each gene, we identified the pseudotime at which the uncentered profile reached its maximum, then circularly shifted the pseudotime values so that this maximum fell at the center of the range (pseudotime 0.5). A new GAM was fit on the shifted data as described above, and used to predict expression along the same regular grid. This yielded a centered, smoothed expression profile for each gene in which all genes have their peak at the center of the pseudotime axis. These centered profiles were used in the subsequent section to compute both the baseline and shape metrics of each gene.

[…]

We then scaled the curve by its maximum value and centered it around its maximal value. We then scaled the centered smoothed expression profile (defined in the previous section) by its maximum value. The Dynamic Time Warp distance between the scaled and centered expression and an ideal sharp peak defined as the density of a normal distribution of mean 0.5 and standard deviation 0.01 was computed with the dtw package."

• The 2-PC view of ILso seems to align well with phase, but some of the other cell types (such as Seam in Figure 3C) are more complex - and also it seems possible that there could be cell types where the phase information is in e.g. PC2 and 3 instead of 1 and 2; how customizable is the approach and how dependent is it on a clean circular pattern in the PC plot?

• *

We have expanded the Discussion to include this point:

"This could indicate either a genuine absence of oscillatory programs; the presence of oscillations driven by only a few genes that are insufficient to shape PCA structure; or oscillations that are present but reside in higher principal components dominated in PCs 1-2 by other sources of cell-to-cell variation."

By using an Elastic Principal Cycle (ElPiGraph) to fit pseudotime rather than relying on angle from the origin (as is common for this type of data), we accommodate trajectories within PCs 1-2 that deviate from perfect circularity, including elongated or asymmetric shapes such as in seam cells (Fig. 3C). However, when phase information resides in higher-order PCs, in the absence of an independent timing reference there is no principled way to identify which PCs carry oscillatory signal versus other gradients of cell-to-cell variation. Recovering oscillations in such cell types would therefore require complementary approaches, such as synchronized time-course sampling, rather than a modification of the current pipeline.

• It would be useful to annotate the examples (Fig 4A, lower panels) with whether they were newly identified or known from the bulk time course. And consider a larger supplemental figure with a sampling of newly identified genes in a similar format across a range of amplitudes etc

We added Supplementary Figure S4C with examples across a range of amplitudes.

• The examples are all relatively tight peaks (width We developed an approach to quantify the width of peaks in the Meeuse data (Methods); we display the distribution of peak width for genes expressed in ILso and seam cells in the new Supplementary Figure S4A. Our approach did not display a systematic bias to detect narrow or wide peaks. We added the following in the Results:

“More generally, our classification captures a range of expression profile morphologies without apparent bias (Supp. Fig. S4).”

Figure 5

• There are important caveats in the interpretation of perplexity. For example a cell type that oscillates but with the vast majority of genes expressed uniformly or at one specific phase, would get a low perplexity, while a cell with multiple distinct states that don't cycle (this may be why body muscle has a modestly elevated sore) might achieve high perplexity. Worth addressing at some point.

We added these caveats:

"Potential caveats are that some non-oscillatory cell types might have high perplexity, for example if there are other sources of complex transcriptional heterogeneity among cells, while some oscillatory cell types might have low perplexity, for example if oscillating genes do not dominate the PCA structure."

• Fig 5C raises the question of how power (for each of these metrics) relates to number of cycling genes in a cell type and the density of its sampling across time (for example is glia 4 just a poorly sampled cell type, or is it qualitatively different in what fraction of its transcriptome is cycling?). Just recoloring this plot by number of single cells per annotation might touch on this, or could try a subsampling approach.

We added this with the new Supp. Fig. S5C:

"To test whether differences in perplexity could be explained by differences in the number of sampled cells, we recomputed perplexity after subsampling to progressively smaller numbers of cells for several representative cell types. Perplexity values were largely stable across subsample sizes, indicating that the classification of cell types as oscillatory or non-oscillatory is not driven by differences in statistical power (Supp. Fig. S5C)."

• The identification of pharyngeal muscle and epithelial oscillatory genes is a nice resource aspect of this paper given past work by EM showing these cells changing across the life cycle; it appears these cells have distinct enrichments (Fig 5G) and I think talking about these differences more explicitly could add to the closing paragraph in this section about aECM heterogeneity

We have added the following:

"In addition, the nematode astacin (NAS) metalloproteases appeared enriched in pulsatile genes in glia and pharynx, but not hypodermis (Fig. 5G, Supp. Table S6), consistent with ultrastructural observations that the pharyngeal muscle becomes secretory during molts and that the protease NAS-6 is required to digest the old pharyngeal cuticle (Sparacio et al., 2020)."

Figure 6

• This section is great and a very useful resource for future work. A detailed analysis may be beyond the scope of this work, but for Fig 6B I wondered whether the TF oscillation phase matched/preceded the timing of its predicted targets (for the subset of TFs that were themselves oscillatory in that cell type)? Even a qualitative analysis of this would be informative.

We added a new supplementary Figure S7 and commented on it in the text:

"__For the subset of TFs that are themselves pulsatile, we asked whether their peak expression coincides with or precedes that of their predicted targets. We found that pulsatile targets are modestly enriched in a temporal window around the TF's own peak (Supp. Fig S7), consistent with near-simultaneous expression of TFs and their targets, as previously observed for nhr-23 (Johnson et al., 2023). This temporal enrichment was most consistent for nhr-23 and nhr-25, which showed significant enrichment across most cell types, while other TFs showed more variable patterns (Supp. Fig. S7)."__

Open-ended/discretionary

A general challenge in single cell data analysis is that standard methods like clustering can give misleading or hard to interpret results when multiple processes occur simultaneously. For example, cells can have signatures of cell fate and cell cycle and depending on the genes used for clustering and strengths of those signals, naïve clustering may cause them to group by either fate of cell cycle phase. This is a long-winded way to say an application of the approach reported here would be to identify cycling genes shared between cell types that could be removed from the "variably expressed genes" lists prior to clustering to improve cell type separation, or used exclusively to allow clustering by phase rather than cell type. (definitely discretionary to consider this but could be mentioned in Discussion as a possible application)

**Referees cross-commenting**

I agree with all of this, including Reviewer #1 that asynchrony may be hard to address with current data, and with both reviewers that the dataset stands on its own.

Reviewer #3 (Significance (Required)):

This paper addresses the problem of how to identify cycling genes in single cell data, using the C. elegans larval/molt cycle as a model system. The system has emerged as a powerful model for understanding regulation of periodic gene expression, with past bulk RNA-seq time course have identified 1000s of cycling genes. However, how cyclic gene expression varies across cell types was not known. This study uses single cell RNA-seq and develops new analysis approaches to identify cycling genes across dozens of C. elegans cell types. Strengths are the generation of a new single cell data enriched for larval glia, identification of cyclic gene expression across many C. elegans cell types, an improved analytical framework for identifying cycling genes that could be applied in other datasets, and substantial analysis of pathways and regulators involved. Weaknesses are limited, and include minor overinterpretations of the data and missed opportunities for additional analyses. The work should be of interest to a broad audience including not just C. elegans researchers but also the single cell and chronobiology communities.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

This study describes both new scRNA-seq data from C. elegans, targeting glia/epidermal cell types and especially the ILso glial cell, and analytical approaches to identify periodically expressed genes in the dataset. Overall the data appear of high quality so have value as a resource, and the analysis provides a substantial improvement in our understanding of how different cell types vary in their cyclic expression across the molt cycles. While I have make many suggestions, overall this is a very nice study as is and definitely seems likely to be an impactful publication.

Major

Figure 2:

• The dataset includes cells from multiple stages (L2 and L4 mentioned in the text, adult as well listed in Supplemental Table 1). There is a superficial display in Figure S1 which seems to imply that whether the same cell type clusters together across stages vs making stage specific clusters might be complex. But this isn't really discussed at all in the paper. For Figure 2 specifically it seems critical to know whether stages were pooled or separated for this analysis, and the question of whether the cyclic program varies across stages (at least for well sampled cells like ILso) is important.

Figure 3

• This approach overall is good for cells that cycle in a way their signature comes up in Meeuse but would it detect rare cell type cycles? Maybe the PCA space velocity approach could be a way to screen for cell types that cycle in a way that isn't detected in the whole organism time course data (or rule out the presence of large cycling gene sets)? For example "pharyngeal gland" seems to have a weak cycling signature using the Meeuse gene set (Fig. 3D) but fairly clear "circular UMAP" structure (Fig 3B).
• Do these data say anything about the question of whether all cell types in an organism are synchronized in the same phase as each other, or whether some might be systematically earlier or later in the cycle at a given time? It seems like if individual samples have enough stage bias (as an illustrative but made up example, if sample "230421_AM" has mostly early L4 while "230421_PM" has mostly late L4), then these data could be used to see if for example ILso cells tend to have earlier or later phases in the same sample compared to hyp cells. In my view, this is an important enough general question in the field to be worth addressing if the data are sufficient. And it could also provide an independent way to support/refute the presence of additional cycling cells (see Fig. 5 comments)

Figure 5

• This seems a nice approach to address the earlier question about detecting cell type specific oscillations. But then only results for the cell types previously identified as oscillatory are reported. It seems important to report the potential cycling genes for the other cell types (PHsh, Coelomocytes, maybe Pharyngeal Gland) so their cycling status could be tested by others in the future.
• Regarding the last section ("only 17% were pulsatile in five or more cell types", "only 10 genes were pulsatile in all 17 oscillatory cell types" etc) - thresholding of a dataset like this can lead to false negatives resulting from incomplete (and cell type specific differences in power) which is a common source of technical non-overlap in this type of comparison. Indeed it is notable that the highest overlap was with ILso (specific sort target, likely to be especially well powered) and CEPso. There are various approaches to estimate not just confident overlap but also confident non-overlap, for example the "irreproducible discovery rate" (IDR) approach commonly used for ChIP-seq data. While clearly based on gene set enrichment there is cell type specificity, I'd suggest toning down the interpretation of the fractional overlap in the text if this can't be resolved.

Minor

Figure 1:

• I was a little unclear about the coloring in Fig 1C (are the colors by annotated tissue or something else like clusters?) - suggest specifying in the legend.
• More details on clustering and annotations approaches in the methods would be useful.
• I have mixed feelings about the word "skin" in the figure panels - while more accessible to a broad audience, hypodermis or hyp subset labels (hyp 7 etc) might be more precise.
• Table S2 would benefit from including the number of cells annotated with each cell type name

Figure 2

• Fig 2B is nice - clearly shows the difference in expression of phase specific genes in the two example cells and conceptual framework for averaging. I was struck by the relatively broad range of phase values though (For example the bottom cell has highly expressed genes with phases ranging from ~100 degrees to ~280). It seems this could reflect technical noise in the single cell data or imprecision in the phase calls in Meeuse. But there is also the interesting possibility that there is biological flexibility in the order/expression of phased genes at this single cell level. Not sure if there is an obvious way to address this or whether it should be in the scope of this work but maybe at least worthy of a mention

Figure 3

• The class Alter et al SVD paper https://www.pnas.org/doi/full/10.1073/pnas.97.18.10101 was the first use case of SVD/PCA in genome wide expression data and used (cell cycle) periodic expression as the main use case. The plots in Figures 2 and 3 are very similar to that approach, which basically used the relevant (~sin and ~cos correlated) principle components to define phases of both samples and genes. I mention this mostly in case it is useful to see how they approached the question and maybe as a relevant citation.

Figure 4

• Minor method clarification - how was DTW adapted to deal with circular data, specifically to identify cases where the peak is centered at pseudotime == 0/1? It seems from the figures that maybe some approach was used to center the raw data on the peak but I didn't see a description of how this was done (apologies if I missed it)
• The 2-PC view of ILso seems to align well with phase, but some of the other cell types (such as Seam in Figure 3C) are more complex - and also it seems possible that there could be cell types where the phase information is in e.g. PC2 and 3 instead of 1 and 2; how customizable is the approach and how dependent is it on a clean circular pattern in the PC plot?
• It would be useful to annotate the examples (Fig 4A, lower panels) with whether they were newly identified or known from the bulk time course. And consider a larger supplemental figure with a sampling of newly identified genes in a similar format across a range of amplitudes etc
• The examples are all relatively tight peaks (width <0.5 pseudotime units) - is this approach able to identify genes with wider "plateau" patterns (and do such patterns exist?) Figure 5
• There are important caveats in the interpretation of perplexity. For example a cell type that oscillates but with the vast majority of genes expressed uniformly or at one specific phase, would get a low perplexity, while a cell with multiple distinct states that don't cycle (this may be why body muscle has a modestly elevated sore) might achieve high perplexity. Worth addressing at some point.
• Fig 5C raises the question of how power (for each of these metrics) relates to number of cycling genes in a cell type and the density of its sampling across time (for example is glia 4 just a poorly sampled cell type, or is it qualitatively different in what fraction of its transcriptome is cycling?). Just recoloring this plot by number of single cells per annotation might touch on this, or could try a subsampling approach.
• The identification of pharyngeal muscle and epithelial oscillatory genes is a nice resource aspect of this paper given past work by EM showing these cells changing across the life cycle; it appears these cells have distinct enrichments (Fig 5G) and I think talking about these differences more explicitly could add to the closing paragraph in this section about aECM heterogeneity

Figure 6

• This section is great and a very useful resource for future work. A detailed analysis may be beyond the scope of this work, but for Fig 6B I wondered whether the TF oscillation phase matched/preceded the timing of its predicted targets (for the subset of TFs that were themselves oscillatory in that cell type)? Even a qualitative analysis of this would be informative.

Open-ended/discretionary

A general challenge in single cell data analysis is that standard methods like clustering can give misleading or hard to interpret results when multiple processes occur simultaneously. For example, cells can have signatures of cell fate and cell cycle and depending on the genes used for clustering and strengths of those signals, naïve clustering may cause them to group by either fate of cell cycle phase. This is a long-winded way to say an application of the approach reported here would be to identify cycling genes shared between cell types that could be removed from the "variably expressed genes" lists prior to clustering to improve cell type separation, or used exclusively to allow clustering by phase rather than cell type. (definitely discretionary to consider this but could be mentioned in Discussion as a possible application)

Referees cross-commenting

I agree with all of this, including Reviewer #1 that asynchrony may be hard to address with current data, and with both reviewers that the dataset stands on its own.

Significance

This paper addresses the problem of how to identify cycling genes in single cell data, using the C. elegans larval/molt cycle as a model system. The system has emerged as a powerful model for understanding regulation of periodic gene expression, with past bulk RNA-seq time course have identified 1000s of cycling genes. However, how cyclic gene expression varies across cell types was not known. This study uses single cell RNA-seq and develops new analysis approaches to identify cycling genes across dozens of C. elegans cell types. Strengths are the generation of a new single cell data enriched for larval glia, identification of cyclic gene expression across many C. elegans cell types, an improved analytical framework for identifying cycling genes that could be applied in other datasets, and substantial analysis of pathways and regulators involved. Weaknesses are limited, and include minor overinterpretations of the data and missed opportunities for additional analyses. The work should be of interest to a broad audience including not just C. elegans researchers but also the single cell and chronobiology communities.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors use single cell sequencing (scRNA-Seq ) of cells obtained from larval stages of C elegans -- primarily the L4 stage, but also the L2. Worms are disrupted and individual cells are sorted by expression of fluorescent markers specific to glial cells, a cell type that is relatively rare in the population, and of particular interest to the focus of the study. In this fashion, the samples were enriched for glial cells but, bedcause the soting is not perfect, also contain representations of other cell populations, including hypodermal (skin) and other epithelial cells, muscles, and neurons. 2D representation of the scRNA-Seq data in principle component (PC) space reveals sets of cells of the same cell type (for example glia or skin cells) arranged in roughly circular patterns, indicative of rhythmic gene expression in those cell types. Much of this circular PC behavior is shown to be driven by genes that had previously been shown, by bulk RNAseq of staged larvae, to undergo rhythmic gene expression in conjunction with the larval stages and the molts that punctuate the larval stages. Based on the previously published relative timing of expression of these cycling genes, and the pattern of peak expression of each gene in the scRNA-Seq 2D PC space, the authors could calculate a phase angle of expression of each gene relative to its peak in each cell, and thereby calculate an average phase angle of all cycling gene for each cell, and place that metric in register with the roughly circular pattern of cell types in the 2D PC plot.

The authors show that many of these rhythmic genes encode extracellular matrix (ECM) proteins or other proteins related to cuticle synthesis and assembly, or molting. Cell types exhibiting cyclic gene expression included skin, pharyngeal epithelial, as well as several types of glia, notably socket glia, which synthesize a specialized ECM that surrounds and protects sensory neurons.

Finally, the authors analyze the patterns of cyclic gene expression in several cell types with respect to the expression of transcription factors (TFs) that are expressed in the cell type, including TFs that appear to likewise cycle, and whose predicted targets are enriched for cycling genes. From this computational analysis, the authors derive sets of hypothetical transcriptional regulatory circuits underlying phased expression of cycling genes.

Major comments:

• Are the key conclusions convincing?

1) Yes, the data support the conclusion that the authors' approach and methodology can take a list of genes known to cycle in expression level at larval stages and identify the cycling gene expression profiles of those genes in single cell sequencing datasets. It is also convincing that the authors' data analysis methods can identify cycling genes from the scRNA-Seq data that had not been previously identified as cycling from bulk RNAseq. Furthermore, the enrichment of genes encoding collagens and other ECM components is clear from the data.

2) The above being said, it is noteworthy that the conclusions of the manuscript - including the sets of predicted novel cycling genes, and the predicted transcription factor-target circuits -- were not confirmed experimentally using independent samples or orthogonal methodology. I think it is OK for the authors to leave these predictions for later experimental confirmation, but it would be appropriate for the authors to discuss this caveat about the need for strategic experimental tests to confirm the more novel findings presented here, while at the same time pointing out predictions from their analysis that fit with previous experimental findings (for example cases such as NHR-85 and NHR-23 where previous studies support that the relevant TF is involved in regulating molting-associated transcriptional activity.)

3) There is an issue of concern that is perhaps about terminology, and not necessarily conceptual: Throughout the manuscript the authors variously use the terms, "oscillatory", "transient", and "pulsatile" to refer to cyclic gene expression. It seems that each of these terms could have distinct meanings, based on their English usage: The term "oscillatory" gene expression would seem to be a general term for gene expression that varies in a regular, rhythmic fashion. "Transient" gene expression seems like a general term for ON/OFF dynamics, albeit not necessarily oscillatory. "Pulsatile" gene expression implies oscillatory dynamics where the rise and fall of gene expression is relatively abrupt and might also imply ON/Off dynamics (between zero to some positive value). These terms are used seemingly interchangeably in the early parts of the manuscript, and then later, "pulsatile" is used increasingly, so the reader starts to wonder why. The authors should define these terms precisely and use the terminology deliberately and consistently.

4) Related to the above, the authors should address how lowly-expressed genes behave in scRNA-Seq data, where the transcriptome is not fully sampled in each cell, and how that phenomenon could affect the apparent variation of gene expression within a population. My understanding is that if the expression level of a gene goes below some threshold percentage of the total transcriptome, it may not show up at all in the reads from that cell, even though the gene may still be expressed. Therefore, a gene can display apparent on/off behavior within a population of cells whilst the underlying variation in mRNA levels for that gene may be far less abrupt. How might this phenomenon affect the interpretation of a gene's dynamics as "pulsatile"? - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

5) Page 12: "Taken together, our results suggest that cuticle formation is the main commonality among pulsatile genes, and that distinct cell types use very different gene expression programs during this process. Thus, while cuticle aECM is typically perceived as a single homogeneous meshwork, our results suggest that the cuticle is actually a patchwork matrix with different patterning and composition contributed by distinct cell types."

It is not necessarily surprising that the cuticle made by skin cells could have composition non-identical to the cuticle made by glial cells or pharyngeal cells. But by describing the cuticle as a 'patchwork' elicits in the reader's mind an image of the skin of the animal (seam + Hyp) being mosaic for distinct cuticle compositions. Is that what the authors intend to say? It would be interesting if there were differences in composition of cuticle between skin cell types, and so it would be helpful if the authors could comment on how the transcript profiles compare for hypodermal seam cells vs multinucleate Hyp cells. - Would additional experiments be essential to support the claims of the paper?

6) The data here are mostly from L4 stage larvae, with a possible (but unknown) contribution from L2 larvae. It would be helpful, in terms of broader understanding of their roles in larval progression, if some of the oscillatory genes identified here (especially the novel ones) were tested by orthogonal methodology (such as fluorescent protein tagging) for oscillatory expression at other stages. However, these experiments are arguably beyond the scope of this paper, and as long as the authors note the importance of such confirmatory experiments in their Discussion, I don't think that further experimentation is critical for this paper. - Are the data and the methods presented in such a way that they can be reproduced?

7) In general, yes. - Are the experiments adequately replicated and statistical analysis adequate?

8) Yes.

Minor comments:

• Specific experimental issues that are easily addressable.

9) Page 4: Regarding the single cell sequencing approach, the authors should comment on the extent to which mRNAs are efficiently recovered from hypodermal syncytial cells (Hyp), which are multinucleate. Could the data from Hyp be chiefly from nuclear transcripts? If so, how might that affect the interpretation of the data?

10) It is confusing that Table S1 lists male-enriched samples that were apparently sequenced, but only hermaphrodite data were analyzed for the paper. To prevent confusion, the male samples should not be listed.

11) Page 5, bottom: The following analysis requires clarification (at least for this reader): "To test if such oscillatory gene expression is present in ILso glia, we computed the average phase of each cell (Fig. 2B). Specifically, for each cell, we computed a weighted circular average of the peak phases of oscillating genes (derived from the previous bulk RNA-Seq data), using the gene expression levels in that cell as weights."

In reading this part of the main text, this reader struggled to understand how one can compute the phase angle for a given gene in a cell by comparing its level of expression in that cell to measurement of the level of that gene in previous bulk RNA-Seq data. Of course, there is far more to the analysis than that, which the Methods and Materials section on page 18 describes in more detail, where one learns that the level if each gene in each cell is scaled to its maximum expression across all the cells analyzed, and that the previous bulk sequence analysis is used to simply provide a phase angle for the gene's peak expression relative to an arbitrary framework (which corresponds to a larval stage, one assumes). The presentation of this analysis on Page 5 in the main text should be revised to include a full description of what was done so the reader can follow along and understand it without having to read the Methods section. But moreover, the Methods section treatment of this analysis is still not entirely clear; for example, certain variables (W, s, and c) are not defined. The presentation of the mathematics should be clarified so that the reader can understand the analysis without having to look up scTransform-normalization. - Are prior studies referenced appropriately?

12) yes - Are the text and figures clear and accurate? - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

13) Figure S3 Panel A: What does the green line mean? Figure S3 Panel C: The use of the "predictors" tem is confusing because on page 8, the part of the narrative referring to Figure S3, the term used is "descriptors". Is that an meningful switch in terminology?

14) The legend to Figure S3 requires more details to enable the reader understand the Figure. The same critique applies to most of the Supplemental Figure legends, where more details are required to allow the reader to understand each Figure without having to refer back to the main text.

15) Page 19: "The cells were grouped by cell type independent of the stage of collection (L2 or L4), and each cell type was processed individually."

Why were L2s and L4s pooled? How does this affect the analysis and/or the outcomes? Could there be confounding effects from pooling the samples that could affect the analysis or the conclusions?

Referees cross-commenting

There is substantial agreement amongst all three reviewers, regarding the signifcance of the findings and that the conclusions are well enough supported by the data such that no additional experiments are required. We all recommend revisions to clarify or expand the description of the experiments and/or analysis. Many comments are reiterated by more than one Reviewer. I agree with all the other reviewers' critiques.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

The finding of oscillatory and molting-related gene expression patterns in glial cells emphasizes the importance of molting-related ECM/cuticle production by these sensory-accessory cells and will serve as a platform for further studies and further understanding the structural and molecular basis of glial cell support functions, especially in the context of changing roles for sensory neurons during developmental progression.

The methodology and data analysis of C. elegans scRNA-Seq data presented here offers several significant advances, especially since it had been known that thousands of genes cycle in rhythm with the C. elegans molting cycle, yet that was based on previous bulk sequencing, so it was not possible to resolve cell-type specific expression. This paper presents methods for analysis of cycling gene expression in specific cell types.

The manuscript derives hypothetical TF-target regulatory interactions that are proposed do underly cyclic gene expression in specific cell types. This is a significant resource for future work to explore and delineate upstream oscillator mechanisms, and answer questions such as, Is there a central oscillator for all of larval stage rhythmic gene expression? and, How are different genes expressed with different phases of the larval stages? etc. - Place the work in the context of the existing literature (provide references, where appropriate).

The authors cite important previous studeis that used scRNA-Seq to profile gene expression in specific C. elegans cell type in various developmental and physiological settings, and previous studies that used bulk RNAseq to identify genes whose transcripts cycle along with the larval stages. This manuscript reports the first study to examine cyclic gene express in C. elegans on the single-cell level. - State what audience might be interested in and influenced by the reported findings.

Moderately broad audience of biologists interested in biological oscillators; developmental biologists interested in gene regulatory control of developmental cell fate timing and reiterative developmental processes; neurobiologists interested in glial cell function in developmental contexts. - Define your field of expertise with a few keywords to help the authors contextualize your point of view.

C. elegans larval development; temporal control of cell fate progression.

Are there are any parts of the paper that you do not have sufficient expertise to evaluate.

Honestly, some of the mathematical analysis is beyond my ability to judge whether the chosen approach is the best choice for the particular setting.

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Referee #1

Evidence, reproducibility and clarity

This interesting manuscript uses single cell RNAseq of developing C. elegans larvae to identify temporal pulses or oscillations in gene expression within glia and many other epithelial cell types - mostly in genes related to cuticle synthesis or remodeling. It identifies different sets of genes that oscillate within different cell types, and identifies many apparent oscillatory genes that were missed in prior studies because they are expressed in smaller populations of cells (whereas bulk data mainly report on oscillations within the major hypodermis).

A second major contribution of this manuscript is to pioneer analysis methods for detecting oscillatory gene expression in scRNAseq datasets. That said, it's important to state that the methods for estimating phase coherence, GAM, perplexity, etc. make sense to me intuitively but I can't assess the math and other details, which are outside of my expertise.

Most of my comments are minor ones about suggested clarifications to the text or figures. Some may require additional analyses, but none should require additional data collection.

1. The manuscript focuses much of its analysis on one specific glial cell type (ILso), yet the authors tell us almost nothing about this cell type or why they would care about it. It would be helpful to include just a little more background on glial biology and the epithelial-like characteristics of socket glia.
2. Many transcriptomic studies of epithelia (including the Purice et al study of adult glia) use single NUCLEI RNAseq rather than single cells because of the challenges in separating cells connected by tight junctions. In C. elegans there are also various epithelial syncytia to contend with. In text or Methods, the authors should comment on why they think cells were appropriate to look at in this instance, and whether there are certain cell types that were missed or could only be obtained as cell fragments based on that choice.
3. Related to above, the authors do not mention any detection or exclusion of likely doublets. Is there reason to think that doublets were not present in any substantial numbers? I'm not super concerned about this since doublets containing hyp7 fragments should have worked against them in detecting glia-specific oscillations, but I do think the issue should be addressed in the text or Methods.
4. p. 4 "previously unappreciated local differences in cuticle patterning." This statement should be tempered since many stage- or tissue-specific differences in cuticle patterning have been described previously (including in papers from the Heiman lab and others that are cited here). This study uncovers many additional examples but it's not a completely new finding.
5. Table 1 and text: the distinction between pulsatile and oscillatory should be explained more at the outset. These terms sometimes seem to be used interchangeably, but then Table 1 seems to make a distinction, not discussed until the final "limitations" section.
6. Figure 1 and Figure 3A,B. These UMAPs look very unusual, with no discernable individual dots. Is this just a resolution issue? Or, if relevant, please add info to legend and/or Methods explaining what data smoothing was done here to make them look this way and why.
7. Figure 2C and Figure 6B. In the pseudotime plots, it would be natural for readers to assume that 0 is the beginning of the larval stage and 360 is the end, but that is not actually the way the Meeuse 2020 phase angles work - instead the beginning of the larval stage falls around 160. Please make sure this is made clear, especially when referring to "early and late groups" of TF targets. In Fig 6B, Early and Late categories appear reversed because of the way the data are plotted.
8. Figure 3B and Figure 5D-G. The authors group many unidentified clusters into the catchall "skin" category but don't clearly define it in the main text. Table S2 suggests this category includes anterior and posterior skin cells but possibly also other cuticle-lined tubular epithelia that aren't properly referred to as skin (e.g. vulva cells, excretory socket or pore cells). It may also include things like rectum, buccal cavity, excretory duct. Please define your criteria for "skin" more precisely in the main text (any cuticle-lined cell type that is not glia?), and perhaps a more general term such as external epithelia would be more appropriate.
9. Also related to cluster assignments: please specify if "excretory" category includes canal, duct, pore, gland all together, or only a subset of these. Only the duct and pore are cuticle lined and therefore expected to have oscillatory matrix gene expression.
10. Figure 5. This figure feels disjointed and could be broken up into two figures (panels A-C and panels D-G). The first 3 panels seem more related to Figures 3 & 4 - identifying which cell types have strong pulsatile gene expression - whereas the later panels get into the degree of cell type specificity in matrix gene expression.
11. Figure 5D-E. The very low degree of sharing is fascinating but could be an underestimate that depends on the thresholds chosen for calling a gene "pulsatile". It may be helpful to test a range of thresholds to see how much this matters. For those ~2,500 genes that appear pulsatile in just one cell type, are they called expressed but non-pulsatile in other cell types? That would seem odd to me biologically and most likely a threshold artifact.
12. Figure 5F and p.21 Methods, the authors analyze only 140 collagen genes and 38 ZP domain genes retrieved from InterPro, but there are at least 173 cuticle collagen genes and 43 ZP domain genes described in the literature. Therefore, their lists are incomplete and the Methods should say so.

https://pubmed.ncbi.nlm.nih.gov/33543001/ https://pubmed.ncbi.nlm.nih.gov/30409789/ 13. If most oscillatory gene expression is truly a function of the molt cycle, as suggested by the matrix gene families in Figure 5, then one might expect that most of the detected oscillatory genes would no longer be expressed in adults, or at least wouldn't appear "pulsatile" in adults. Is this true? There now are a variety of published adult data sets, including the Purice et al data on glia, that could be examined to address this.

Referees cross-commenting

I agree with the other reviewers' critiques, including the point of Reviewer #2 that orthogonal confirmation methods (such as by imaging) could have been nice but are not necessary. The question of Reviewer #3 about tissue synchrony/asynchrony is a very important one but I am not confident it can be addressed with these types of data.

Significance

As a molting invertebrate, C. elegans must build and shed its protective cuticle at multiple times across its life cycle, and this requires temporal control of many genes involved in matrix structure and processing. Although temporal oscillations were already well documented from bulk RNAseq data, this manuscript extends those prior findings by showing that different sets of genes oscillate within different cell types (including sensory glia), and by identifying many apparent oscillatory genes that were missed in prior studies because they are expressed in smaller populations of cells (whereas bulk data mainly report on oscillations within the major hypodermis). These data about cell-type specific temporal programs and gene sets emphasize the exquisite specificity of apical matrix and will be broadly useful to researchers in the C. elegans community.

A second major contribution of this manuscript is to pioneer analysis methods for detecting oscillatory gene expression in scRNAseq datasets, even where bulk temporal data may not exist. This will be valuable for others doing sRNAseq studies in nematodes but also in other systems where cells may have molt cycle- or circadian-regulated oscillations.

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Reply to the reviewers

__Reviewer #1 (Evidence, reproducibility and clarity (Required)):____

Summary In this study, Phalora et al identified the selective autophagy receptor SQSTM1/p62 as a MR1 interacting protein by proteomics approach using a cell line overexpressing MR1. While SQSTM1/p62 is implicated in autophagy regulation and autophagosome formation, genetic ablation of SQSTM1/p62 resulted in enhanced MAIT cell activation upon challenge with E. coli, but not with a synthetic agonist 5-OP-RU. In contrast, knockout of Atg5 and Atg7, both of which are involved in phagophore expansion engendered increased activation of MAIT cells upon both stimuli. From these data, the authors concluded that some factors in autophagy controlled the MR1 activity, thus the autophagy is a pivotal regulator of cellular antigen presentation.

Major comments: 1. The notion that "This regulation appears to occur at an early step in the trafficking pathway." in the summary appears not to be compatible with the present data. What the authors have shown in the study is possible implication of autophagy components such as SQSTM1/p62, Atg5, and Atg7 that are implicated in autophagosome and phagophore formation. Should the authors highlight an "early step of trafficking", Atg14L, Atg13, and/or Atg101 must be analyzed by genetic knockout in addition to PI3 kinase inhibitors that are supposed to affect an early step in autophagy. Such an approach could confirm whether the regulation of MR1 occurs at an early step of trafficking, or at least, at an early step of autophagy.__

The reviewer may have misinterpreted our conclusion. When we state ‘an early step in the trafficking pathway’ we are referring to MR1 trafficking (from the ER to the PM) and not to early steps in the autophagy pathway. We have modified the text to make this clearer.

__ In Figure 2, while the degree of β2M depletion from B1 appears to be superior to that in B6 (Figure 2A), why the former was more potent in producing IFN-γ relative to the latter upon E. coli and 5-OP-RU (Figure 2D)?__

We cannot conclusively say why MAIT cell activation is reduced to a greater extent in clone B6 compared to clone B1, whereas the protein depletion is not as pronounced. Most likely as these are clonal cells there may be genetic/phenotypic differences apart from depletion of B2M that may impact upon antigen presentation. Importantly both B1 and B6 are significantly decreased in terms of MR1 surface expression and MAIT cell activation compared to the control as would be expected.

__ In Figure 3B, right column, what is Ac-6-FP? The left histograms show MR1 expression level upon DMSO, E. coli, and 5-OP-RU challenge. There is no explanation.__

We thank the reviewer for pointing this out. The bar chart was mislabelled and should read 5-OP-RU (as in the histogram). This has now been corrected in the figure.

__ Also in the same figure, was MR1 geomeans in Control, 5-1, 5-2, 5-3, 7-1, 7-2, and 7-3 upon Ac-6-FP superior to DMSO? If so or not, please explain the rational.__

The difference in MR1 geomeans between DMSO and 5-OP-RU treated cells was significantly different. However as stated in the text the difference between control and Atg depleted cells for each condition was not statistically significant although there is a trend for increasing MR1 expression in KD cells.

__ Figure 3C is highly intentional. If the authors put two left panels together (Control, 5-1, 5-2, and 5-3), is there still statistical difference among them?__

The data for Atg5.3 was displayed separately as the experiments for this cell line were performed at a later timepoint using different donor cells. Therefore, it would be inappropriate to combine and/or compare them with the data for Atg 5.1 and 5.2. For clarity the figure has now been modified and this explanation added to the figure legend.

__ There was no explanation for Figure 4B why the authors used Hela-MR1-HA. Other cell lines were used in the rest of the experiments. It is highly desirable to perform the experiment with THP1-MR1-HA in terms of logical development.__

As the reviewer correctly states, it would be ideal to use Thp.MR1.HA cells for these microscopy experiments as they have been used throughout the rest of the paper. However, Thp1 cells can be difficult to image and HeLa cells which are more amenable to this technique are commonly used instead, generally and for MR1 studies. We have validated the HeLa.MR1.HA cell lines and can show that they upregulate MR1 at the cell surface in response to antigen and can activate MAIT cells. This data is now included as a supplementary figure (Supplementary Figure 11) and the rationale for the use of these cells explained in the main text.

__ In addition, Figure 4B represent only the non-activated status. Given that association of SQSTM1/p62 with MR1 is dependent on E.coli and/or 5-OP-RU (Figure 1A), the same immuno-fluorescent imaging in the presence of the inhibitors upon stimulation with these reagents would also be desirable. It will uncover whether MR1 and SQSTM1/p62 colocalize upon stimulation, and such colocalization is perturbed in the presence of the inhibitors.__

The aim of this microscopy experiment was to demonstrate that perturbations to the autophagy pathway induced by different drug treatments also affected MR1 localisation and/or expression to complement the other experiments in that figure (Figure 4A and 4C). SQSTM1 expression was included as a control as it is known to be regulated by autophagy. Although assessing the interaction between MR1 and SQSTM1 under different autophagy conditions may be of interest we did not find it to be particularly relevant in this case as our focus shifted to the autophagy pathway in general rather than the specific interaction between MR1 and SQSTM1.

__ Whereas the authors addressed the question as to at which stage MR1 is regulated in trafficking in Figure 5, there was no experiments with 5-OP-RU (an agonist for MAIT cells). This casts the doubt whether observed phenotype really represented the true MR1 trafficking, because there is no guarantee that the trafficking pathway for antagonist (Ac-6-FP) is same as that for agonist.__

5-OP-RU and Ac-6-FP are small chemically synthesised molecules and an agonist and antagonist of MR1 antigen presentation respectively There is no evidence to suggest that apart from activation of MAIT cells (5-OP-RU is stimulatory, Ac-6-FP is not) that they would behave any differently in terms of trafficking and interaction with MR1. Indeed, both are used interchangeably in the MR1 field.

__ Given the importance of MR1 overexpression in showing the association between MR1 and SQSTM1/p62, it is worthwhile to consider performing the knockout experiments with Thp1-MR1-HA rather than Thp1. It will further clarify the role(s) of SQSTM1/p62, Atg5, and Atg7 in MR1 trafficking and resultant MAIT cell activation.__

The interaction studies had to be performed with overexpressed MR1 as the endogenous protein is very difficult to detect for these types of experiments. The majority of the functional studies were performed with the endogenous protein which avoids any issues concerned with the use of overexpressed and tagged proteins and addresses concerns that interactions observed with the overexpressed protein are simply artifactual. As the functional assays validate the interaction data, we believe it is not necessary to repeat the depletion experiments in the MR1 overexpressed cell lines.

__ Minor comments: 1.Please explain why the authors failed to detect IL23A in the coimmunoprecipitation. Should MR1-IL23A interaction be specific, what is a biological significance?__

This point is addressed in the discussion. It is sometimes the case that interactions identified by mass spec cannot be recapitulated by co-immunoprecipitation and alternative methods may need to be employed to verify the interaction. Since this work concentrates on the autophagy pathway further experiments involving IL23A were deemed beyond the scope of this manuscript. Of note, IL23A will be strongly induced over very low background levels by E coli, which would amplify the impact of any weak interactions.

__ When Hela-MR1-HA was used, did the authors obtain the same results as Thp1-MR1-HA as shown in Figure 1C-D? This is relevant to the specificity in the interaction between MR1 and SQSTM1/p62 as shown in Figure 4B.__

The interaction between MR1 and SQSTM1 in the presence of E.coli was not confirmed in the HeLa.MR1.HA cells. SQSTM1 is included as a positive control as it is known to be regulated by autophagy. As these experiments were performed in the absence of any antigen, we would not expect to observe an interaction in this instance.

__ While S1, S2, S3, and S4 showed a similar degree of SQSTM1 depletion in Figure 2A, there was difference in the potential of IFN-γ production from MAIT cells among the clones. Only S4 showed decreased potential for IFN-γ upon 5-OP-RU, though E. coli failed to so. Contrary to 5-OP-RU, S1-S3 showed an enhanced potential while S4 failed to do so. Why is that so?__

As the SQSTM1 knockout cells are clonal cells there may be other genetic/phenotypic differences, besides depletion of SQSTM1, that can account for the observed differences in MAIT cell activation. To mitigate for these differences, we tested 4 different clonal cell lines, with 3 out of 4 clones displaying the same phenotype with respect to activation of MAIT cells.

__ Given that there was little correlation between MR1 expression level and the potential of S1-S4 to promote or inhibit the ligand-dependent production of IFN-γ (Figure 2C right panel and Figure 2D), it is difficult to conclude that the factors implicated in autophagy play a pivotal role in MR1-dependent MAIT cell activation.__

Surface MR1 levels on the whole are difficult to detect even in the presence of antigen as MR1 surface expression appears to be very tightly controlled. Although MR1 surface expression levels between the different SQSTM1 clones appeared to be somewhat variable, in the Atg depleted cells they showed a more consistent upregulation compared to the control (although these differences were not statistically significant). In both cases, stimulation with E.coli resulted in increased MAIT activation demonstrating that these autophagy proteins did affect MR1 presentation and that small (perhaps undetectable in some cases) changes in surface expression did impact MR1 function. Therefore, we have concluded that autophagy factors are able to regulate MR1 antigen presentation but to what extent and how remains unclear. We have removed the word ‘pivotal’ from the abstract as we agree with the reviewer that the impact of these interactions has not been conclusively established.

__ There was no consistency in the experimental design for Figure 5. Please explain the rational why the authors have used 7.1 in A and C, but not in B, D and E?__

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For some of the experiments it was not possible to display and thus quantify all the cell lines in one figure eg the western blot data for the EndoH experiments (Figure 5D). Therefore, one representative cell line from Atg5 and Atg7 depleted cells was chosen, as on the whole all the cell lines behaved similarly. This rationale is now included in the main text.

__ The control appeared to behave as 7.1 did. Was there statistical difference between 7.1 and 7.2 in Figure 5C? If so, what is the interpretation.__

As the reviewer correctly notes, in Figure 5C the Atg7.1 cell line had similar kinetics to the control cell line in terms of MR1 surface expression. In other experiments Atg7.1 shows increased MR1 surface expression compared to the control (Figure 3B, although not statistically significant). One major difference between these experiments is the timing, Figure 3B is measured after an overnight incubation while Figure 5C is measured over 6 hours. It may be the case that in this cell line MR1 takes slightly longer to accumulate at the cell surface compared to Atg7.2. As these are heterogenous cell populations, there may be other factors that account for these differences apart from depletion of Atg7. Statistical analysis has now also been included for this data.

__ Time course over 6 h will be required to assess the MR1 expression in Figure 5C.__

It has been demonstrated by others that MR1 is able to reach the cell surface within 4 hours of antigen exposure (McWilliams et al, 2016), therefore a time course over 6 hours to measure MR1 surface expression was deemed sufficient.__

Reviewer #1 (Significance (Required)):

The present study uncovered the possible implication of autophagy factors in MR1 trafficking, in other words, MAIT cell activation. Although the previous study has demonstrated the importance of the protein loading factors (McWilliam et al., PNAS,117 24974-24985 2020), this study adds another pathway for MAIT cell activation. However, the conceptual significance is limited in that depletion of the factors pertinent to autophagy such as Atg5 and Atg7 in Thp1 resulted in rather weak interference in terms of MR1 trafficking and MAIT cell activation. Thus, this study will interest those who work in basic immunology, in particular, in regulation of antigen-presentation molecules and T cells as well as those who are in the field of MAIT cell biology. Although the field of this reviewer covers biochemistry, molecular biology, developmental biology, immunology and regenerative medicine, proteomics approach (in detailed technique) as seen here to identify the associated molecules is somewhat beyond the reviewer's expert.

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

Summary

The authors used a mass spectrometry proteomics approach to screen for proteins which interact with the MHC-I-related molecule MR1. In addition to expected interacting partners, they identified SQSTM1/p62, a selective autophagy mediator, and demonstrated that MAIT cell responses to fixed E. coli were increased with knockout of SQSTM1. The authors further investigated the role of autophagy in regulating MR1 ligand presentation through knockout of two key autophagy proteins, Atg5 and Atg7, or treatment with various autophagy inhibitors. MR1 surface expression and MAIT cell activation were variably increased following interruption of autophagy in the context of fixed E. coli or synthetic ligand treatment of human monocytes and B cell lines. The authors concluded that preformed pools of MR1 are regulated by autophagy.

Major comments

Overall, this is an interesting study that is the first to identify autophagy as a potential regulatory mechanism for MR1. There are a number of conceptual questions relevant to the model system. The main concerns regard a number of the conclusions made, given the analysis of the data as presented. These concerns are described in more detail below.

Conceptual concerns:

1. The investigators rightly note the challenge in studying MR1 protein due to low endogenous expression. However, the use of over-expressed MR1 protein begs some questions with regard to the identification of ER degradation and autophagy proteins (which as they note are also involved in the degradation of damaged and defective cellular components). Although they have previously shown that MR1-HA tagged protein goes to the cell surface and presents antigen, it is impossible to know what proportion of the over-expressed molecules are functional, and it is plausible that a proportion of these molecules that end up in ER degradation or autophagy pathways identified, but would still IP with the HA tag. In the data shown, it is not entirely clear that the impacts of the molecules are actually impacting MR1 protein absent overexpression. Example: In Figure 2, there is very little impact of the complete KO of SQSTM1 on MR1 protein expression in WT THP1 cells, despite this protein only interacting with MR1 in E.coli infected cells. In contrast, in the 5-OP-RU incubated cells, there is a difference in MR1 expression in the SQSTM1 mutant clones, but no impact to MAIT cell activation. The authors note these issues and discuss the possibility that the other functions of SQSTM1 are coming in to play and further look at Atg5 and Atg7, however the absence of these proteins also have no significant impact on the expression of MR1 protein. Can the authors comment on this? The authors state that the increase in MAIT cell responses to fixed E. coli-treated polyclonal populations of SQSTM1 KO cells (same cells as SF2D) was blocked by the use of an anti-MR1 antibody, but do not show this data. Why not done with clonal populations? It is unclear why this data was not shown as it would help to support that the impact of inhibited autophagy is really on the functional MR1 protein pool, rather than a pool of non-functional but still HA tagged MR1 that has been shunted to degradation or autophagy pathways.__

The reviewer rightly acknowledges the challenges associated with detecting endogenous MR1 protein levels which can be difficult to measure even after antigen exposure. For this reason, many researchers use a tagged protein in overexpressing cell lines to study MR1 as we (and others) have done for the proteomics analysis and validation studies. The use of tagged overexpressed proteins can be problematic because they may not recapitulate endogenous protein structure, localisation and/or function. Although we have previously demonstrated that HA tagged MR1 behaves similarly to its endogenous counterpart in terms of trafficking to the cell surface and presentation to MAIT cells (Ussher et al, 2016), there is still a possibility that there is a population of non-functional protein that is targeted for degradation. As we understand, it is the reviewer’s concern that it is this protein pool that is immunoprecipitating with autophagy components.

Firstly, although the interaction studies were necessarily performed using tagged overexpressed protein, the majority of the functional studies (ie measuring surface MR1 levels and MAIT cell activation in SQSTM1 and Atg depleted cells, Figures 2 and 3) were performed in wildtype Thp1 cells, expressing endogenous levels of MR1. As explained in response to reviewer 1, MR1 surface levels as displayed in Figures 2C and 3B, are very tightly controlled and can be difficult to detect even after antigen exposure as demonstrated in the accompanying histograms. Therefore, subtle differences in MR1 surface levels are to be expected especially when measuring an increase rather than a decrease in expression. Although for SQSTM1 depletion there was some variability in MR1 surface levels, for Atg depletion there was a clear trend towards increased expression, although these differences were not statistically significant. In both cases (depletion of SQSTM1 and Atg) there was a definite effect on MR1 presentation as MAIT cell activation was increased in nearly all cases. It is well established in the literature that MAIT activation, in the 5 hour timecourse of our experiments, is wholly MR1 dependent. Therefore, these subtle, and perhaps sometimes undetectable, differences on endogenous MR1 surface expression do have an effect on MR1 function and we believe this validates the data from the interaction studies using overexpressed protein.

In addition, experiments performed with the MR1 blocking antibody would not necessarily address the reviewers concerns as again these were done on Thp1 cells expressing endogenous levels of MR1 and not the overexpressing cell lines. However, for completeness this data has now been included as a supplementary figure.

Secondly one of the top hits from the proteomics analysis was B2M, a protein known to associate with MR1 and to be functionally important. Other proteins identified by our screen include components of the peptide loading complex which have also been reported to be important for MR1 trafficking and antigen presentation. It should also be noted that SQSTM1 was identified in a similar proteomics screen performed by a different lab (McWilliams et al, 2020). Therefore, we believe that these findings also validate use of the HA tagged MR1 construct to generate true protein interactions.

__ The conclusion that "regulation of MR1 by autophagy is not dependent on new protein synthesis and is most likely occurring on pre-existing pools of MR1" is not strongly supported by the data. If MR1 is processed normally through the golgi in Atg5 and 7 deficient cells (Figure 5D), how can the conclusion be made that the pre-existing pools of MR1 are in the ER? There is a non-significant decrease in MR1 surface expression from CHX treatment in the context of Ac-6-FP stimulation in Atg KO cells. This data is not clear enough to support a firm conclusion in either direction. Have the authors performed this experiment using 5-OP-RU or fixed E. coli as ligand sources? Is there a similar trend seen using the Atg KO C1R cells? Further supporting experiments may be necessary to conclude whether or not this trend is biologically relevant.__

We thank the reviewer for their comment. The statement that pre-existing pools of MR1 are in the ER is based on reports from the literature where it has been shown that unbound ligand receptive MR1 remains in the ER until it comes into contact with antigen. Since we were able to show that MR1 trafficked normally through the Golgi in Atg depleted cells, the effects of autophagy on MR1 expression and function must occur prior to Golgi processing. This would indicate the ER population of MR1 as the likely targets of regulation by autophagy especially considering the function of SQSTM1 which binds to proteins in the ER.

The experiments with CHX treatment were used to establish whether it was new or pre existing protein that was targeted by autophagy. Since CHX had no effect on MR1 surface expression this would indicate that new protein synthesis is not required for MR1 trafficking in Atg depleted cells.

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Analysis of Western Blot data:

1. There are many places throughout the manuscript where statements are made with regard to increases and decreases in the protein expression level with treatment, or comparisons between control and knockout samples. Although the legends generally indicate these experiments were based on at least 3 replicates (except some cases, where noted), there is no quantification of any western blotting data. There is no information in the legends or methods as to how much sample was loaded. Specific examples:

a. Figure 1/Supp Figure 1: Figure 1C and 1D: There are several differences in the inputs between the 2 blots, including differences in the no antigen samples (which should be the same) or presence of multiple bands in one blot for a given marker but not the other. Fig 1C: the band for Calreticulin in the immunoprecipitated E. coli-treated Thp1.MR1.HA samples (right lane) is very weak. Fig. 1D: the bands are weak and there is no clear difference for Calnexin in the immunoprecipitated 5-OP-RU treated Thp1.MR1.HA samples (right lane) compared to no ligand despite the conclusion that Calnexin weakly associates with MR1 in the context of 5-OP-RU ligand. Are some of these weak associations visible due to different inputs? Why are the input blots for anti-HA so different between the no antigen controls in the E coli vs 5-OP-RU blots? Supp Figure 1B: the +5-OP-RU pulldown of MR1.HA appears as to be more (like with E.coli), but no quantification. Why does so little B2M IP with 5-OP-RU MR1? Supp Figure 1D (and others): statements are made about increases and decreases without quantification. All: Presumably HSP90 is used as a loading control for the input, but this is not discussed nor is there quantification.__

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We thank the reviewer for this comment. As western blotting is a multi-step process often over more than one day, there are numerous points at which variation can occur between blots no matter how carefully the conditions are controlled to minimise this. It is for this reason that it is generally not good practice to compare samples that have been run on different gels. Therefore, we do not believe that comparisons between blots in Figures 1C and 1D, relating to differences in input proteins for example, are appropriate nor informative. If we take the top anti-HA blot for Figure 1C there is a big increase in protein expression in the Ip of E.coli treated cells (final lane) which is not as pronounced with 5-OP-RU treatment (Figure 1D, top blot, final lane). This sample will dictate the exposure time of the blot (so as to prevent saturation of this sample) which then affects detectable expression of less well expressing samples on the same blot (such as the input samples in Figure 1C). Therefore there may appear to be less input protein in Figure 1C than Figure 1D but there is also more protein in the E.coli treated pull down than in the 5-OP-RU treated one, which also needs to be taken into account. This is one example of why it is difficult to compare samples across blots. To accurately and correctly compare these input samples they would need to be run on the same gel.

The only useful comparison that can be drawn is between samples from the same blot, so comparing input protein in the presence and absence of E.coli for instance. To take the reviewer’s example, for the anti-calreticulin blot in Figure 1C, there is a weak interaction of calreticulin with MR1 in the presence of E.coli. If we compare the input lanes on this blot (effectively the loading control), there actually appears to be slightly more protein in the E.coli negative sample that the positive one. This would argue against the reviewers claim that this weak interaction is actually due to differences in the input and it is instead more likely to simply be a weak interaction. It is important to point out that this interaction, and others involving components of the peptide loading complex, have also been validated by other groups.

With regards to Calnexin association with MR1 in the presence of 5-OP-RU, we did not mean to imply that this association was only in the presence of 5-OP-RU as it is evident from the data that Calnexin weakly associates even in the absence of antigen. The text has now been changed to make this clearer.

The anti-HSP90 blot has been included to show that a random protein, not identified by our proteomics screen, does not spuriously associate with MR1, and not as a loading control for the input samples per se. This explanation has now been included in the text.

Finally with regard to quantification of the co-immunoprecipitation blots, while quantification of western blots in some cases can be informative (eg relative expression of a protein compared to a control), it is at best only a semi-quantitative technique and not generally applied to co-immunoprecipitation data. As we are looking for a binary result (presence/absence of a particular protein) rather than a relative value, we do not see how quantification of this data will make it any more informative. We have included more detail of the sample loading in the methods section as requested by the reviewer and have added quantification of other blots where appropriate. __

b. Supp Figure 5: The authors conclude there are no difference in protein interactions with MR1 in Atg5 or 7 deficient cells. By eye, there appear to in fact be differences, but there is no quantification to support the conclusions either iway. These data are subsequently used to make interpretive statements about the data in Figure 5. There is no indication of the number of times this experiment was performed.__

In supplementary figure 5, we aimed to determine whether depletion of Atg 5 or 7 negatively affected the MR1 proteome ie whether interactions that were previously observed were disrupted and whether this contributed to the effects on MR1 antigen presentation observed in these cell lines. The interactions between MR1 and the tested proteins remained intact in Atg depleted cells. However, as Atg depletion increased MR1 protein expression some of these interactions are more pronounced in the depleted cell lines compared to the control cell line. Thus, the reviewer is correct in stating that there are differences in the protein interactions between the cell lines but in all cases the protein interactions remain intact which was the focus of our analysis. We have modified the text to make this clearer. The figure legend now also includes the number of replicates for this experiment.

__ Figure 4A: No quantification to support conclusions. Unclear why both blocking and inducing autophagy would both increase the amount of MR1 in cells.__

Quantification of this western blot data has now been included in the figure. Blocking autophagy (3MA and Wort) has a much greater effect on total MR1 protein levels, while inducing autophagy (EBSS) has minimal effects compared to the control. As autophagy is a highly dynamic process with western blotting providing just a snapshot of this process, inhibiting and inducing autophagy can both lead to the same observed phenotype of increased autophagosomes, due to blocking fusion with lysosomes and increased autophagosome formation respectively.

__

Analysis of Fluorescence microscopy data (Figure 4B):

1. There are several concerns with the conclusions drawn from the fluorescence microscopy images (Figure 4B). How many images/fields were taken and cells analyzed per condition? How were individual fields chosen for imaging to be unbiased? Overall, the conclusions are observational and require quantification. For example, the authors indicate "an increase in MR1 cytoplasmic signal intensity following treatment...", but there is not data analysis to support this statement. This could be quantified by analyzing average MR1-HA fluorescence intensity across the cell volume compared to the bright fluorescence intensity of the non-cytoplasmic MR1-HA regions. Similarly, the number and intensity of the SQSTM1 foci should be quantified. Quantification is required to make the stated conclusions.__

---

We thank the reviewer for their helpful suggestions regarding the microscopy experiments. Quantification of the data has now been added, including MR1 fluorescent intensity and the number of SQSTM1 foci, which supports the data from Figure 4A. The methods and figure legend have been updated to include more details of the analysis pipeline.

__ Other statistical concerns:

1. Some of the figure legends do not clearly state the number of independent experiments performed (2D, 3C-D, 5A, SF2, SF3, SF5). If these experiments were only performed once, additional repeats and appropriate statistical analysis are necessary to validate any conclusions drawn from these results.__

The number of replicates for each experiment are now included in the figure legends. __

1. Was statistical analysis performed on the MR1 mRNA expression in Figure 5A, and how many independent experiments are shown? There appears to be a decrease in MR1 expression in the Stg7.1 KO cells, which might impact the overall MR1 expression. Also, statistical analysis seems to be missing from 5B and 5C.__

This figure has now been altered to reflect the number of replicates (2 biological replicates each consisting of 3 technical replicates) and statistical analysis has also been included. Statistical analysis for Figures 5B and 5C has also now been included. __

1. In figure 5E, were there statistical comparisons between the Atg KO and control cells in the Ac-6-FP-treated non-CHX condition? It is unclear whether the statement "As previously observed, there was an increase in surface MR1 levels in Atg-depleted cells compared to the control in the presence of Ac-6-FP" is referring to the non-significant results in 3B or to this data presented in 5E. This statement should be revised to reflect the statistical significance of these data.__

We thank the reviewer for this point. This figure has been amended to include a timecourse of CHX treatment in control and Atg depleted cell lines and statistical analysis has also been included. The statement has been clarified to highlight the point that CHX treatment does not affect the level of MR1 upregulation in control and knockdown cell lines.

__

Throughout the figures, several bar plots are missing the individual data points of experimental or technical replicates.__

All bar plots display either the individual data points where donor cells were used or the average of 3 or more independent experiments with error bars denoting the standard deviation for experiments using cell lines.__

1. The data in Figures 3C-D could be presented and analyzed as paired data (comparing the response from MAIT cells of each PBMC donor to the Ctrl cells vs the Atg KO clones) to better represent the impact of the KO.__

We thank the reviewer for this suggestion. We believe that analysis via ANOVA is more appropriate in this instance due to the number of comparisons made with the control cells.__

Other minor concerns:

1. The conclusion "Overall, in the absence of SQSTM1, cellular changes induced by E. coli result in increased antigen presentation, which is not replicated with 5-OP-RU where MAIT activation may be adversely affected, implying that regulation of MR1 function by SQSTM1 may be dependent on the nature of the antigen" (page 6) is confusing and may need re-wording.__

We are sorry for the confusion and have reworded this sentence to make it clearer. __

1. The x-axis in the bar plots of Fig 3B labels the right group as "Ac-6-FP" in contrast to the histogram label and figure legend, which indicate the cells were treated with 5-OP-RU.__

We thank the reviewer for pointing this out, the bar plot was indeed mislabelled and has now been corrected. __

1. The presentation of data in Figure 5B is confusing. Perhaps the DMSO and Ac-6-FP conditions are mis-labeled? For the DMSO-treated samples, it appears that the data presented are percent surface MR1 GeoMean compared to the 0hr timepoint per cell lines. However, treating cells with Ac-6-FP should result in an increased surface MR1 expression (as seen in the non-CHX samples of Fig 5E, for example). If the data presented are percent of the 0hr DMSO control, wouldn't the % MR1 expression be higher for the Ac-6-FP samples than the DMSO samples? Alternately, it might be clearer to separate these two conditions onto separate plots, with % MR1 calculated relative to the 0 hr control of DMSO or Ac-6-FP treatment, respectively.__

We thank the reviewer for pointing this out, the graph was indeed mislabelled and has now been corrected. The DMSO and Ac-6-FP treated samples are normalised to their own 0-hour timepoint (set at 100%) in order to directly compare the rate of decline of MR1 surface expression between the two conditions. This is now more clearly explained in the figure legend.

__ Unclear in Figures 3 and 5 (and supplements) why all or only some of the Atg5 and 7 clones are used from experiment to experiment.__

Please see our response to reviewer 1 on this point.__

1. The discussion mentions "we found no evidence of an interaction between MR1 and AAKI" on page 9. What data supports this statement?__

We found no evidence of an interaction between MR1 and AAK1 from our proteomics screen, this is now explained in the text.

__ The discussion indicates that "This increase in SQSTM1 protein levels still resulted in increased MR1 surface levels and activation of MAIT cells, the same phenotype observed in SQSTM1-depleted cells" as it relates to the presence of E.coli. This statement is not fully supported by the data as SQSTM1 depletion did not lead to an increase in surface MR1 in E.coli treated cells.__

We thank the reviewer for pointing this out, this sentence has now been corrected. __

1. In the Proteomics/Mass Spec methods section on page 13, the citations to MaxQuant and Andromeda may need to be fixed.__

We thank the reviewer for pointing this out, this has now been corrected. __

1. There is no materials/methods section in the supplement. While most of this is covered by the main manuscript M/M section, there is no information on the IL12 and IL18 cytokine treatment, or treating with il12/il18 or isotype blocking antibody in SF1.__

A methods section for the supplementary data has now been included. __

1. Throughout the manuscript, several full stops are missing following in-text citations (ex: page 1, line 6 "...and Granzyme B 2-4 The microbial...").__

We thank the reviewer for pointing this out, this has now been corrected.__

1. The figure 1 legend should read "LC-MS/MS" rather than "LC-LC/MS"__

---

We thank the reviewer for pointing this out, this has now been corrected.__

1. Several of the citations need updating. They are listed as "Preprint available at ..." but for several of these references, the DOI links to the fully peer-reviewed publications, not a preprint.__

We thank the reviewer for pointing this out, this has now been corrected.

__

Reviewer #2 (Significance (Required)):

Significance

Overall, this work expands the field knowledge of MR1 regulation and antigen presentation. The authors are the first to describe the putative role of key autophagy mediators like SQSTM1 and Atg5/7 in regulating MR1/MAIT cell activation. This report builds upon previous works exploring MR1 trafficking (Huang et al. JEM 2008, McWilliam et al. Nat Imm 2016, Harriff et al. PLoS Path 2016, Karamooz et al. Sci Rep 2019, McWilliam PNAS 2020, Huber et al. Sci Rep 2020) and MR1 protein stability (Abós et al. Biochem Biophys Res Commun 2011, Ussher et al. Eur J Immunol 2016, McWilliam et al. PNAS 2020, Kulicke et al. JBC 2022).

This report would be of interest to researchers in the field of MR1 trafficking and antigen presentation, particularly in the context of increasing interest in targeting MR1 therapeutically (e.g. in cancer immunobiology or autoimmunity). From these results, future work could include characterization of the specific autophagy mechanisms which target MR1 for degradation, the role of SQSTM1 in modulating MR1 function via direct binding through autophagy or additional mechanisms, the variable mechanisms of MR1 trafficking and antigen presentation in the context of internal vs external ligand sources, and exploring if bacterial modulation of autophagy might impact MR1 antigen presentation.

Expertise: MR1 trafficking and antigen presentation, MAIT cell activation, cell and molecular techiques, statistical analyses. Difficult to assess: the relevance of these marker in the autophagy field and evaluating the technical methods for LC-MS/MS.

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

In the current report, Phalora et al., have identified a number of proteins that bind to human MR1. Some of them, including those associated with the peptide-loading complex, such as tapasin, have been identified by others as well. However, these authors found that molecules associated with autophagy-specifically, SQST1/p62-were negative regulators of MR1 surface expression. In other words, knocking out the gene encoding this protein enhanced MR1 expression in THP-1 cells pulsed with E. coli and consequent MAIT cell activation. Moreover, CRISPR/Cas9-mediated deletion of the autophagy proteins, Atg5 and Atg7, resulted in an even greater enhancement of MR1 surface expression. Chemicals that block autophagy had similar effects in both THP-1 and primary PBMC monocytes. Thus, for the first time, it has been demonstrated that, like in classical HLA class I molecules, autophagy plays a role in the surface expression of the MR1 antigen presenting molecule. Overall, the study is very interesting and technically well-done. I do have a few questions, concerns and criticisms that are indicated in the sections below.

Major Comments: 1. It was stated in the text that they used an anti-MR1 mAb to demonstrate the effects on MAIT cell activation were indeed MR1-dependent, yet these data were not shown. Those experiments should be included in the supplemental data section.__

We thank the reviewer for this suggestion, this data has now been included as a supplementary figure.

__ The Discussion lacks a "big picture" assessment/speculation about how these observations fit within a particular disease or set of diseases__

---

The discussion has now been revised to include assessment of how these findings fit into the wider scope of MR1 restricted T cells in health and disease.

__ THP-1 and C1R are essentially cancer cells and it has been shown that MR1T cells likely recognize a tumor antigen presented by MR1. Rather than using purified MAIT cells for this study, the authors used purified CD8+ T cells. MAIT cells represent a portion of them. How many of the non-MAIT cells were activated by THP-1 and/or C1R cells? One could compare MAIT vs. MR1T cell activation depending on the APC type.__

---

We thank the reviewer for this suggestion. We re-analysed some of the data to focus on the non-MAIT population but we were unable to identify a population of non-MAIT cells stimulated by co-incubation with Thp1 or CR1 cells. In general, MR1T cells are quite rare and difficult to isolate solely from the non-MAIT cell population.

__ As autophagy proteins have been shown to be important for MHC class I and, thanks to this work, MR1, it would have been helpful to discuss other antigen presenting molecules (e.g., CD1d) and what this could mean in immune responses overall. How does this help the host?__

We have now included a section in the discussion to address the wider significance of these findings for immune responses via antigen presentation and the implications for other antigen presenting molecules.

__ Minor Comment: 1. Some parts of some figures (e.g., Fig. 1B) have text so small that it is extremely difficult to read. This would be problematic in a journal article.__

We thank the reviewer for pointing this out, the text in the figure has now been adjusted to make it easier to read.

__

Reviewer #3 (Significance (Required)):

This study shows, for the first time, that autophagy processes impact cell surface expression of MR1 and this depends upon the antigen. Because this phenomenon has been demonstrated previously for classical MHC class I molecules (ref. 28) and the lipid-presenting antigen presenting molecule CD1d (Autophagy 13:1025-1036, 2017), the novelty of their findings is somewhat diminished.

An audience who would be interested in this work would include investigators who study antigen presentation to both classical and innate T cells.

Keywords: antigen presentation; MAIT cells; MR1; autophagy; innate immunity__

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #3

Evidence, reproducibility and clarity

In the current report, Phalora et al., have identified a number of proteins that bind to human MR1. Some of them, including those associated with the peptide-loading complex, such as tapasin, have been identified by others as well. However, these authors found that molecules associated with autophagy-specifically, SQST1/p62-were negative regulators of MR1 surface expression. In other words, knocking out the gene encoding this protein enhanced MR1 expression in THP-1 cells pulsed with E. coli and consequent MAIT cell activation. Moreover, CRISPR/Cas9-mediated deletion of the autophagy proteins, Atg5 and Atg7, resulted in an even greater enhancement of MR1 surface expression. Chemicals that block autophagy had similar effects in both THP-1 and primary PBMC monocytes. Thus, for the first time, it has been demonstrated that, like in classical HLA class I molecules, autophagy plays a role in the surface expression of the MR1 antigen presenting molecule. Overall, the study is very interesting and technically well-done. I do have a few questions, concerns and criticisms that are indicated in the sections below.

Major Comments:

1. It was stated in the text that they used an anti-MR1 mAb to demonstrate the effects on MAIT cell activation were indeed MR1-dependent, yet these data were not shown. Those experiments should be included in the supplemental data section.
2. The Discussion lacks a "big picture" assessment/speculation about how these observations fit within a particular disease or set of diseases
3. THP-1 and C1R are essentially cancer cells and it has been shown that MR1T cells likely recognize a tumor antigen presented by MR1. Rather than using purified MAIT cells for this study, the authors used purified CD8+ T cells. MAIT cells represent a portion of them. How many of the non-MAIT cells were activated by THP-1 and/or C1R cells? One could compare MAIT vs. MR1T cell activation depending on the APC type.
4. As autophagy proteins have been shown to be important for MHC class I and, thanks to this work, MR1, it would have been helpful to discuss other antigen presenting molecules (e.g., CD1d) and what this could mean in immune responses overall. How does this help the host?

Minor Comment:

1. Some parts of some figures (e.g., Fig. 1B) have text so small that it is extremely difficult to read. This would be problematic in a journal article.

Significance

This study shows, for the first time, that autophagy processes impact cell surface expression of MR1 and this depends upon the antigen. Because this phenomenon has been demonstrated previously for classical MHC class I molecules (ref. 28) and the lipid-presenting antigen presenting molecule CD1d (Autophagy 13:1025-1036, 2017), the novelty of their findings is somewhat diminished.

An audience who would be interested in this work would include investigators who study antigen presentation to both classical and innate T cells.

Keywords: antigen presentation; MAIT cells; MR1; autophagy; innate immunity

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary

The authors used a mass spectrometry proteomics approach to screen for proteins which interact with the MHC-I-related molecule MR1. In addition to expected interacting partners, they identified SQSTM1/p62, a selective autophagy mediator, and demonstrated that MAIT cell responses to fixed E. coli were increased with knockout of SQSTM1. The authors further investigated the role of autophagy in regulating MR1 ligand presentation through knockout of two key autophagy proteins, Atg5 and Atg7, or treatment with various autophagy inhibitors. MR1 surface expression and MAIT cell activation were variably increased following interruption of autophagy in the context of fixed E. coli or synthetic ligand treatment of human monocytes and B cell lines. The authors concluded that preformed pools of MR1 are regulated by autophagy.

Major comments

Overall, this is an interesting study that is the first to identify autophagy as a potential regulatory mechanism for MR1. There are a number of conceptual questions relevant to the model system. The main concerns regard a number of the conclusions made, given the analysis of the data as presented. These concerns are described in more detail below.

Conceptual concerns:

1. The investigators rightly note the challenge in studying MR1 protein due to low endogenous expression. However, the use of over-expressed MR1 protein begs some questions with regard to the identification of ER degradation and autophagy proteins (which as they note are also involved in the degradation of damaged and defective cellular components). Although they have previously shown that MR1-HA tagged protein goes to the cell surface and presents antigen, it is impossible to know what proportion of the over-expressed molecules are functional, and it is plausible that a proportion of these molecules that end up in ER degradation or autophagy pathways identified, but would still IP with the HA tag. In the data shown, it is not entirely clear that the impacts of the molecules are actually impacting MR1 protein absent overexpression. Example: In Figure 2, there is very little impact of the complete KO of SQSTM1 on MR1 protein expression in WT THP1 cells, despite this protein only interacting with MR1 in E.coli infected cells. In contrast, in the 5-OP-RU incubated cells, there is a difference in MR1 expression in the SQSTM1 mutant clones, but no impact to MAIT cell activation. The authors note these issues and discuss the possibility that the other functions of SQSTM1 are coming in to play and further look at Atg5 and Atg7, however the absence of these proteins also have no significant impact on the expression of MR1 protein. Can the authors comment on this? The authors state that the increase in MAIT cell responses to fixed E. coli-treated polyclonal populations of SQSTM1 KO cells (same cells as SF2D) was blocked by the use of an anti-MR1 antibody, but do not show this data. Why not done with clonal populations? It is unclear why this data was not shown as it would help to support that the impact of inhibited autophagy is really on the functional MR1 protein pool, rather than a pool of non-functional but still HA tagged MR1 that has been shunted to degradation or autophagy pathways.
2. The conclusion that "regulation of MR1 by autophagy is not dependent on new protein synthesis and is most likely occurring on pre-existing pools of MR1" is not strongly supported by the data. If MR1 is processed normally through the golgi in Atg5 and 7 deficient cells (Figure 5D), how can the conclusion be made that the pre-existing pools of MR1 are in the ER? There is a non-significant decrease in MR1 surface expression from CHX treatment in the context of Ac-6-FP stimulation in Atg KO cells. This data is not clear enough to support a firm conclusion in either direction. Have the authors performed this experiment using 5-OP-RU or fixed E. coli as ligand sources? Is there a similar trend seen using the Atg KO C1R cells? Further supporting experiments may be necessary to conclude whether or not this trend is biologically relevant.

Analysis of Western Blot data:

1. There are many places throughout the manuscript where statements are made with regard to increases and decreases in the protein expression level with treatment, or comparisons between control and knockout samples. Although the legends generally indicate these experiments were based on at least 3 replicates (except some cases, where noted), there is no quantification of any western blotting data. There is no information in the legends or methods as to how much sample was loaded. Specific examples:
   • a. Figure 1/Supp Figure 1: Figure 1C and 1D: There are several differences in the inputs between the 2 blots, including differences in the no antigen samples (which should be the same) or presence of multiple bands in one blot for a given marker but not the other. Fig 1C: the band for Calreticulin in the immunoprecipitated E. coli-treated Thp1.MR1.HA samples (right lane) is very weak. Fig. 1D: the bands are weak and there is no clear difference for Calnexin in the immunoprecipitated 5-OP-RU treated Thp1.MR1.HA samples (right lane) compared to no ligand despite the conclusion that Calnexin weakly associates with MR1 in the context of 5-OP-RU ligand. Are some of these weak associations visible due to different inputs? Why are the input blots for anti-HA so different between the no antigen controls in the E coli vs 5-OP-RU blots? Supp Figure 1B: the +5-OP-RU pulldown of MR1.HA appears as to be more (like with E.coli), but no quantification. Why does so little B2M IP with 5-OP-RU MR1? Supp Figure 1D (and others): statements are made about increases and decreases without quantification. All: Presumably HSP90 is used as a loading control for the input, but this is not discussed nor is there quantification.
   • b. Supp Figure 5: The authors conclude there are no difference in protein interactions with MR1 in Atg5 or 7 deficient cells. By eye, there appear to in fact be differences, but there is no quantification to support the conclusions either iway. These data are subsequently used to make interpretive statements about the data in Figure 5. There is no indication of the number of times this experiment was performed.
   • c. Figure 4A: No quantification to support conclusions. Unclear why both blocking and inducing autophagy would both increase the amount of MR1 in cells.

Analysis of Fluorescence microscopy data (Figure 4B):

1. There are several concerns with the conclusions drawn from the fluorescence microscopy images (Figure 4B). How many images/fields were taken and cells analyzed per condition? How were individual fields chosen for imaging to be unbiased? Overall, the conclusions are observational and require quantification. For example, the authors indicate "an increase in MR1 cytoplasmic signal intensity following treatment...", but there is not data analysis to support this statement. This could be quantified by analyzing average MR1-HA fluorescence intensity across the cell volume compared to the bright fluorescence intensity of the non-cytoplasmic MR1-HA regions. Similarly, the number and intensity of the SQSTM1 foci should be quantified. Quantification is required to make the stated conclusions.

Other statistical concerns:

1. Some of the figure legends do not clearly state the number of independent experiments performed (2D, 3C-D, 5A, SF2, SF3, SF5). If these experiments were only performed once, additional repeats and appropriate statistical analysis are necessary to validate any conclusions drawn from these results.
2. Was statistical analysis performed on the MR1 mRNA expression in Figure 5A, and how many independent experiments are shown? There appears to be a decrease in MR1 expression in the Stg7.1 KO cells, which might impact the overall MR1 expression. Also, statistical analysis seems to be missing from 5B and 5C.
3. In figure 5E, were there statistical comparisons between the Atg KO and control cells in the Ac-6-FP-treated non-CHX condition? It is unclear whether the statement "As previously observed, there was an increase in surface MR1 levels in Atg-depleted cells compared to the control in the presence of Ac-6-FP" is referring to the non-significant results in 3B or to this data presented in 5E. This statement should be revised to reflect the statistical significance of these data.
4. Throughout the figures, several bar plots are missing the individual data points of experimental or technical replicates.
5. The data in Figures 3C-D could be presented and analyzed as paired data (comparing the response from MAIT cells of each PBMC donor to the Ctrl cells vs the Atg KO clones) to better represent the impact of the KO.

Other minor concerns:

1. The conclusion "Overall, in the absence of SQSTM1, cellular changes induced by E. coli result in increased antigen presentation, which is not replicated with 5-OP-RU where MAIT activation may be adversely affected, implying that regulation of MR1 function by SQSTM1 may be dependent on the nature of the antigen" (page 6) is confusing and may need re-wording.
2. The x-axis in the bar plots of Fig 3B labels the right group as "Ac-6-FP" in contrast to the histogram label and figure legend, which indicate the cells were treated with 5-OP-RU.
3. The presentation of data in Figure 5B is confusing. Perhaps the DMSO and Ac-6-FP conditions are mis-labeled? For the DMSO-treated samples, it appears that the data presented are percent surface MR1 GeoMean compared to the 0hr timepoint per cell lines. However, treating cells with Ac-6-FP should result in an increased surface MR1 expression (as seen in the non-CHX samples of Fig 5E, for example). If the data presented are percent of the 0hr DMSO control, wouldn't the % MR1 expression be higher for the Ac-6-FP samples than the DMSO samples? Alternately, it might be clearer to separate these two conditions onto separate plots, with % MR1 calculated relative to the 0 hr control of DMSO or Ac-6-FP treatment, respectively.
4. Unclear in Figures 3 and 5 (and supplements) why all or only some of the Atg5 and 7 clones are used from experiment to experiment.
5. The discussion mentions "we found no evidence of an interaction between MR1 and AAKI" on page 9. What data supports this statement?
6. The discussion indicates that "This increase in SQSTM1 protein levels still resulted in increased MR1 surface levels and activation of MAIT cells, the same phenotype observed in SQSTM1-depleted cells" as it relates to the presence of E.coli. This statement is not fully supported by the data as SQSTM1 depletion did not lead to an increase in surface MR1 in E.coli treated cells.
7. In the Proteomics/Mass Spec methods section on page 13, the citations to MaxQuant and Andromeda may need to be fixed.
8. There is no materials/methods section in the supplement. While most of this is covered by the main manuscript M/M section, there is no information on the IL12 and IL18 cytokine treatment, or treating with il12/il18 or isotype blocking antibody in SF1.
9. Throughout the manuscript, several full stops are missing following in-text citations (ex: page 1, line 6 "...and Granzyme B 2-4 The microbial...").
10. The figure 1 legend should read "LC-MS/MS" rather than "LC-LC/MS"
11. Several of the citations need updating. They are listed as "Preprint available at ..." but for several of these references, the DOI links to the fully peer-reviewed publications, not a preprint.

Significance

Overall, this work expands the field knowledge of MR1 regulation and antigen presentation. The authors are the first to describe the putative role of key autophagy mediators like SQSTM1 and Atg5/7 in regulating MR1/MAIT cell activation. This report builds upon previous works exploring MR1 trafficking (Huang et al. JEM 2008, McWilliam et al. Nat Imm 2016, Harriff et al. PLoS Path 2016, Karamooz et al. Sci Rep 2019, McWilliam PNAS 2020, Huber et al. Sci Rep 2020) and MR1 protein stability (Abós et al. Biochem Biophys Res Commun 2011, Ussher et al. Eur J Immunol 2016, McWilliam et al. PNAS 2020, Kulicke et al. JBC 2022).

This report would be of interest to researchers in the field of MR1 trafficking and antigen presentation, particularly in the context of increasing interest in targeting MR1 therapeutically (e.g. in cancer immunobiology or autoimmunity). From these results, future work could include characterization of the specific autophagy mechanisms which target MR1 for degradation, the role of SQSTM1 in modulating MR1 function via direct binding through autophagy or additional mechanisms, the variable mechanisms of MR1 trafficking and antigen presentation in the context of internal vs external ligand sources, and exploring if bacterial modulation of autophagy might impact MR1 antigen presentation.

Expertise: MR1 trafficking and antigen presentation, MAIT cell activation, cell and molecular techiques, statistical analyses. Difficult to assess: the relevance of these marker in the autophagy field and evaluating the technical methods for LC-MS/MS.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

Summary

In this study, Phalora et al identified the selective autophagy receptor SQSTM1/p62 as a MR1 interacting protein by proteomics approach using a cell line overexpressing MR1. While SQSTM1/p62 is implicated in autophagy regulation and autophagosome formation, genetic ablation of SQSTM1/p62 resulted in enhanced MAIT cell activation upon challenge with E. coli, but not with a synthetic agonist 5-OP-RU. In contrast, knockout of Atg5 and Atg7, both of which are involved in phagophore expansion engendered increased activation of MAIT cells upon both stimuli. From these data, the authors concluded that some factors in autophagy controlled the MR1 activity, thus the autophagy is a pivotal regulator of cellular antigen presentation.

Major comments:

1. The notion that "This regulation appears to occur at an early step in the trafficking pathway." in the summary appears not to be compatible with the present data. What the authors have shown in the study is possible implication of autophagy components such as SQSTM1/p62, Atg5, and Atg7 that are implicated in autophagosome and phagophore formation. Should the authors highlight an "early step of trafficking", Atg14L, Atg13, and/or Atg101 must be analyzed by genetic knockout in addition to PI3 kinase inhibitors that are supposed to affect an early step in autophagy. Such an approach could confirm whether the regulation of MR1 occurs at an early step of trafficking, or at least, at an early step of autophagy.
2. In Figure 2, while the degree of β2M depletion from B1 appears to be superior to that in B6 (Figure 2A), why the former was more potent in producing IFN-γ relative to the latter upon E. coli and 5-OP-RU (Figure 2D)?
3. In Figure 3B, right column, what is Ac-6-FP? The left histograms show MR1 expression level upon DMSO, E. coli, and 5-OP-RU challenge. There is no explanation.
4. Also in the same figure, was MR1 geomeans in Control, 5-1, 5-2, 5-3, 7-1, 7-2, and 7-3 upon Ac-6-FP superior to DMSO? If so or not, please explain the rational.
5. Figure 3C is highly intentional. If the authors put two left panels together (Control, 5-1, 5-2, and 5-3), is there still statistical difference among them?
6. There was no explanation for Figure 4B why the authors used Hela-MR1-HA. Other cell lines were used in the rest of the experiments. It is highly desirable to perform the experiment with THP1-MR1-HA in terms of logical development.
7. In addition, Figure 4B represent only the non-activated status. Given that association of SQSTM1/p62 with MR1 is dependent on E.coli and/or 5-OP-RU (Figure 1A), the same immuno-fluorescent imaging in the presence of the inhibitors upon stimulation with these reagents would also be desirable. It will uncover whether MR1 and SQSTM1/p62 colocalize upon stimulation, and such colocalization is perturbed in the presence of the inhibitors.
8. Whereas the authors addressed the question as to at which stage MR1 is regulated in trafficking in Figure 5, there was no experiments with 5-OP-RU (an agonist for MAIT cells). This casts the doubt whether observed phenotype really represented the true MR1 trafficking, because there is no guarantee that the trafficking pathway for antagonist (Ac-6-FP) is same as that for agonist.
9. Given the importance of MR1 overexpression in showing the association between MR1 and SQSTM1/p62, it is worthwhile to consider performing the knockout experiments with Thp1-MR1-HA rather than Thp1. It will further clarify the role(s) of SQSTM1/p62, Atg5, and Atg7 in MR1 trafficking and resultant MAIT cell activation.

Minor comments:

1.Please explain why the authors failed to detect IL23A in the coimmunoprecipitation. Should MR1-IL23A interaction be specific, what is a biological significance? 2. When Hela-MR1-HA was used, did the authors obtain the same results as Thp1-MR1-HA as shown in Figure 1C-D? This is relevant to the specificity in the interaction between MR1 and SQSTM1/p62 as shown in Figure 4B. 3. While S1, S2, S3, and S4 showed a similar degree of SQSTM1 depletion in Figure 2A, there was difference in the potential of IFN-γ production from MAIT cells among the clones. Only S4 showed decreased potential for IFN-γ upon 5-OP-RU, though E. coli failed to so. Contrary to 5-OP-RU, S1-S3 showed an enhanced potential while S4 failed to do so. Why is that so? 4. Given that there was little correlation between MR1 expression level and the potential of S1-S4 to promote or inhibit the ligand-dependent production of IFN-γ (Figure 2C right panel and Figure 2D), it is difficult to conclude that the factors implicated in autophagy play a pivotal role in MR1-dependent MAIT cell activation. 5. There was no consistency in the experimental design for Figure 5. Please explain the rational why the authors have used 7.1 in A and C, but not in B, D and E? 6. The control appeared to behave as 7.1 did. Was there statistical difference between 7.1 and 7.2 in Figure 5C? If so, what is the interpretation. 7. Time course over 6 h will be required to assess the MR1 expression in Figure 5C.

Significance

The present study uncovered the possible implication of autophagy factors in MR1 trafficking, in other words, MAIT cell activation. Although the previous study has demonstrated the importance of the protein loading factors (McWilliam et al., PNAS,117 24974-24985 2020), this study adds another pathway for MAIT cell activation. However, the conceptual significance is limited in that depletion of the factors pertinent to autophagy such as Atg5 and Atg7 in Thp1 resulted in rather weak interference in terms of MR1 trafficking and MAIT cell activation. Thus, this study will interest those who work in basic immunology, in particular, in regulation of antigen-presentation molecules and T cells as well as those who are in the field of MAIT cell biology.

Although the field of this reviewer covers biochemistry, molecular biology, developmental biology, immunology and regenerative medicine, proteomics approach (in detailed technique) as seen here to identify the associated molecules is somewhat beyond the reviewer's expert.

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Reply to the reviewers

Reviewer #1

1. The inverse relationship between PGCLC and DE efficiency is intriguing but under-explored. The observation that lines efficient for PGCLCs (Podx1, Kolf2) are poor at DE differentiation, and vice versa, is one of the key findings. Yet this is presented almost in passing. It would strengthen the paper considerably if the authors discussed whether their Polycomb-regulated gene set predicts DE efficiency with an inverse sign, and whether the logistic regression model can be tested on the DE data directly.

As suggested by the reviewer, we have enhanced our analysis of definitive endoderm (DE) differentiation efficiency and discussed it more prominently in the manuscript in the section “A subset of Polycomb targets is predictive of differentiation properties”. In particular, we now examine the correlation between gene expression from RNAseq and DE differentiation. For this purpose, we took the genes used to predict PGCLC efficiency (all of which are regulated by H3K27me3), and examined the correlation between their expression and the efficiencies of PGCLC and DE differentiation. We found that that differentiation is not a binary outcome for DEs, with many intermediate cases observed. Thus, instead of using a logistic regression, we employed a sigmoidal regression scheme for DEs. For this analysis, we used the absolute difference between observed and predicted efficiency, resulting in a mean absolute error of 12% [95% CI: 8-22%].

We have now included an extra panel (Figure 7C) showing the correlations between expression of the H3K27me3 genes and the differentiation efficiencies in both PGCLC and DE fates. As anticipated by the reviewer, this plot reveals an inverse correlation, which we highlight in the main manuscript. Further, we now mention that these genes can also be used to predict DE differentiation efficiency, with satisfactory accuracy (although the confidence interval is wide due to the small sample size, as in the case of PGCLCs).

The mathematical model is elegant but the choice to vary parameter E across cell lines needs stronger justification. The model assumes that inter-line differences are driven by variation in the overall rate of H3K27 methylation (parameter E). This is a reasonable starting assumption, but the authors should discuss alternative scenarios more explicitly. Could variation in demethylase activity, PRC2 recruitment strength, or replication timing equally well explain the data? The fact that EPOP is differentially expressed is mentioned as a potential mechanistic candidate for modulating E, which is compelling, but the link remains correlative. The authors should be more cautious in their language here, stating that EPOP "may be sufficient to completely switch the transcriptional regulation" goes beyond what the data show.

We thank the Reviewer for these suggestions and have tightened our discussion of these points. It is correct that variation in demethylase activity can also explain our data. We now explicitly point this out in the section “The behaviour of H3K27me3 can be explained using a simple mathematical model”. However, this possibility does not fit as well with the RNA expression data. While we found differential expression of the PcG gene EPOP, we did not detect any differential expression of the KDM6 histone demethylases (KDM6A-KDM6C). Therefore, we still favour our original suggestion of variation in the methylation rates over this possibility. In addition, we have moderated our wording on EPOP, stating in the Discussion that changes in EPOP expression “may be sufficient to alter the transcriptional regulation of specific target genes.”

The predictive model for differentiation efficiency is promising but the PGCLC training set is too small for confident generalisation claims.The authors acknowledge this (109 features, ~21 data points), and the L2 regularisation is appropriate. However, the claim of 91% accuracy with a 95% CI of 78-100% on the PGCLC data should be presented more cautiously. With such a small dataset, the confidence interval is very wide. The more convincing validation comes from the DN data (143 lines from Jerber et al.), where the model trained on PGCLC data performs comparably to the full-transcriptome model. This cross-fate generalisation is quite strong and should be emphasised more prominently as the primary evidence for the validity of the model.

We have followed the reviewer’s guidance and revised our language, when discussing the PGCLC case in the section “A subset of Polycomb targets is predictive of differentiation properties”. We have also emphasised more clearly the successful validation of the DN data.

1. The claim of "epigenetic memory" during differentiation (iPSC to pre-ME) is suggestive but would benefit from additional analysis. The authors show that 60% of pre-ME DEGs overlap with iPSC DEGs, and that H3K27me3-cluster genes maintain their expression patterns. However, 60% overlap could partly reflect genes that are simply not regulated during the short 12-hour pre-ME induction. To strengthen this claim, the authors should compare the overlap rate for H3K27me3-cluster genes specifically versus other clusters. If Polycomb targets show significantly higher overlap than, for example, K4&ATAC genes, this would more convincingly support a Polycomb-specific memory mechanism.

We have now performed this analysis, examining the persistence of DEGs into the pre-ME state (i.e., whether a gene that was differentially expressed in hiPSCs remains differentially expressed in pre-ME). Excluding the H3K9me3 cluster (the smallest cluster containing fewer than 25 genes), the K27 cluster is the most persistent cluster in terms of fraction of genes per cluster. When the clusters were pooled into the different variables involved (ignoring H3K9me3), H3K27me3 again emerged as the most persistent chromatin feature. Unfortunately, however, these results were not statistically significant, so we are unable to include them in the manuscript.

Lack of genetic background analysis. Ten lines from nine donors will harbour substantial genetic variation. The authors note that genetic variation has been linked to iPSC heterogeneity but do not analyse whether the three "outlier" lines (Kucg2, Sojd3, Yoch6) share genetic features. For instance, common variants at PRC2 component loci, EPOP regulatory variants, or structural variants that might alter H3K27me3 domain boundaries. The HipSci consortium provides genotyping data for these lines. A targeted analysis of variants at Polycomb-related loci would be feasible and could either strengthen the epigenetic interpretation or reveal a genetic confounder.

We thank the Reviewer for raising this important point. To investigate potential confounding effects due to genetic variation between the hiPSC lines in our panel, we performed a targeted analysis of genetic variation across Polycomb-related loci (H3K27me3 occupied loci and Polycomb group genes) in all ten cell lines (using whole genome sequencing data from the HipSci consortium). This analysis specifically tested whether the three “compromised” lines (Yoch6, Sojd3 and Kucg2) share consistent genetic variants relative to the seven “normal” lines. We identified 15 indels (out of 4115) that satisfied this criterium. However, all are located in non-coding regions and none overlap with ATAC-seq peaks. Hence, they are unlikely to function as gene regulatory elements (e.g., enhancers), but we cannot exclude the possibility that they affect gene expression in other ways. We have added a new Results section “Genetic variants shared between differentiation-compromised hiPSC lines” to discuss these points, as well as adding new text to the Discussion and Methods.

Minor Comments

The promoter definition ({plus minus}1 kb from gene start) is non-standard; most studies use a window upstream of the TSS rather than gene start. The authors mention they confirmed robustness to an alternative definition (-1 kb to gene start) but do not show this data. It should be included in the supplement.

We now show the data for the alternative promoter definition in Supplementary Fig. 5B and Supplementary Fig. 7C. These results demonstrate that our conclusions are robust to different promoter definitions.

For CUT&Tag, no spike-in normalisation is mentioned. Given that the key conclusions is based on quantitative comparisons of H3K27me3 levels across cell lines, the absence of spike-in controls is a potential concern. The authors should discuss whether technical variation between CUT&Tag libraries could contribute to the observed bimodality. At minimum, the correlation between replicates for H3K27me3 should be shown (presumably it is high, but this should be documented).

We thank the Reviewer for this suggestion. As now shown in Supplementary Fig. 4C, the correlation between our H3K27me3 replicates is indeed high (R between 0.93 and 0.96). Hence, technical variation between CUT&Tag libraries is unlikely to contribute to the observed bimodality.

The statistical test for the PGCLC/H3K27me3 overlap (p We thank the reviewer for noticing this. Indeed, this is the case. The test assumes independence of lines, which is in general a reasonable assumption, but may not always hold. Specifically, the Kolf2 and Kolf3 lines are derived from the same donor, which implies they are not completely independent. However, for all other lines, we still think independence is a reasonable assumption and, thus, the overall result of the test should be a good approximation. We have added this caveat to the manuscript.

Figure 6A: the heatmaps for H3K4, ATAC and H3K27 are shown side by side but at apparently different scales; this should be clarified or made consistent.

Indeed, the scales in all heatmaps are the same. We have clarified this in the captions of the figures.

Reviewer #2

1.) Figure 2B. Are all GO terms shown in the figure or are these just the top terms? If this is a suset then all terms should be provided as a supplemental table. If this is all significant terms, this is relitavely modest considering the number of DEGs (712) and is probably due to the fact that DEGs are derived from all comparisons and so could be diluted by the presence of multiple opposing effects. If this is the case, you could identify DEGs that define the PCA groupings and then re-run the GO analysis to potentially provide a better definition of the functional differences between groups of cell lines.

The GO terms previously displayed were the top hits. We have now included all the significant terms in Supplementary Files 4 and 5 (for the Molecular Function and the Biological Process ontologies, respectively).

Chromatin accessibility at gene promoters is a poor predictor of transcription, but it is likely that accessibility at distal regions (e.g putative enhancers) might be a better predictor. Did the authors look at this? This possibility should at least be mentioned when discussing the ATC-seq data and the lack of correlation with transcription.

• *

We thank the reviewer for this suggestion. To locate additional regulatory regions, we downloaded tracks for the enhancer-associated marks H3K4me1 and H3K27ac for the ten cell lines from Todd and colleagues (Todd et al., Genome Biology, 2025; https://genomebiology.biomedcentral.com/articles/10.1186/s13059-025-03658-8). We then intersected the ATAC-seq peaks with the H3K4me1 peaks in each cell line to identify putative enhancers. For each protein coding gene, we then identified the closest ATAC and H3K4me1 positive peak (among all cell lines), which we assumed was the most likely enhancer for that gene. We then evaluated the ATAC, H3K27ac and H3K27me3 signal within these enhancers for each cell line. With this information, we tried using a version of our SVM-based pipeline to improve our understanding of transcriptional regulation in genes within the ‘origin’ cluster (for which we failed to get significant insights from our standard SVM approach). Thus, we used seven variables as an input for the SVM: The four of the standard approach and three additional variables from the ATAC/H3K27ac/H3K27me3 signal at the nearest enhancer. However, for genes with an enhancer closer than 100kb, the performance of the SVM with enhancer variables was similar to the standard SVM (or slightly worse). If we focused on genes with enhancers 10kb or closer to the TSS (75 genes), then the SVM with the enhancer signal did modestly improve the prediction. However, when analysing the results more closely, it was only for a handful of genes (around 10) where the usage of the enhancer data was beneficial, and, even then, it was mostly down to the H3K27me3 signal rather than the more standard enhancer marks, such as H3K27ac or chromatin accessibility. This lack of improvement in the accuracy is probably due to our inability to identify the correct enhancers, as distance on the linear genome scale is often a poor predictor of enhancer-promoter interactions.

Ultimately, because the improvement is for such a small number of genes, we have not included this analysis in the manuscript. However, we do now mention in the manuscript in section “Chromatin accessibility does not always correlate with transcription” that we tried to include distal enhancers but that this approach was not successful.

2.) Fig 1C. Statistic overview at end of legend should be moved under section describing panel C in the legend.

We have now made this change.

3.) 'Furthermore, the transition value of 30% enables repression to be stably maintained even after DNA replication, when, on average, histone modification levels will be transiently halved'. Whilst this is potentially true and a plausible interpretation, you cannot exclude that the signal is not derived from different cell populations in the culture due to cellular heterogeneity such as cell cycle or spontaneous differentiation. This possibility should be noted in the text.

We thank the Reviewer for this suggestion. Due to the possible alternative explanations pointed out by the reviewer, and to minimise any possible misunderstandings, we decided to drop this sentence from the manuscript, which is not required for any of our main conclusions.

4.) 'Higher values indicate stronger correlation or anticorrelation and, thus, stronger differences between cell lines.' I don't believe this makes sense as written. Do the authors mean stronger partitioning of different iPSC lines into clusters?

Indeed, this sentence wasn’t very clear -- we have now rewritten it to improve clarity: “Because absolute correlation values were used, high values indicate that expression profiles between two cell lines are either highly correlated or highly anticorrelated. Across all pairwise comparisons, high values suggest strong partitioning of cell lines with highly similar or markedly different transcriptional profiles.”

5.) 'We found that 60% of the DEGs in pre-ME were also DEGs in hiPSCs'. This needs to be made clearer. Do the authors mean DEGs between iPSCs following differentiation or DEGs between undifferentiated iPSCs and their differentiated derivatives? The former suggests that the iPSCs are already partially differentiated and that differentiation in promoted or constrained by this starting state whilst the latter would suggest that some lines are skewed towards the mesendoderm.

We mean that of the genes that are differentially expressed between the 10 lines in pre-ME, 60% were also differentially expressed between the 10 lines in iPSCs (prior to differentiation). We have reworded this sentence to make it clearer.

6.) 'Finally, histone marks in the iPSC state were also predictive of expression in the pre-ME state, albeit with slightly lower accuracy than for the iPSC state (Supplementary Fig. 8C, D), which may indicate the existence of an epigenetic memory system that is maintained during differentiation.' Or the retention of an epigenetic signature that failed to be erased during the initial generation of the iPSCs.

We agree with the reviewer that this is entirely possible: our point is that memory states may persist from iPSCs to pre-ME. The memory state may of course predate the initial generation of the iPSCs. We have amended the section “Pre-ME transcriptomes suggest inheritance along the developmental trajectory” to include this possibility.

7.) 'To minimise the risk of overfitting, only reliable targets were retained'. Whilst this is outlined in the methods as stated, a summary of what this means should be included in the body text.

We thank the Reviewer for this suggestion. We have included the required extra text in the section “A subset of Polycomb targets is predictive of differentiation properties”. We have also revised the performance metrics so that they are strictly comparable with the results of Jerber and colleagues (which implies, in some cases, removing error bars, as in the results of Jerber et al., 2021). The reviewer may notice differences in the values reported but all our claims remain valid.

Reviewer #3

The major claim that among histone modifications that have been profiled in this manuscript, H3K27me3 is the most predictive for expression is supported by the analysis. However the analysis may be skewed because the RNAseq and the H3K27me3 difference are driven by the extreme skewing of the 3 cell lines Yoch6, Sojd3 and Kucg (Fig 2A, 2C and 6A). Two of these lines cannot form EBs at all, a major failure in their pluripotent characteristics.

We thank the reviewer for raising this fundamental point. Our aim for this study was to use iPSC lines that have passed existing standards and could easily be chosen from a panel of lines by an unsuspecting user. Indeed, the differentiation-compromised lines in our study are indistinguishable from other PSCs from a validated source that extensively characterises the distributed material (HipSci resource, https://www.hipsci.org). This source categorises these cell lines as correctly reprogrammed and fully pluripotent. In addition, we now present PluriTest data (doi: 10.1038/nmeth.1580) from all normal lines available from the HipSci resource (835 lines) and highlight the ten cell lines used in this study (see Supplementary Fig. 1A). All cell lines in our panel have pluripotency scores over 20, and all but one (Bima1 – which notably differentiates efficiently into PGCLCs and DNs) have novelty scores below 1.67; these values have been empirically determined as pluripotency signature thresholds (Müller et al., 2011). This analysis clearly demonstrates that the cell lines in our study are not outliers, an important fact which we have now added to section “Marked differences in the developmental efficiency of hiPSC lines”.

Furthermore, one of the key advances of our study is that we identify a chromatin and transcription signature that will enable researchers in the stem cell community to identify iPSC lines with compromised differentiation potential early on. We also note that compromised differentiation potential is widespread among human PSCs. For example, Jerber et al. report that 48 out of 183 hiPSC lines could not be differentiated successfully into dopaminergic neurons (doi:10.1038/s41588-021-00801-6). Thus, our study addresses an important and widespread issue in the stem cell field, a point we now emphasise in the introduction of the manuscript.

Further, one of the lines that can form EBs, fails to make PGCLCs but can differentiate into DE, Letw5 has neither the RNA profile nor the H3K27me3 profile of the skewed iPSC lines. Therefore, whether H3K27me3 truly influences phenotype at least in terms of PGCLC and DE differentiation of iPSCs is not supported by the analysis in the manuscript.

We agree that the behaviour of Letw5 is interesting, and we discuss its properties extensively in section “Marked differences in the developmental efficiency of hiPSC lines” and Fig. 1E. As we state, comparing Letw5 with Kucg2, “These findings suggest that Kucg2 hiPSCs have limited developmental competence to generate PGCLCs, while Letw5 hiPSCs are capable of PGCLC specification but fail to sustain the germ cell fate, pointing to a defect in fate maintenance rather than in initial developmental capacity.” Hence, the evidence points towards Letw5 having a separate defect which is unrelated to the impaired Polycomb regulation identified in the other three problematic lines. We also emphasise this point in section " A major role for H3K27me3 in hiPSC transcriptional heterogeneity", where we state that "[...] in this case [Letw5], a distinct mechanism, independent of H3K27me3 dysregulation, may result in impaired germ cell development."

1. What are the predictions from applying SVM to data from only the 6 cell lines Podx, Kolf2, Kolf3, Bima 1, Qolg1, Wibj2. The DE differentiation potential will also have to be measured for each of these cell lines.

Following the reviewer’s suggestion, we applied the SVM only to data from those six cell lines (which do not include any of the defective cell lines), see section “Linking variation in chromatin features with transcriptional output using SVMs”. Given that the SVM only takes as input data from differentially expressed genes, the set of genes used decreased markedly as there are fewer genes differentially expressed among these cell lines (125 DEGs). Nevertheless, for this subset of genes, the SVM still retains satisfactory accuracy (both AUROC and overall accuracy in the 70% to 75% range; now shown in Supplementary Fig. 6H). This result is particularly remarkable given that the SVM is operating with very little data (five datapoints for training and one for testing, per gene) and that the cell lines are very similar to each other. As the reviewer points out, we hope these results might encourage other researchers to pursue similar analysis approaches.

For DE differentiation, we previously included data (Supplementary Fig. 3B, C) for the following lines: Podx1, Kolf2, Kucg2, Letw5, Sojd3, and Yoch6. Only Kolf3, Bima1, Qolg1 and Wibj2 were missing. We have also now measured DE differentiation in three remaining lines (Kolf3, Qolg1, and Wibj2).

The above analysis may also shed light on howextreme the input parameters must be for SVM to be a good classifier? Such an analysis may also assist future users of the method to assess whether SVM would be useful for their datasets.

Please see our previous answer. We argue that the results presented above for six similar cell lines imply that this type of computational approach can have general applicability and does not require extreme inputs. We have followed the Reviewer’s suggestion and now incorporate this finding in section “Linking variation in chromatin features with transcriptional output using SVMs”: “Furthermore, the SVM does not require extreme values or outliers, and hence the overall approach could be of rather general applicability. As a performance verification, we applied the SVM to a dataset containing only the cell lines that could generate PGCLCs with high or intermediate efficiency, and while the performance is slightly reduced, it remains satisfactory (accuracy 75%; Supplementary Fig. 6H).”

If the SVM on the 6 lines does not predict a binary switch in H3K27me3 to be predictive could the authors incorporate DNA methylation and H3K4me1 from the same publication as the chromatin accessibility. Such an analysis may also assist future users of the SVM method to assess the number of parameters required to separate closely related phenotypes.

See previous answer. We note that DNA methylation data for our hiPSC panel is not available; it is not part of the study that the reviewer mentions (https://link.springer.com/article/10.1186/s13059-025-03658-8). Although H3K4me1 data is available in Todd et al., we did not find that this data improved the ability of our model to make successful predictions (see reply to Reviewer #2, point 1).

Most gene regulation occurs at the level of the enhancer, restricting analysis to promoter associated histone modifications is limiting.

We thank the Reviewer for raising this very valid point. Please see response to Reviewer #2, point 1.

One puzzling piece of data is the very high 60% of PGCLCs on day 1 of differentiation (Fig 1E) in the competent cell lines. BLIMP1 is expressed in hiPSCs, calling into question whether the initial differentiation into pre-ME was successful.

We think there is a misunderstanding regarding the experimental timeline. Day 1 of differentiation in Fig. 1E refers to one day after PGCLC induction from the pre-ME stage following the addition of BMP4, SCF, LIF, and EGF (see schematic in Fig. 1A). We have revised the text to make this clearer. Furthermore, BLIMP1 (PRDM1) is not expressed in hiPSCs. To demonstrate this, we now show the expression levels of BLIMP1 (PRDM1), B2M (low to mid-level expression in most human cell types), SOX2 (highly expressed pluripotency marker), and HOXC10 (differentiation marker that is not expressed in PSCs) across our cell line panel. At this scale, BLIMP1/PRDM1 expression is not detectable. When SOX2 is omitted from this bar plot, the very low expression levels of BLIMP1/PRDM1 become apparent, as it is close to the levels for the differentiation marker HOXC10. We conclude that BLIMP1/PRDM1 is expressed at extremely low levels across our ten hiPSC lines.

The H3K27me3 and H3K9me3 signals are integrated over the entire gene as inputs into the SVM, however PCA analysis to separate the cell lines is only shown for the promoter

This is not quite correct. For the PCA analysis for the histone marks and ATAC-seq, we used both the promoter region (Fig. 2C, Supplementary Fig. 5B) and the gene body (Supplementary Fig. 5A), with similar results. For the SVM, for H3K27me3 and H3K9me3, we primarily used the entire gene region, but we also tested other regions (Supplementary Fig. 6A), with similar or slightly inferior results.

SVMs have been used to predict enhancers from epigenomic data PMID: 22328731 and to classify cancers PMID: 11120680. Applying SVM as classifier for gene expression prediction is not very novel.

We thank the Reviewer for raising this point. We did not claim that the use of SVMs was itself novel. It has certainly been used in other contexts, as the reviewer points out, to predict enhancers, for cancer classification, and to predict expression patterns. In fact, SVMs had already been used to predict gene expression from chromatin features (Cheng et al, 2011; already cited in our manuscript). What is novel in our work is the reverse-engineering of the method to extract mechanistic information about each gene (i.e., assign a chromatin feature set relevant to the changes in expression). This computational methodology, in conjunction with the rich experimental dataset produced, allows us to classify differentially expressed genes in terms of the chromatin features that enable prediction of transcription. This highlights the differences between cell lines and enables further downstream analysis such as, mechanistic models of histone modification dynamics and the prediction of iPSC differentiation efficiency. We have rewritten the Introduction to the manuscript to better emphasise these points.

The biological insights are limited. For example, the observation that " a variety of forms of transcriptional regulation" Fig 4B. It is well known that H3K27me3 decorates lineage specifying genes and is part of the bivalent domain with H3K4me3. The anti-ATAC category could represent locations where a repressor is bound DNA which would also result in increased accessibility and is not a surprising result.

We believe our work does offer significant biological insights. While we agree that it is well known that H3K27me3 decorates lineage specifying genes, it was not previously known that digital Polycomb dysregulation at specific loci was a key feature controlling the ability of pluripotent cell lines to differentiate properly. In addition, we have been able to identify a core set of genes whose H3K27me3 profiles are highly informative for differentiation efficiency. Moreover, we are able to explain the variation in H3K27me3 levels by simple, quantitative, mathematical model.

Finally, the anti-ATAC category is a minor finding and not one of the central conclusions of this paper. Nevertheless, we appreciate the Reviewer’s suggestion and have incorporated this possible interpretation into section “Chromatin accessibility does not always correlate with transcription”.

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Referee #3

Evidence, reproducibility and clarity

Human induced pluripotent stem cells (iPSCs) have variable differentiation capability and can demonstrate bias toward specific lineages. In this manuscript, try to identify epigenetic features that may explain biased differentiation. They perform RNAseq and CUT and TAG for H3K4me3, H3K27me3 and H3K9me3 on 10 hiPSC lines which some of which show a opposing differentiation potential toward primordial germ cell like cells (PGCLCs) or definitive endoderm (DE). Using a support vector machine per gene that is variably expressed, they identify combinations of epigenetic marks and accessibility that could explain the change in expression. They identify H3K27me3 as a binary switch with high enrichment of this modification, predicting repression.

The major claim that among histone modifications that have been profiled in this manuscript, H3K27me3 is the most predictive for expression is supported by the analysis. However the analysis may be skewed because the RNAseq and the H3K27me3 difference are driven by the extreme skewing of the 3 cell lines Yoch6, Sojd3 and Kucg (Fig 2A, 2C and 6A). Two of these lines cannot form EBs at all, a major failure in their pluripotent characteristics. Further, one of the lines that can form EBs, fails to make PGCLCs but can differentiate into DE, Letw5 has neither the RNA profile nor the H3K27me3 profile of the skewed iPSC lines. Therefore, whether H3K27me3 truly influences phenotype at least in terms of PGCLC and DE differentiation of iPSCs is not supported by the analysis in the manuscript. Further analysis that may support their claim

1. What are the predictions from applying SVM to data from only the 6 cell lines Podx, Kolf2, Kolf3, Bima 1, Qolg1, Wibj2. The DE differentiation potential will also have to be measured for each of these cell lines.
2. The above analysis may also shed light on how extreme the input parameters must be for SVM to be a good classifier? Such an analysis may also assist future users of the method to assess whether SVM would be useful for their datasets.
3. If the SVM on the 6 lines does not predict a binary switch in H3K27me3 to be predictive could the authors incorporate DNA methylation and H3K4me1 from the same publication as the chromatin accessibility. Such an analysis may also assist future users of the SVM method to assess the number of parameters required to separate closely related phenotypes.
4. Most gene regulation occurs at the level of the enhancer, restricting analysis to promoter associated histone modifications is limiting.
5. One puzzling piece of data is the very high 60% of PGCLCs on day 1 of differentiation (Fig 1E) in the competent cell lines. BLIMP1 is expressed in hiPSCs, calling into question whether the initial differentiation into pre-ME was successful.
6. The H3K27me3 and H3K9me3 signals are integrated over the entire gene as inputs into the SVM, however PCA analysis to separate the cell lines is only shown for the promoter The recommended analysis above is not substantial because it only requires missing DE differentiation in terms of experiments. Data and methods have sufficient detail to be reproduced.

Referee cross-commenting

I agree with the other reviewer comments

Significance

The data generated and differentiation are useful for the hiPSCs community.

SVMs have been used to predict enhancers from epigenomic data PMID: 22328731 and to classify cancers PMID: 11120680. Applying SVM as classifier for gene expression prediction is not very novel.

The biological insights are limited. For example, the observation that " a variety of forms of transcriptional regulation" Fig 4B. It is well known that H3K27me3 decorates lineage specifying genes and is part of the bivalent domain with H3K4me3. The anti-ATAC category could represent locations where a repressor is bound DNA which would also result in increased accessibility and is not a surprising result.

Specialized for an audience of epigenetics and iPSC.

My expertise is in epigenetics, cell identity specification and pluripotency. I do not have expertise to evaluate accuracy of compuational method.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Miangolarra and colleagues explore functional heterogeneity in human iPSC, a characteristic which can impact on their translational utility. They characterise the capacity of ten iPSCs lines to differentiate in to either mesendoderm, primordial germ cell-like cells and/or definitive endoderm and explore the mechanistic basis of this potential by interrogating their transcriptional and epigenetic status using 'omics' approaches and mathematical modelling. The authors find that the iPSCs group based on differentiation capacity and their underlying transcriptional and epigenetic status, partitioning that is most tightly associated with H3K27me3 patterns that are binary in nature.

Key findings/outputs of the study: Inter-iPSC line variability in the differentiation tendency is reciprocal between PGCLCs and definitive endoderm.

Distinct differentiation/or maintenance capacities of iPSCs are governed/marked by altered H3K27me3 signatures.

Grouping of iPSC lines based on developmental capacity is demarcated by transcription profiles and their corresponding H3K27me3 patterns.

Chromatin accessibility at gene promoters is a relatively poor predictor of transcriptional status.

The transcription state of iPSCs is a good predictor of gene expression patterns following subsequent differentiation.

H3K27me3 shows a somewhat binary relationship with gene expression which the authors liken to a digital signature that is consistent with the read-write activity of PRC2.

A subset of H3K27me3 targets is strongly predictive of transcriptional state and differentiation capacity.

A machine learning approach that utilises integrated epigenome status to predicts high or low gene expression with high accuracy in iPSCs.

The authors present a large amount of high-quality data that is of broad interest to various fields as it provides: 1. Mechanistic insight into the epigenetic basis of gene regulation in human pluripotent cells. 2. A metric for assessing differentiation potential of pluripotent cells with important translational implications 3. Machine learning tools that could be of broad utility to the field of epigenetics and gene regulation (provided as well annotated code in Github).

Whilst this reviewer is unable to provide an in-depth assessment of the machine learning approach presented, the modelling and data handling is accessible. Whilst this study does not provide substantial biological insights, the collective works is of broad utility and interest to various fields and I believe can be published once the following minor comments/concerns are addressed.

Comments

Figure 2B. Are all GO terms shown in the figure or are these just the top terms? If this is a suset then all terms should be provided as a supplemental table. If this is all significant terms, this is relitavely modest considering the number of DEGs (712) and is probably due to the fact that DEGs are derived from all comparisons and so could be diluted by the presence of multiple opposing effects. If this is the case, you could identify DEGs that define the PCA groupings and then re-run the GO analysisto potentially provide a better definition of the functional differences between groups of cell lines. Chromatin accessibility at gene promoters is a poor predictor of transcription, but it is likely that accessibility at distal regions (e.g putative enhancers) might be a better predictor. Did the authors look at this? This possibility should at least be mentioned when discussing the ATC-seq data and the lack of correlation with transcription.

Fig 1C. Statistic overview at end of legend should be moved under section describing panel C in the legend.

'Furthermore, the transition value of 30% enables repression to be stably maintained even after DNA replication, when, on average, histone modification levels will be transiently halved'. Whilst this is potentially true and a plausible interpretation, you cannot exclude that the signal is not derived from different cell populations in the culture due to cellular heterogeneity such as cell cycle or spontaneous differentiation. This possibility should be noted in the text.

'Higher values indicate stronger correlation or anticorrelation and, thus, stronger differences between cell lines.' I don't believe this makes sense as written. Do the authors mean stronger partitioning of different iPSC lines into clusters?

'We found that 60% of the DEGs in pre-ME were also DEGs in hiPSCs'. This needs to be made clearer. Do the authors mean DEGs between iPSCs following differentiation or DEGs between undifferentiated iPSCs and their differentiated derivatives? The former suggests that the iPSCs are already partially differentiated and that differentiation in promoted or constrained by this starting state whilst the latter would suggest that some lines are skewed towards the mesendoderm.

'Finally, histone marks in the iPSC state were also predictive of expression in the pre-ME state, albeit with slightly lower accuracy than for the iPSC state (Supplementary Fig. 8C, D), which may indicate the existence of an epigenetic memory system that is maintained during differentiation.' Or the retention of an epigenetic signature that failed to be erased during the initial generation of the iPSCs.

'To minimise the risk of overfitting, only reliable targets were retained'. Whilst this is outlined in the methods as stated, a summary of what this means should be included in the body text.

Referee cross-commenting

I agree with the other reviewer's comments.

Significance

The presented manuscript investigates the molecular basis of developmental potential heterogeneity in human iPSCs. The study is clear, well presented and provides sufficient detail on methodology, reagents and computational tools to allow reproducibility. The claims made are supported by the data and analysis.

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Referee #1

Evidence, reproducibility and clarity

Summary

This study investigates the molecular basis of inter-line variability in human iPSC differentiation efficiency. The authors profile ten HipSci consortium hiPSC lines for transcriptome (RNA-seq), chromatin accessibility (ATAC-seq, from a prior study), and three histone modifications (H3K4me3, H3K9me3, H3K27me3) by CUT&Tag. They develop an SVM-based computational pipeline to link epigenomic variation to transcriptional differences across lines. The central findings are that H3K27me3 variation shows the most consistent inter-line differences, displays a bimodal (digital ON/OFF) distribution consistent with a mathematical model of PRC2 read-write feedback, and that a small set of Polycomb-regulated genes can predict differentiation efficiency into both PGCLCs and dopaminergic neurons. The authors also show that these transcriptional differences propagate into the pre-mesendoderm intermediate state, suggesting epigenetic memory during early lineage commitment. This is overall a very good study, with interesting and novel findings for the field. However, some issues should be addressed before publication:

Major Comments

1. The inverse relationship between PGCLC and DE efficiency is intriguing but under-explored. The observation that lines efficient for PGCLCs (Podx1, Kolf2) are poor at DE differentiation, and vice versa, is one of the key findings. Yet this is presented almost in passing. It would strengthen the paper considerably if the authors discussed whether their Polycomb-regulated gene set predicts DE efficiency with an inverse sign, and whether the logistic regression model can be tested on the DE data directly.
2. The mathematical model is elegant but the choice to vary parameter E across cell lines needs stronger justification. The model assumes that inter-line differences are driven by variation in the overall rate of H3K27 methylation (parameter E). This is a reasonable starting assumption, but the authors should discuss alternative scenarios more explicitly. Could variation in demethylase activity, PRC2 recruitment strength, or replication timing equally well explain the data? The fact that EPOP is differentially expressed is mentioned as a potential mechanistic candidate for modulating E, which is compelling, but the link remains correlative. The authors should be more cautious in their language here, stating that EPOP "may be sufficient to completely switch the transcriptional regulation" goes beyond what the data show.
3. The predictive model for differentiation efficiency is promising but the PGCLC training set is too small for confident generalisation claims. The authors acknowledge this (109 features, ~21 data points), and the L2 regularisation is appropriate. However, the claim of 91% accuracy with a 95% CI of 78-100% on the PGCLC data should be presented more cautiously. With such a small dataset, the confidence interval is very wide. The more convincing validation comes from the DN data (143 lines from Jerber et al.), where the model trained on PGCLC data performs comparably to the full-transcriptome model. This cross-fate generalisation is quite strong and should be emphasised more prominently as the primary evidence for the validity of the model.
4. The claim of "epigenetic memory" during differentiation (iPSC to pre-ME) is suggestive but would benefit from additional analysis. The authors show that 60% of pre-ME DEGs overlap with iPSC DEGs, and that H3K27me3-cluster genes maintain their expression patterns. However, 60% overlap could partly reflect genes that are simply not regulated during the short 12-hour pre-ME induction. To strengthen this claim, the authors should compare the overlap rate for H3K27me3-cluster genes specifically versus other clusters. If Polycomb targets show significantly higher overlap than, for example, K4&ATAC genes, this would more convincingly support a Polycomb-specific memory mechanism.
5. Lack of genetic background analysis. Ten lines from nine donors will harbour substantial genetic variation. The authors note that genetic variation has been linked to iPSC heterogeneity but do not analyse whether the three "outlier" lines (Kucg2, Sojd3, Yoch6) share genetic features. For instance, common variants at PRC2 component loci, EPOP regulatory variants, or structural variants that might alter H3K27me3 domain boundaries. The HipSci consortium provides genotyping data for these lines. A targeted analysis of variants at Polycomb-related loci would be feasible and could either strengthen the epigenetic interpretation or reveal a genetic confounder.

Minor Comments

• The promoter definition ({plus minus}1 kb from gene start) is non-standard; most studies use a window upstream of the TSS rather than gene start. The authors mention they confirmed robustness to an alternative definition (-1 kb to gene start) but do not show this data. It should be included in the supplement.
• For CUT&Tag, no spike-in normalisation is mentioned. Given that the key conclusions is based on quantitative comparisons of H3K27me3 levels across cell lines, the absence of spike-in controls is a potential concern. The authors should discuss whether technical variation between CUT&Tag libraries could contribute to the observed bimodality. At minimum, the correlation between replicates for H3K27me3 should be shown (presumably it is high, but this should be documented).
• The statistical test for the PGCLC/H3K27me3 overlap (p < 0.04, combinatorial argument) assumes independence of lines, which may not hold if genetic relatedness or batch effects are present. This should be noted.
• Figure 6A: the heatmaps for H3K4, ATAC and H3K27 are shown side by side but at apparently different scales; this should be clarified or made consistent.

Referee cross-commenting

I agree with the comments from other reviewers

Significance

This paper makes a primarily conceptual advance in understanding why iPSC lines differ in their differentiation capacity. The key insight is that Polycomb regulation operates in a digital (bistable) fashion at specific loci, and that this digital behaviour both explains the sharpness of inter-line transcriptional differences and enables prediction of differentiation outcomes from a small gene set. This work will be of broad interest to the stem cell biology community, particularly those working on iPSC-based disease modelling and cell therapy where line-to-line variability is a major practical challenge. The mathematical modelling component will appeal to quantitative/systems biologists interested in chromatin regulation. The computational pipeline may find applications beyond iPSCs, in any setting where epigenomic and transcriptomic data are available across multiple conditions.

Reviewer expertise: Developmental biology, chromatin regulation, iPSC differentiation, epigenetics.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

*Specific comments for revision - Major:

1) The benchmarking framework relies heavily on simulated mixtures as ground truth. However, these mixtures are derived from intracellular RNA profiles and may not fully capture the biological characteristics of cfRNA, including fragmentation patterns, differential release mechanisms, and extracellular stability. This raises concerns about whether the reported performance truly reflects real-world cfRNA scenarios. The authors should explicitly discuss the limitations of this pseudo-ground truth and the potential biases introduced by the simulation design. Incorporating cfRNA-specific features or alternative validation strategies would strengthen the reliability of the conclusions.*

Response: The reviewer highlights the framework's reliance on simulated mixtures, which may not fully capture the complexity of real-world cfRNA samples. We acknowledge this limitation and agree that simulated data cannot completely reproduce all biological and technical characteristics of cfRNA. Nevertheless, simulation-based benchmarking remains the current standard for systematically evaluating deconvolution methods because the true tissue and cell-type composition of cfRNA samples is not known. To improve the biological realism of our simulations, we incorporated two cfRNA-specific features: (i) the introduction of negative binomial noise to model technical and biological variability and (ii) the removal of rapidly degrading transcripts based on mRNA half-life, as published cfRNA data show rapidly degrading transcripts to be underrepresented.

To further address the reviewer's comments, improving representation of simulations to cell free RNA, we will include an additional cfRNA-specific benchmarking scenario based on detectability-filtered simulations. The simulated mixtures will be restricted to genes that are consistently detected across multiple published cfRNA cohorts and diseases, thereby better reflecting the subset of transcripts that are reliably measurable in cell free RNA.

2) The manuscript clearly demonstrates that cell type-of-origin deconvolution is substantially less robust than tissue-level inference. However, the explanation remains largely descriptive, focusing on transcriptional similarity and reference incompleteness. A deeper mechanistic analysis is needed to understand the root causes of this limitation. In particular, the authors should consider discussing the impact of collinearity between cell-type signatures, the identifiability of mixture models, and the role of signal-to-noise ratio in cfRNA data. Providing quantitative or theoretical insights would significantly enhance the contribution of the study.

Response: The reviewer highlights that the difference in performance between tissue- and cell-type-level inference is not fully explained. Our discussion focused on the larger number of potential contributors in COO inference, its greater sensitivity in signal-to-noise, and the ability of different methods to handle correlated signatures. TOO was evaluated using approximately 30 merged tissue groups, whereas COO inference used approximately 80 merged cell-type groups. The larger COO label space increases model dimensionality and the number of potential misassignment routes. Regarding signal-to-noise ratio, noise and degradation perturbations affect both TOO and COO inference, but COO is expected to be more sensitive because the transcriptional differences separating related cell types are smaller than those separating broader tissue groups. We evaluated seven deconvolution methods with different underlying assumptions across multiple reference configurations using matched TOO and COO frameworks. The observed variation across method–reference combinations indicates that both reference design and method-specific handling of correlated signatures, model constraints, and noisy inputs influence deconvolution robustness. The reviewer also correctly points out that collinearity between cell-type signatures may contribute to the reduced performance. To investigate this, we will calculate pairwise similarities between the reference signatures for all tissue and cell-type categories in each TOO and COO reference matrix. Analysis that is being undertaken suggests higher collinearity among the COO signatures. We will further examine the relationship between signature collinearity and deconvolution error to support per-cell-type error than versus per-tissue error.

3) The current evaluation focuses on reconstruction accuracy and correlation with biochemical markers, such as ALT. However, it remains unclear whether improved deconvolution performance translates into better clinical prediction or disease classification. Given the importance of cfRNA in biomarker discovery, the authors should consider evaluating the downstream utility of deconvolution outputs. For example, comparing predictive performance between raw cfRNA features and deconvolved proportions in classification or survival models would provide a more comprehensive assessment of practical value.

Response: We thank the reviewer for this excellent suggestion regarding the clinical utility of deconvolution outputs. We agree that evaluating whether improved deconvolution performance translates into better disease classification, prediction, or prognostic models would be an important step toward demonstrating the practical value of cfRNA deconvolution. However, we believe that such analyses are beyond the scope of the current manuscript. The primary objective of this study was to systematically benchmark tissue- and cell-type-level cfRNA deconvolution in a whole-body setting by comparing multiple deconvolution methods across different parameter settings and reference configurations. Our focus was therefore on establishing the analytical performance and robustness of existing deconvolution approaches rather than evaluating their downstream clinical applications. Importantly, a rigorous assessment of predictive performance would require carefully curated disease-specific cohorts, appropriate clinical endpoints, and models tailored to individual clinical questions, all of which introduce additional sources of variability beyond the deconvolution task itself. We agree that comparing disease classification or survival models based on raw cfRNA expression with those incorporating deconvolved tissue or cell-type proportions is a valuable direction for future work, and we will highlight this in the Discussion.

4) All evaluated methods belong to classical frameworks, including regression-based, Bayesian, and optimization-based approaches. Recent advances in machine learning, such as deep generative models and representation learning, are not considered in this study. The manuscript would benefit from discussing whether the observed limitations are intrinsic to the deconvolution problem or specific to current methodologies. Including a perspective on emerging approaches would improve the relevance of the work.

Response: This point is similar to that raised by Reviewer 2 (Major Point 3), related to advanced machine learning-based deconvolution approaches absent in our benchmark. We focused on benchmarking methods that have previously been applied to cfRNA deconvolution. While deep learning methods have recently emerged for transcriptomic deconvolution in less complex settings (reviewed in https://doi.org/10.1016/j.csbj.2025.05.038), they have not yet been systematically evaluated in a body-wide cfRNA deconvolution framework. To address this point, we will expand our benchmark by including the recently developed deep learning-based deconvolution method DECODE and evaluate its performance in cell-free RNA settings. In addition, we will expand the Discussion to provide a broader perspective on emerging machine learning approaches for deconvolution, discussing whether the limitations identified in this study primarily reflect fundamental challenges of the cfRNA deconvolution problem (e.g., reference collinearity and low signal-to-noise ratio) or limitations of current methodologies, as well as the potential suitability of these emerging approaches for cell-free transcriptomic applications.

*Specific comments for revision - Minor:

1) The study primarily relies on mean absolute error and Pearson correlation. While these metrics are appropriate, they may not fully capture compositional differences in deconvolution results. Including additional evaluation metrics would provide a more comprehensive assessment.*

Response: We thank the reviewer for this helpful suggestion. To provide an additional evaluation, we will include the Jensen–Shannon divergence (JSD) for each method–reference combination across the different deconvolution scenarios. As a distribution-based metric, JSD complements the existing performance measures by quantifying differences in the overall composition of the inferred tissue or cell type proportions. Because JSD depends on the number of categories in the composition, these comparisons will be performed within the same reference dataset, allowing us to assess how different deconvolution methods redistribute mass across a common set of tissues or cell types.

2) Although the methods are described, it is not entirely clear whether default parameters were used consistently across tools or whether any tuning was performed. Providing more explicit details on parameter settings would improve reproducibility and allow fairer comparison across methods.

Response: In the revised manuscript, we will provide more explicit details on the parameter settings to improve reproducibility. We will clarify whether the default parameters were used for each deconvolution method or whether any parameter tuning was performed, and include the relevant parameter settings in the Methods section.

Significance

This manuscript presents a comprehensive benchmarking study of tissue- and cell type-of-origin deconvolution methods in plasma cell-free RNA (cfRNA). The authors systematically evaluate seven widely used approaches across multiple simulated and clinical datasets, considering both methodological variability and reference-dependent effects. The inclusion of realistic simulation settings, such as noise and transcript degradation, together with validation on diverse clinical cohorts, strengthens the practical relevance of the work. The study addresses an important gap in the field, as cfRNA deconvolution is increasingly used in liquid biopsy applications but lacks standardized evaluation frameworks.

Reviewer #2

Evidence, reproducibility and clarity

The authors are evaluating the performance of seven cell-type deconvolution methods using cytoplasm-free mRNA. More specifically, they are benchmarking these methods at tissue and cell type levels, assigning the tissue or cell type of origin (TOO or COO) to the mixture. Using a benchmark relevant to the cfRNA context, they demonstrate that determining TOO is simpler than estimating COO. They also demonstrate that, overall, BayesPrism is the most reliable method for deconvoluting the cfRNA signal. Finally, the study has a more translational focus, correlating cfRNA deconvolution from a published dataset with biomarkers linked to tissue damage. The authors found that the results of RNA deconvolution are linked to biomarkers and could potentially be used to retrieve the disease-associated signal produced by injured tissue. COO is less correlated with the biomarkers than TOO, and BayesPrism outperformed the other deconvolution tools tested, strengthening the previous benchmarks.

Major comments: The manuscript is well structured and written relatively clearly. My main concern about the study is the choices made in its design. It is not always clear from the manuscript or the figures why these choices were made. While these choices are correct, their justification is either absent or poorly stated. This includes: - the removal of 10-40% of rapidly degrading rRNA from the signature matrices - central vs random (5, 10) reference profiles - maximum signature sizes - inner/outer merges on figure S7.

Response: In the revised version, we will provide rationale for the design decisions used in the manuscript. We will provide clearer justification for the removal of rapidly degrading mRNA from the signature matrices, the use of central versus random reference profiles, the maximum signature sizes, and the inner versus outer merge strategies used in Figure S7.

Another concern is that most end users are more interested in the relative differential abundance of cell types/tissues between samples than in the absolute proportions of cell types/tissues. Could the author create a figure showing which method can identify the cell types/tissues that are differentially present between samples, as the results can differ from the overall accuracy?

Response: We thank the reviewer for this valuable suggestion. We agree that, in many applications, users are more interested in relative differences in tissue or cell type abundance between samples. In the current manuscript, relative abundances of tissues and cell types of interest are presented in several figures, including Figures 6 and 7 and Supplementary Figures S12, S14, and S15. To address the reviewer's suggestion more directly, we will include an additional figure in the revised manuscript showing the distribution of estimated proportions for each tissue or cell type across individual samples, stratified by disease group and by study cohort. This will facilitate the identification of tissues and cell types that are differentially abundant between samples and complement the overall benchmarking results.

The panel of chosen deconvolution methods is fine. However, I would add Scaden or preferably DECODE to complete the methods with a deep learning approach. The analyses seem reproducible, and the code is already available and well organized.

Response: This point is similar to that raised by Reviewer 1 (Major Point 4). We will include DECODE in the revised benchmark and are currently training and evaluating DECODE for multi-organ cell-free RNA deconvolution task. Compared with Scaden, DECODE is a more suitable deep learning approach for this application. It is computationally efficient, which is advantageous for this more complex task, and, by design, can accommodate heterogeneous reference datasets with substantial batch effects.

Minor comments:

There are too many commas in the affiliations.

Response: This will be corrected in the resubmission.

The manuscript needs to cite Svenningsen et al. (2024): https://doi.org/10.1002/jev2.12511, as, to my knowledge, it is the only previous study of deconvolution from extracellular RNA.

Response: We will cite this reference in the revised manuscript.

Correlation figures such as S2A should be colored by cell type/tissue. If this results in too many colours, some cell types should be merged.

Response: This will be corrected in the resubmission. We will highlighting selected tissues and cell type examples. Including all 30 tissues and 80 cell types would make the figure uninterpretable, and merging would undermine the individual tissue and cell-type interpretation.

• *

Figure 4B: It is difficult to assess what constitutes a good result. Please add points of the ground truth if relevant.

• *

Response: Figure 4B shows the estimated proportions of brain cell types following deconvolution of bulk RNA-sequencing data derived from brain tissue. The expected total proportion across all inferred brain cell types is 100%. The purpose of this analysis is to evaluate how different method–reference combinations using the brain-augmented reference influence the inferred composition of brain cell types. We will revise the figure legend to clarify this.

There is a repetition in the Fig S7 legend (augmented with augmented with).

Response: This will be corrected in the resubmission.

Significance

*The use of deconvolution on cfRNA is novel and could contribute to bridging the gap between the development of deconvolution methods and their application, for example in a clinical context. This demonstrates that cell type (or tissue) deconvolution could be employed in personalized medicine applications.

The study also provides insights into how to benchmark deconvolution in the context of cfRNA, such as depleting low-half-life mRNA.

While this work does not present any new deconvolution methods, datasets or benchmarks outside the context of cfRNA, I believe its contribution is significant enough to be published and to reach a wide audience, ranging from deconvolution method developers to bioinformaticians working in the field of personalized medicine.

An interesting development of this work would be to further close the gap between benchmarks and the clinical use of cfRNA deconvolution by providing clearer usage guidance and testing it experimentally. Expertise of the reviewer: OMICS analyses, cell-type deconvolution*

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Referee #2

Evidence, reproducibility and clarity

The authors are evaluating the performance of seven cell-type deconvolution methods using cytoplasm-free mRNA. More specifically, they are benchmarking these methods at tissue and cell type levels, assigning the tissue or cell type of origin (TOO or COO) to the mixture. Using a benchmark relevant to the cfRNA context, they demonstrate that determining TOO is simpler than estimating COO. They also demonstrate that, overall, BayesPrism is the most reliable method for deconvoluting the cfRNA signal. Finally, the study has a more translational focus, correlating cfRNA deconvolution from a published dataset with biomarkers linked to tissue damage. The authors found that the results of RNA deconvolution are linked to biomarkers and could potentially be used to retrieve the disease-associated signal produced by injured tissue. COO is less correlated with the biomarkers than TOO, and BayesPrism outperformed the other deconvolution tools tested, strengthening the previous benchmarks.

Major comments:

The manuscript is well structured and written relatively clearly. My main concern about the study is the choices made in its design. It is not always clear from the manuscript or the figures why these choices were made. While these choices are correct, their justification is either absent or poorly stated. This includes:

• the removal of 10-40% of rapidly degrading rRNA from the signature matrices
• central vs random (5, 10) reference profiles
• maximum signature sizes
• inner/outer merges on figure S7.

Another concern is that most end users are more interested in the relative differential abundance of cell types/tissues between samples than in the absolute proportions of cell types/tissues. Could the author create a figure showing which method can identify the cell types/tissues that are differentially present between samples, as the results can differ from the overall accuracy?

The panel of chosen deconvolution methods is fine. However, I would add Scaden or preferably DECODE to complete the methods with a deep learning approach. The analyses seem reproducible, and the code is already available and well organized.

Minor comments:

There are too many commas in the affiliations.

The manuscript needs to cite Svenningsen et al. (2024): https://doi.org/10.1002/jev2.12511, as, to my knowledge, it is the only previous study of deconvolution from extracellular RNA.

Correlation figures such as S2A should be colored by cell type/tissue. If this results in too many colours, some cell types should be merged.

Figure 4B: It is difficult to assess what constitutes a good result. Please add points of the ground truth if relevant.

There is a repetition in the Fig S7 legend (augmented with augmented with).

Referees cross-commenting

I mostly agree with Reviewer #1. I would not consider the following two points to be mandatory: - A deeper mechanistic analysis to understand the root causes of the difference between COO and TOO. While the question of why is of the utmost interest, I feel it is outside the scope of the manuscript. However, the authors could discuss the potential causes of these differences in more detail in the discussion and leave the question open for future work in this domain. - The default parameters of the tools used are clear in the GitHub repository associated with the manuscript. I will leave it to the editor to decide whether it is sufficient or whether the methods section should be clearer, as Reviewer #1 suggests. I have no strong opinion about it.

Significance

The use of deconvolution on cfRNA is novel and could contribute to bridging the gap between the development of deconvolution methods and their application, for example in a clinical context. This demonstrates that cell type (or tissue) deconvolution could be employed in personalized medicine applications.

The study also provides insights into how to benchmark deconvolution in the context of cfRNA, such as depleting low-half-life mRNA.

While this work does not present any new deconvolution methods, datasets or benchmarks outside the context of cfRNA, I believe its contribution is significant enough to be published and to reach a wide audience, ranging from deconvolution method developers to bioinformaticians working in the field of personalized medicine.

An interesting development of this work would be to further close the gap between benchmarks and the clinical use of cfRNA deconvolution by providing clearer usage guidance and testing it experimentally.

Expertise of the reviewer: OMICS analyses, cell-type deconvolution

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Referee #1

Evidence, reproducibility and clarity

Specific comments for revision - Major:

1) The benchmarking framework relies heavily on simulated mixtures as ground truth. However, these mixtures are derived from intracellular RNA profiles and may not fully capture the biological characteristics of cfRNA, including fragmentation patterns, differential release mechanisms, and extracellular stability. This raises concerns about whether the reported performance truly reflects real-world cfRNA scenarios. The authors should explicitly discuss the limitations of this pseudo-ground truth and the potential biases introduced by the simulation design. Incorporating cfRNA-specific features or alternative validation strategies would strengthen the reliability of the conclusions.

2) The manuscript clearly demonstrates that cell type-of-origin deconvolution is substantially less robust than tissue-level inference. However, the explanation remains largely descriptive, focusing on transcriptional similarity and reference incompleteness. A deeper mechanistic analysis is needed to understand the root causes of this limitation. In particular, the authors should consider discussing the impact of collinearity between cell-type signatures, the identifiability of mixture models, and the role of signal-to-noise ratio in cfRNA data. Providing quantitative or theoretical insights would significantly enhance the contribution of the study.

3) The current evaluation focuses on reconstruction accuracy and correlation with biochemical markers, such as ALT. However, it remains unclear whether improved deconvolution performance translates into better clinical prediction or disease classification. Given the importance of cfRNA in biomarker discovery, the authors should consider evaluating the downstream utility of deconvolution outputs. For example, comparing predictive performance between raw cfRNA features and deconvolved proportions in classification or survival models would provide a more comprehensive assessment of practical value.

4) All evaluated methods belong to classical frameworks, including regression-based, Bayesian, and optimization-based approaches. Recent advances in machine learning, such as deep generative models and representation learning, are not considered in this study. The manuscript would benefit from discussing whether the observed limitations are intrinsic to the deconvolution problem or specific to current methodologies. Including a perspective on emerging approaches would improve the relevance of the work.

Specific comments for revision - Minor:

1) The study primarily relies on mean absolute error and Pearson correlation. While these metrics are appropriate, they may not fully capture compositional differences in deconvolution results. Including additional evaluation metrics would provide a more comprehensive assessment.

2) Although the methods are described, it is not entirely clear whether default parameters were used consistently across tools or whether any tuning was performed. Providing more explicit details on parameter settings would improve reproducibility and allow fairer comparison across methods.

Significance

This manuscript presents a comprehensive benchmarking study of tissue- and cell type-of-origin deconvolution methods in plasma cell-free RNA (cfRNA). The authors systematically evaluate seven widely used approaches across multiple simulated and clinical datasets, considering both methodological variability and reference-dependent effects. The inclusion of realistic simulation settings, such as noise and transcript degradation, together with validation on diverse clinical cohorts, strengthens the practical relevance of the work. The study addresses an important gap in the field, as cfRNA deconvolution is increasingly used in liquid biopsy applications but lacks standardized evaluation frameworks.

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Reply to the reviewers

Response to Reviewer's Comments

We thank the reviewers for their careful, constructive, and encouraging assessment of our manuscript. As described in detail in the point-by-point response below, we have extensively revised the manuscript and Supplementary Information. Together, these changes provide further support for the role of Rlig1 in neural function and visually guided behaviour during zebrafish development.

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

Summary: Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

This study characterizes the function of RNA ligase 1 (Rlig1) in the vertebrate model zebrafish. Rlig1 is one of only two known RNA ligases in vertebrates, and its biological roles remain poorly understood. The authors combine gene expression analysis, loss-of-function approaches, transcriptomic profiling, calcium imaging, and behavioral assays to investigate its function during development. They show that loss of rlig1 (including maternal-zygotic loss) has no major effects on development or morphology, but that it leads to impairments in visually-guided behavior and altered neuronal activity in response to visual stimuli. Transcriptomic analyses reveal widespread dysregulation across multiple developmental stages, nominating genes that may underly the observed neural phenotypes. Together, the findings support a role for Rlig1 in neural development and function in vertebrates.

We thank the reviewer for this accurate and positive summary of our study and for recognising the complementary, multi-level approaches used to examine the in vivo role of Rlig1.

Major comments: - Are the key conclusions convincing?

The key conclusion of this study is that Rlig1 plays an important role in the development and function of vertebrate neural circuits. Overall, this overarching conclusion, as well as the individual conclusions from each set of experiments, are well supported by the data presented. The combination of tissue-specific expression of rlig1, robust behavioral phenotypes in mutants, transcriptomic changes across multiple developmental stages, and circuit differences observed through calcium imaging provides a coherent, multi-faceted argument for the importance of this enzyme in brain development and function. While the precise RNA substrates of Rlig1 and the mechanistic link between transcriptomic changes and neural phenotypes remain to be defined, the authors clearly acknowledge these next steps and limitations. This study is a critical foundation for those future experiments.

We appreciate the reviewer’s positive assessment of the strength and coherence of the evidence.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

The claims in the manuscript are generally well-supported. The authors clearly acknowledge limitations and future experiments to further dissect mechanism in the Discussion section.

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

No major additional experiments appear essential for supporting the current claims.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

No experiments are required for the current claims of the manuscript.

We thank the reviewer for this assessment.

• Are the data and the methods presented in such a way that they can be reproduced?

The methods are generally well described. I would suggest that the "raw images, data, and source code for custom scripts used in this work" be made accessible without having to request from the authors. Zenodo provides up to 50 GB of storage, which is likely sufficient for the data presented in this manuscript. In particular, I think it is important to share the behavior analysis, calcium imaging pipeline, and transcriptomics analysis. Even if all the data is too large, a sample dataset and analysis scripts should be publicly available.

We agree and thank the reviewer for this important suggestion. To ensure that the study can be reproduced without the need to contact the authors, we have made the underlying data and custom analysis code publicly accessible. The RNA-seq data have been deposited in the GEO repository under accession number GSE308510 and are available at https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE308510.

In addition, the raw imaging data, behavioural and calcium-imaging datasets, processed data, and custom scripts used for the behavioural, calcium-imaging, as well as the tRNA and rRNA sequencing data have been deposited on KonDATA (DOI: 10.48606/vpwgm69277srrgaj) – together more than 190 GB – and can be accessed using this link: https://kondata.uni-konstanz.de/radar/en/dataset/vpwgm69277srrgaj?token=gLEaYEENHjmHBhjhHUHK.

We have revised the Data and code availability statement in the manuscript accordingly.

• Are the experiments adequately replicated and statistical analysis adequate?

The experiments appear adequately replicated, and statistical analyses are appropriate for the types of data presented.

We thank the reviewer for this positive assessment. To further improve transparency, we have revised the figure legends and Methods to define sample-size notation consistently throughout the manuscript. As suggested by Reviewer 3, we now distinguish biological replicates or independent experiments (N) from individual embryos, larvae, cells, imaging planes, or trials (n), as appropriate.

Minor comments: - Specific experimental issues that are easily addressable. - Are prior studies referenced appropriately? - Are the text and figures clear and accurate? - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Throughout the manuscript: use the prime symbol for 5/3 DNA/RNA instead of an apostrophe. The prime symbol is present in a small number of sentences, but mostly the apostrophe is used.

We thank the reviewer for noting this. We have replaced apostrophes with prime symbols throughout the manuscript to ensure consistent notation of 5′ and 3′ RNA/DNA termini.

Line 227: "Next, we compared the total number of neurons". The elavl3 driver labels brain cells in addition to neurons. - The authors compared to the total number of brain cells, but can they make any comments on the size of the brain across the various areas? I imagine this data is also accessible by analyzing the imaging already collected.

The elavl3 promoter is widely used as a pan-neuronal driver in zebrafish. Our calcium-imaging experiments used the Tg(elavl3:H2B-GCaMP8s) line, in which nuclear-localised GCaMP8s is expressed under the control of the elavl3 regulatory region. This established configuration enables brain-wide functional imaging of neuronal activity in larval zebrafish.

To assess whether differences in regional brain size might contribute to the observed phenotype, we quantified brain dimensions in 5 dpf larvae using the existing imaging data. Measurements were performed manually in Fiji in a blinded manner, with genotypes assigned only after completion of the analysis. We quantified tectum width, hindbrain width, and tectum length, as illustrated in the new Supplementary Figure 6.

MZrlig1 larvae showed a modest reduction in tectum width (MZrlig1: 299 ± 14 µm; WT: 312 ± 10 µm; one-sided t-test, p = 0.00125) and tectum length (MZrlig1: 122 ± 5 µm; WT: 134 ± 9 µm; one-sided t-test, p = 1.03 × 10⁻⁵). In contrast, hindbrain width did not differ between genotypes (MZrlig1: 164 ± 10 µm; WT: 164 ± 10 µm; one-sided t-test, p = 0.52). Following assessment of data distribution, statistical significance was evaluated using one-sided t-tests with Bonferroni correction for three comparisons (n = 18 MZrlig1 and n = 20 WT larvae).

Importantly, the unchanged hindbrain width indicates that the reduced number of motion-responsive hindbrain neurons in MZrlig1 larvae is unlikely to be explained by a gross difference in hindbrain size. These findings therefore support our interpretation that Rlig1 loss is associated with reduced neuronal responsiveness in the hindbrain.

Given that there is already a mouse mutant for this gene and transcriptomics, can the authors do a more thorough job comparing the transcriptomics from that study with their own?

We thank the reviewer for this helpful suggestion. When we applied the differential-expression thresholds used in our zebrafish analysis (absolute log₂ fold change ≥ 1.5 and adjusted p value ≤ 0.05) to the genes reported in the mouse study, only flg2 met these criteria. Thus, the available mouse dataset provides limited scope for a direct gene-by-gene comparison with our data.

To extend our analysis beyond poly(A)-enriched mRNA sequencing, we additionally performed tRNA and rRNA sequencing using total RNA from 5 dpf WT and MZrlig1 larvae. The tRNA analysis identified 17 significantly altered tRNAs in MZrlig1 larvae, including seven upregulated and ten downregulated species (Figure 5i; Supplementary Tables 8–9). Notably, the affected tRNAs include tRNA-Lys-CTT, which was previously identified among RNAs enriched in human Rlig1 immunoprecipitates, and tRNA-Thr-CGT, which was reported to be increased in female rlig1 knockout mouse brains. Although the direction of change is not fully conserved across these studies, these overlaps further support the possibility that Rlig1 influences tRNA homeostasis.

In parallel, rRNA sequencing revealed differential abundance of 122 5S rRNA transcripts, with 86 upregulated and 36 downregulated in MZrlig1 larvae (Figure 5h; Supplementary Tables 10–11). Together, these new analyses show that loss of Rlig1 is associated with altered abundance of both tRNA and rRNA species, consistent with previous evidence linking Rlig1 to RNA homeostasis. At the same time, we explicitly state that these data do not identify direct enzymatic substrates of Rlig1, but provide a resource and rationale for future mechanistic studies.

A clearer statement on the similarities and differences of Rlig1 and RtcB would be helpful. Is it possible RtcB is compensating at all?

We thank the reviewer for this comment. We have clarified the similarities and differences between Rlig1 and RtcB in the Introduction and Discussion. Although both enzymes catalyse RNA ligation, they act on distinct end chemistries. RtcB mediates 3′–5′ ligation of RNA ends generated during canonical tRNA splicing, joining a 5′-hydroxyl end to a 2′,3′-cyclic phosphate or 3′-phosphate end. In contrast, Rlig1 catalyses 5′–3′ ligation of RNA fragments bearing a 5′-phosphate and a 3′-hydroxyl group.

These distinct substrate requirements make direct functional compensation by RtcB unlikely. RNA ends generated for ligation by Rlig1 would first require end processing to generate termini compatible with RtcB-mediated ligation. Nevertheless, indirect compensation or partial functional overlap after such processing cannot be excluded.

We sought to address this question experimentally by obtaining rtcb mutants from the European Zebrafish Resource Center. However, subsequent genotyping showed that the supplied sperm did not contain the intended rtcb mutant alleles, precluding analysis in the present study. We have therefore explicitly acknowledged that the extent to which RtcB may compensate for loss of Rlig1 remains unresolved and will require analysis of validated rtcb mutant lines in future work.

I examined the DEG tables, and I did not notice an obvious substantial enrichment of genes on chromosome 25 (White et al., 2022, https://doi.org/10.7554/eLife.72825). Were the different samples from different clutches or the same clutch? I may have missed it. Regardless, I would carefully check the DEGs that are important for conclusions and check that they are not on the same chromosome as rlig1. It is likely worth rerunning all of the GO/GSEA with genes on chromosome 25 excluded.

We thank the reviewer for raising this potential confound. The RNA-seq samples were derived from independent clutches. To determine whether the observed transcriptional changes could be influenced by local effects associated with the rlig1 locus on chromosome 25, we performed two complementary analyses.

First, we examined the chromosomal distribution of differentially expressed genes (DEGs) at each developmental stage. The chromosomal distribution was assessed using the original DEG analysis presented in the manuscript (no pre-filtering before DESeq2; DEGs defined as padj 1). Chromosome 25 contains 806 of 25,254 annotated protein-coding genes in the zebrafish genome, corresponding to 3.2% of all coding genes. Across developmental stages, the proportion of DEGs located on chromosome 25 ranged from 1.4% to 4.1% (cleavage: 12/419; sphere: 17/; shield: 37/892; bud: 26/781; 1 dpf: 3/216; 5 dpf: 8/587). Relative to the genomic expectation, this corresponds to enrichment values between 0.43- and 1.30-fold. Only the shield stage showed a modest increase in the proportion of chromosome 25 DEGs (1.30-fold), whereas all other stages were at or below the genomic expectation. Thus, genes on chromosome 25 are not globally overrepresented among the DEGs in the rlig1 mutant dataset.

Second, we repeated the complete differential-expression analysis for each developmental stage after excluding all chromosome 25 genes before DESeq2 normalisation, size-factor estimation, and dispersion modelling. This re-analysis was performed using an updated workflow, including removal of genes with zero total counts prior to DESeq2, which changes the number of genes entering Benjamini–Hochberg correction and consequently the total number of detected DEGs; all other analysis parameters were identical to the original analysis. This approach ensured that chromosome 25 genes could not influence either normalisation or statistical inference for genes on other chromosomes. Using the same DEG thresholds as in the original analysis (padj 1), exclusion of chromosome 25 had only minimal effects on the remaining DEG sets.

Stage

Full DEGs

Non-Chr25 DEGs

Lost (Chr25)

Lost (non-Chr25)

Gained

1 (4-cell)

419

415

5

0

1

2 (Sphere)

913

879

34

5

5

3 (Shield)

592

553

37

5

3

4 (Bud)

349

329

20

0

0

5 (1 dpf)

7

6

1

0

0

6 (5 dpf)

168

164

4

0

0

Across all six developmental stages, only ten non-chromosome-25 genes lost significance and nine genes gained significance. These minor changes were confined largely to the sphere and shield stages, which also showed the highest relative representation of chromosome 25 DEGs. At the 4-cell, bud, 1 dpf, and 5 dpf stages, no non-chromosome-25 genes lost significance after chromosome 25 was excluded.

We also repeated the GO and GSEA analyses after excluding chromosome 25 genes. As expected, a small number of individual terms changed; however, the principal enrichment patterns and overall biological interpretation remained unchanged. Together, these analyses indicate that the transcriptomic phenotype is not substantially driven by chromosome 25-linked DEGs or by local effects associated with the edited rlig1 locus. While this analysis cannot exclude effects on individual linked genes, it shows that such effects do not substantially affect the main transcriptional or pathway-level conclusions of the study.

**Referees cross-commenting**

I missed the point about the RNA-seq samples being cousin-matched. While I am optimistic that the results won't change, I agree with Reviewer #3 that some confirmation is necessary. It was unclear to me whether the samples were from the same or different clutches - if they are from different clutches and share overlapping genes, that would also add support to the results. I think that detail was missing from the methods, and I had pointed it out. Either additional RNA-seq or even qPCR of some top genes from a heterozygous incross is a reasonable request.

We thank the reviewer for raising this point and apologise that the breeding design for the transcriptomic experiments was not described sufficiently clearly. The developmental RNA-seq samples were not cousin-matched. Rather, WT and MZrlig1 embryos were collected from separate group matings and therefore originated from different clutches. Independent pooled samples were analysed at each developmental stage, as now described explicitly in the revised Methods.

We agree that independent validation in a sibling-controlled genetic setting is important. We therefore performed RT-qPCR for eight genes selected from the 5 dpf mRNA-seq dataset using sibling-matched zygotic rlig1 mutants and WT larvae generated by heterozygous incrosses. For each genotype, three independent biological replicates were analysed, with four larvae per sample. Six of the eight selected genes showed changes in the same direction as in the original MZrlig1 RNA-seq dataset: cyp2p9, itln3, sult3st4, fabp7b, hamp, and rlig1 itself. In particular, itln3 remained strongly upregulated, whereas rlig1 expression was markedly reduced in the sibling-matched zygotic mutants. In contrast, gdf3 and gstp1.1 did not show the same directional change in this validation experiment.

These results provide independent support that several of the transcriptional changes identified in the MZrlig1 RNA-seq dataset are also observed in sibling-matched zygotic mutants. At the same time, the incomplete concordance of individual genes is consistent with the fact that maternal-zygotic and zygotic mutants represent biologically distinct conditions and may differ in both effect size and molecular consequences. We have added these validation data as Supplementary Figure 7 and revised the Results and Methods accordingly.

Reviewer #1 (Significance (Required)):

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

This study provides a conceptual and biological advance by identifying a role for a vertebrate RNA ligase in brain development, behavior, and transcriptional regulation.

• Place the work in the context of the existing literature (provide references, where appropriate).

Although RNA ligases from single-cell organisms and phage are well-characterized, the roles of RNA ligases in vertebrates are relatively understudied. There are only two, including the one the one that is the focus of this manuscript. This study demonstrates an in vivo function for Rlig1, linking molecular changes to neural development and function. The Rlig1 enzyme was only very recently discovered (2023), making this work timely and an important addition to an area with relatively few studies.

A major strength of the study is its multi-level approach, integrating diverse techniques to coherently link this gene to organism-level phenotypes. This work provides a strong conceptual and functional advance by demonstrating a role for Rlig1 in vertebrate neural circuit function and behavior. A remaining mechanistic gap is that the direct RNA substrates of Rlig1 are not identified, and the observed transcriptomic changes in mRNA are likely downstream consequences of its loss. However, these points are clearly acknowledged in the discussion, making the study a well-balanced contribution. Given the existence of a mouse knockout model, further discussion comparing the zebrafish transcriptomic results and phenotypes to those observed in mouse would help place this work in the context of prior studies. Overall, the main conclusions are well supported, and the limitations do not undermine them. This study represents an important contribution that establishes a foundation for future mechanistic work linking Rlig1 substrates to the observed phenotypes.

We thank the reviewer for this thoughtful and encouraging assessment.

• State what audience might be interested in and influenced by the reported findings.

Zebrafish basic science researchers, particuarly those studying how genes lead to altered neural circuits and behavior, are the most direct target audience. However, the work is of more broad interest to those in the fields of neurodevelopment, gene regulation, and RNA biology / processing.

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I am comfortable evaluating zebrafish mutants, transcriptomics, and behavioral assay design. I have more limited experiment in neural circuit anaysis and interpretation of calcium imaging data, though this part of the manuscript was also clearly presented and understandable.

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

Summary Klusman et al have investigated the function of the RNA ligase rlig1 in zebrafish. They first document expression of the gene, by quantitative RT-PCR and HCR-fluorescent in situ hybridization. They then test ligase activity of the Rlig1 protein in vitro. They next generate a null mutant and test function of the visual system using behaviour as well as calcium imaging. The data indicate that rlig1 is broadly expressed and capable of ligating RNA; loss of rlig1 has mild effects on overall development and pronounced effects on behavioural and neuronal response to visual stimuli. Finally, the authors use bulk transcriptome analysis to identify changes in gene expression in the mutants.

We thank the reviewer for this accurate summary of our study and for recognising that the behavioural and calcium-imaging results together support a role for rlig1 in visual processing and visually guided behaviour.

**Referees cross-commenting**

I agree that more details are required about the crosses would be useful.

We also agree that further detail on the breeding schemes is important. We have therefore expanded the Methods and figure legends to describe the crosses used for each experiment, including the relationship between mutant and control animals and whether samples were sibling- or cousin-matched.

Reviewer #2 (Significance (Required)):

Overall, the conclusions that rlig1 is required for normal development of the embryo, especially of a fully functioning visual system, are well supported. The optomotor response experiments have high power and, together with functional imaging, show a clear difference between mutant and wildtype.

One limitation of this manuscript is in the characterization of gene expression. The gene expression database in Zfin contains one image of rlig1 (https://zfin.org/ZDB-IMAGE-060710-1925#image), which shows broad expression in cells of the embryo and larvae and no expression in the yolk. The images here, with the exception of the mutant in Figure 3C, show expression in the yolk. This would suggest that the yolk signal is not autofluorescence, which is inconsistent with the Thisses' data. Additonally, Figure S1 indicates a variable level of non-specific signal, especially in panel g. Thus, the distribution of rlig1 mRNA is unclear.

We agree that the yolk-associated signal should not be interpreted as specific rlig1 expression.

rlig1 transcripts are completely absent from the RNA-seq datasets of MZrlig1 mutants at all developmental stages analysed. Thus, the variable fluorescence observed in the yolk and in the no-probe controls (Supplementary Figure 1) cannot represent residual rlig1 expression, but must reflect non-specific background signal and/or autofluorescence. We have clarified this point in the revised manuscript.

The transcriptome analysis identified changes in gene expression in the mutant. This establishes a role for rlig1 in development, and identifies several processes that are disrupted by loss of rlig1. However, the molecular analysis sheds little light on direct targets of the ligase. Given the established effects on tRNA, for example, it is unclear why RNA was analysed only by short reads on poly(A) RNA. The reader is left wondering whether zebrafish tRNA contains introns that require Rlig1 for processing. In this context, it would be useful for the authors to provide more background on tRNA splicing in vertebrates, including a mention of tricRNA, and potentially the role of TSEN complex in brain development.

We have expanded the Introduction as suggested to provide additional context on tRNA splicing in vertebrates. We now explain that canonical tRNA splicing is initiated by the TSEN complex and completed by RtcB, which ligates RNA ends with chemistries distinct from those used by Rlig1. We also discuss that excised tRNA introns can form stable tRNA intronic circular RNAs (tricRNAs), and that defects in TSEN complex components are associated with neurodevelopmental disorders, underscoring the importance of RNA processing for nervous-system development.

We agree that our poly(A)-enriched RNA-seq data do not identify direct RNA substrates of Rlig1. We have clarified throughout the manuscript that these experiments were designed to characterise downstream transcriptional consequences of rlig1 loss.

We have additionally analysed tRNA and rRNA abundance in total RNA from 5 dpf WT and MZrlig1 larvae. These analyses identified altered levels of specific tRNA and 5S rRNA species in MZrlig1 larvae (Figure 5h,i; Supplementary Tables 8–11), supporting an association between Rlig1 loss and altered RNA homeostasis.

To summarize, this manuscript extends work in the mouse and in cell lines that demonstrate a requirement for rlig1. It does not shed light on direct targets of Rlig1, but provides a strong foundation for future work on the role of RNA ligation in vertebrate development and brain function.

This paper is expected to be of interest to a specialised audience.

Minor points: The images showing gene expression in Figure 2 are not easy to see, due to the LUT used and low intensity of the signal. To aid the reader, the HCR channel should be shown in grayscale, possibly with the contrast enhanced (to the same extent in all images).

To improve the visibility and interpretation of the HCR signal, we have added a new Supplementary Figure 2 showing the rlig1 channel in greyscale. Within comparable developmental-stage panels, identical contrast settings were applied to all images.

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

Summary This paper provides good evidence that a newly described enzyme that catalyzes 5'-3' RNA ligation - rlig1 - plays some role in early vertebrate neurodevelopment. Using embryonic and larval zebrafish as a model, they found that, while rlig1 mRNA is highly maternally deposited and ubiquitously expressed early on, expression later in development localizes to the brain and eyes. They generated a stable CRISPR/Cas9 large deletion mutant spanning from upstream the 5'UTR past the start codon. By comparing wild type and maternal-zygotic (MZ) rlig1 mutants, the authors found that animals developed overtly normally but did show reduced behavioral responsiveness to a visual stimulus experimental paradigm. By combining calcium imaging and poly(A)-enriched RNA-sequencing transcriptomic analyses, they found that there was decreased neuronal activity in regions needed for visual processing, and that there was dysregulation of neural-related gene networks and metabolic and translational pathways.

We thank the reviewer for this detailed and accurate summary of our study and for recognising the convergent evidence linking Rlig1 loss to altered neural activity and visually guided behaviour in developing zebrafish.

Major comments 1) My main major comment is that, because there is so much inherent variability in behavior and even development across different clutches, this study relies on comparing (cousin-matched) WT and maternal-zygotic rlig1 mutant animals. In most reliable peer-reviewed papers, this is not a fair comparison. While I appreciate that authors stated that they used parents that were siblings (so, offspring would be cousin-matched), I do not consider this scientifically rigorous enough for the claims presented. a. I do not consider it a reasonable request to ignore the massive amount of work that went into this paper using WT and MZrlig1 comparisons. However, at minimum, authors should consider performing essential behavior and RNA-seq (see point b) experiments with heterozygous incrosses of single-pair matings, and genotyping the animals post-hoc. Including this critical data in a main figure, as the basis for using MZ animals for the rest of the paper, would induce some confidence that the phenotypes and claims presented are not a result of inherent variability. If the authors already have adult heterozygous animals of mating age, I estimate that these experiments may be completed very reasonably within 3-4 weeks; if new animals need to be generated, this request would take ~4 months. Typically, these kinds of experiments would not be considered a financial burden to perform.

Our central genetic condition was maternal-zygotic loss of rlig1, motivated by the strong maternal deposition of rlig1 mRNA during cleavage stages. A heterozygous incross would produce zygotic mutants that still receive maternal rlig1 transcript and protein, and would therefore test a related but biologically distinct condition. For the maternal–zygotic experiments, we used cousin-matched WT controls derived from the same parental family to minimise genetic-background differences, and we performed the behavioural assays with substantial numbers of larvae across independent experiments.

We nevertheless repeated the behavioural analysis as suggested using zygotic rlig1 mutants and WT sibling controls obtained from heterozygous incrosses. This analysis revealed a qualitatively similar, although less pronounced, reduction in visually guided behaviour in zygotic mutants (new Supplementary Figure 4). We speculate that the reduced effect size is consistent with partial compensation by maternally supplied rlig1 transcript or protein in zygotic mutants.

b. For transcriptomic analyses, I have two main points: i) again, it is difficult to statistically rigorously compare transcriptomes of nonsibling-matched animals with such low numbers of single 5 dpf brains. In line with point a, it would be essential to pool at least a few WT and rlig1 mutant siblings for at least 3 biological replicates per samples and compare those analyses with the results from MZ animals. ii) Typically this would not be a major concern, however given the nature of the gene of interest and published in vitro findings, I do consider that the rlig1 enzyme catalyzes 5'-3' RNA ligation, has been shown to be implicated in rRNA integrity and tRNA targeting, and is broadly essential for repair, splicing, and editing of RNAs. Thus, while the poly(A)-enriched RNA sequencing can provide context about gene networks that are affected (either primarily or secondarily), sequencing that enriches for tRNAs, polysome profiling or ribosome profiling, or some more targeted sequencing approach would be more appropriate to more rigorously support the claims in the paper. Depending on readiness of mating-age animals, this experiment and analyses may reasonably take up to 3 months; this approach may be considered a financial burden. Alternatively, with the current mRNA sequencing, the authors could delve into whether they can identify altered splicing or RNA editing dynamics in different RNA modules. I estimate that this alternative analysis approach may take up to one month to develop and interpret.

We would like to clarify that the poly(A)-enriched RNA-seq was not performed on single 5 dpf brains, but on independent pools of 8–10 age- and genotype-matched whole embryos or larvae collected across six developmental stages. We have also validated eight selected 5 dpf RNA-seq candidates by RT-qPCR using sibling-matched zygotic rlig1 mutants and WT larvae generated by heterozygous incrosses. For each genotype, we analysed three independent biological replicates, each comprising a pool of four larvae. Six of the eight tested genes showed changes in the same direction as in the original MZrlig1 RNA-seq dataset, including cyp2p9, itln3, fabp7b, hamp, sult3st4, and rlig1 (new Supplementary Figure 7). Although zygotic mutants are not equivalent to maternal–zygotic mutants because they retain maternally supplied rlig1 transcript and protein, these results provide independent support for a substantial subset of the transcriptional changes identified in the MZrlig1 dataset. We have revised the Methods, Results, and Discussion to describe the breeding schemes and this limitation more explicitly.

We also agree that poly(A)-enriched RNA-seq alone cannot identify direct Rlig1 substrates or adequately assess non-polyadenylated RNA classes. We therefore added targeted analyses of tRNA and rRNA abundance from total RNA isolated from 5 dpf WT and MZrlig1 larvae. The tRNA analysis identified seven tRNAs with increased and ten with decreased abundance in MZrlig1 larvae, including tRNA-Lys-CTT, previously found among RNAs enriched in human Rlig1 immunoprecipitates, and tRNA-Thr-CGT, which was reported to be increased in female rlig1 knockout mouse brains (Figure 5i; Supplementary Tables 8–9). In parallel, the rRNA analysis identified altered abundance of 122 5S rRNA species, with 86 increased and 36 decreased in MZrlig1 larvae (Figure 5h; Supplementary Tables 10–11).

These new data provide additional evidence that loss of Rlig1 is associated with altered tRNA and rRNA homeostasis. At the same time, we explicitly state that neither the mRNA-, tRNA-, nor rRNA-seq datasets establish direct enzymatic substrates of Rlig1 or demonstrate altered tRNA splicing, RNA editing, or translation. Direct substrate mapping and analyses such as ribosome profiling will be important directions for future work. The revised manuscript frames the transcriptomic analyses accordingly.

o The experiments as documented are adequately replicated and statistical analyses adequate (minus the nonsibling-matched point 1). I note that labels should more clearly state or denote individual (n) or experimental (N) numbers, some of which I provide in Minor comments below.

We agree and have revised the figure legends accordingly. We now distinguish N for independent experiments or biological replicates from n for individual embryos, larvae, imaging planes, segmented cells or trials. Where pooled samples were used, the legends and Methods now state the number of embryos or larvae per pool and the number of independent pools or experiments.

Minor comments Comments on figures or figure legends: 1) Figure 1e, align the "#" labels better, they look diagonal.

Thank you. We corrected the alignment of the labels in Figure 1e.

2) For 1f, consider labeling independent replicates directly on the graph instead of just the label, otherwise not very clear to the reader.

We have revised Figure 1f to make the independent replicates more transparent. The figure now clearly indicates the number of independent replicates used for quantification. Every replicate has a different colour now, and N = 3 is indicated in the figure.

3) Figure 2a, consider adding the reference gene (eef1a) in the legend.

We have added eef1a to the Figure 2a legend and clarified that relative rlig1 mRNA levels were calculated using eef1a as the reference gene.

4) Figure 2a - if I understand the experiment correctly, the current label n=3 (which would mean 3 individual embryos/larvae) should read N=3 (three independent experiments of x number of embryos/larvae per run)

Thank you very much for this suggestion. We have corrected the sample-size notation in Figure 2a. The label now uses N for independent experiments and specifies the number of embryos or larvae used per experiment where appropriate.

5) Supplementary Figure 1 was very unconvincing comparing WT to MZ mutants, I'm sorry to say I really could not tell much difference. When compared to Figure 3c, they look quite different. The DRAQ7 labeling also appeared uneven in Supplementary Figure 1. Consider optimizing the imaging strategy and providing more interpretably images. A separate, aesthetic comment - magenta was very difficult for me to see against a black background, consider switching the rlig1 channel to grayscale or flip the colors so that rlig1 mRNA is cyan, for example.

We thank the reviewer for this comment and apologise that the purpose of Supplementary Figure 1 was not sufficiently clear. This figure shows no-probe control samples imaged in the rlig1 detection channel to document stage-dependent background and autofluorescence. Because no rlig1 probe was applied, no genotype-dependent difference between WT and MZrlig1 samples is expected in these images. The variable signal, including the yolk-associated fluorescence, therefore represents background rather than specific rlig1 mRNA detection.

In contrast, Figure 3c shows samples processed with the rlig1 HCR probe set. The marked reduction of punctate signal in MZrlig1 larvae in this experiment is therefore attributable to the absence of rlig1 transcripts, consistent with the RNA-seq and RT-qPCR data. We have clarified this distinction in the revised text and figure legends.

The apparently uneven DRAQ7 signal in some no-probe control images reflects differences in embryo orientation and imaging planes rather than genotype-specific staining differences. To improve the visibility and interpretability of the HCR data, we have additionally included a new Supplementary Figure 2 showing the rlig1 channel in greyscale, with matched contrast settings within comparable developmental-stage panels.

6) Calcium imaging - related to Major comments above, consider performing this experiment in sibling-matched animals, especially with only one copy of the transgene. If WT vs. sibling mutant results look similar to the WT vs MZ mutant results, this would be more convincing.

We agree that calcium imaging in sibling-matched zygotic mutants would provide a valuable complementary dataset. However, zygotic mutants retain maternally supplied rlig1 transcript and protein and therefore represent a biologically distinct condition from the maternal–zygotic mutants examined in our principal imaging experiments. Consistent with this distinction, the behavioural phenotype in sibling-matched zygotic mutants was qualitatively similar but less pronounced than in maternal–zygotic mutants.

A sufficiently powered brain-wide calcium-imaging analysis in sibling-matched animals would require generation, imaging, and analysis of a substantial additional cohort, while the expected smaller effect size would limit its ability to directly test the maternal–zygotic phenotype reported here. We therefore believe that this experiment extends beyond the scope of the present study.

**Referees cross-commenting**

I agree with Reviewer #1 that at least the raw code is uploaded to GitHub or Zenodo, and raw data to be uploaded to Zenodo.

We agree and thank the reviewer for this important suggestion. To ensure that the study can be reproduced without the need to contact the authors, we have made the underlying data and custom analysis code publicly accessible. The RNA-seq data have been deposited in the GEO repository under accession number GSE308510 and are available at https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE308510.

In addition, the raw imaging data, behavioural and calcium-imaging datasets, processed data, and custom scripts used for the behavioural, calcium-imaging, as well as the tRNA and rRNA sequencing data have been deposited on KonDATA (DOI: 10.48606/vpwgm69277srrgaj) – together more than 190 GB – and can be accessed using this link: https://kondata.uni-konstanz.de/radar/en/dataset/vpwgm69277srrgaj?token=gLEaYEENHjmHBhjhHUHK.

We have revised the Data and code availability statement in the manuscript accordingly (also see the response to Reviewer #1).

I agree with Reviewer #1 that brain size can and should also be assessed, presumably using the same images already collected. For example, in Figure 5b, number of neural cells (even when normalized) could be lower if brain size is small. Reasonable control analysis.

As suggested, we have quantified tectum width, tectum length, and hindbrain width from the existing calcium-imaging datasets in a blinded manner. Although MZrlig1 larvae showed modest reductions in tectum width and length, hindbrain width did not differ between genotypes. Thus, the reduced number of motion-responsive hindbrain cells is unlikely to be explained by a gross difference in hindbrain size. These control analyses are presented in the new Supplementary Figure 6 (also see the response to Reviewer #1).

I agree with Reviewer #2 that addressing, either by writing or experimentally, a bit more about direct targets of the ligase (including tRNAs and rRNAs) will strengthen the manuscript significantly.

We thank the reviewer for this helpful suggestion. To address this point, we have added new analyses of rRNA and tRNA abundance in 5 dpf WT and MZrlig1 larvae, together with an expanded discussion of their interpretation. These data provide additional evidence that loss of Rlig1 is associated with altered RNA homeostasis, while we distinguish such effects from the direct RNA substrates of the ligase, which remain to be identified (also see the response to Reviewer #2).

I agree with Reviewer #1 first comment (last sentence) that, if RNA-seq (or other appropriate sequencing) of sibling-matched samples is financially prohibitive, then at least qPCR of some top genes would be acceptable.

We have performed RT-qPCR validation of selected top differentially expressed genes using sibling-matched WT and zygotic rlig1 mutant larvae generated by heterozygous incrosses. These data provide independent support for the altered expression of several genes identified in the maternal–zygotic rlig1 RNA-seq dataset and are presented in new Supplementary Figure 9 (also see the response to Reviewer #1).

I agree with the additional comment from Reviewer #1 - the manuscript details cousin-matched samples in lines 666-667, but I'd like to add a suggestion that the authors include details about "single-pair" versus "group-mating". For behavior and all analyses in these kinds of zebrafish experiments, it is very important that multiple replicates of single-pair (one female crossed to one male), sibling-matched groups are used.

We appreciate the reviewer’s helpful suggestion. We agree that further detail on the breeding schemes is important. We have therefore expanded the Methods to specify, for each experiment, whether embryos or larvae were obtained from single-pair or group matings, the number of independent crosses or clutches, and whether mutant and control animals were sibling- or cousin-matched.

Reviewer #3 (Significance (Required)):

This study provides a good increase in our knowledge about a newly described RNA ligase enzyme - rlig1 - in vivo. The authors integrate their results across organismal behavior, brain cell activity, and transcriptomes using a newly generated stable genetic mutant to uncover a new link between neuronal RNA processing, development, and sensory-motor computation. Given that the human orthologue of this gene has been associated with neurological and cognitive conditions, including neurodevelopmental and neuroinflammatory disorders and Alzheimer's disease, the generation and characterization of this stable mutant line proves valuable. There are important technical limitations, specifically related to the comparison of wild type and maternal-zygotic mutant animals, that may not faithfully represent statistical differences compared to sibling-matched animals. Basic biological audiences, including in neurodevelopment, genetics, and RNA biology, would be interested in this research.

We thank the reviewer for recognising the value of the stable rlig1 mutant line and for highlighting the importance of the breeding design. We agree that comparisons between cousin-matched WT and maternal–zygotic (MZ) mutant larvae require careful interpretation. However, a fully sibling-matched WT versus MZrlig1 comparison is not genetically possible. Maternal–zygotic mutants must be produced by homozygous mutant mothers, whereas WT siblings can only be obtained from a different maternal genotype. Thus, the maternal genotype and, critically, the presence or absence of maternally deposited rlig1 RNA and protein – necessarily differs between these conditions. This is not merely a technical limitation of the experimental design, but an intrinsic feature of testing maternal–zygotic gene function. A heterozygous incross instead produces sibling-matched zygotic mutants, which retain maternal rlig1 products and therefore represent a biologically distinct genetic condition rather than a direct replacement for the MZ comparison.

For the MZ experiments, we minimised genetic-background differences by using cousin-matched controls derived from the same parental family and by analysing independent experimental replicates. Importantly, the principal behavioural finding was independently supported in sibling-matched zygotic mutants generated by heterozygous incrosses. These larvae showed a qualitatively similar reduction in visually guided behaviour, although with a smaller effect size (new Supplementary Figure 4). We also validated selected transcriptional changes in sibling-matched zygotic mutants by RT-qPCR (new Supplementary Figure 9). The weaker phenotype in zygotic mutants is consistent with partial buffering by maternal rlig1 transcript or protein. Future studies will be valuable to further separate how maternal and zygotic Rlig1 affects gene expression and visually guided behaviour.

Insufficient expertise to evaluate: While I understand the first part of Figure 1, I do not have expertise in these sorts of assays. The rest of the experiments I do have sufficient expertise to evaluate. And thank you to the authors for providing direct DOI links to references.

We are grateful for the reviewers’ detailed comments, which substantially improved the manuscript. We hope that the revised text and additional analyses address the central concerns and make the study more transparent and useful to the field.

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Referee #3

Evidence, reproducibility and clarity

Summary

This paper provides good evidence that a newly described enzyme that catalyzes 5'-3' RNA ligation - rlig1 - plays some role in early vertebrate neurodevelopment. Using embryonic and larval zebrafish as a model, they found that, while rlig1 mRNA is highly maternally deposited and ubiquitously expressed early on, expression later in development localizes to the brain and eyes. They generated a stable CRISPR/Cas9 large deletion mutant spanning from upstream the 5'UTR past the start codon. By comparing wild type and maternal-zygotic (MZ) rlig1 mutants, the authors found that animals developed overtly normally but did show reduced behavioral responsiveness to a visual stimulus experimental paradigm. By combining calcium imaging and poly(A)-enriched RNA-sequencing transcriptomic analyses, they found that there was decreased neuronal activity in regions needed for visual processing, and that there was dysregulation of neural-related gene networks and metabolic and translational pathways.

Major comments

1) My main major comment is that, because there is so much inherent variability in behavior and even development across different clutches, this study relies on comparing (cousin-matched) WT and maternal-zygotic rlig1 mutant animals. In most reliable peer-reviewed papers, this is not a fair comparison. While I appreciate that authors stated that they used parents that were siblings (so, offspring would be cousin-matched), I do not consider this scientifically rigorous enough for the claims presented.

a. I do not consider it a reasonable request to ignore the massive amount of work that went into this paper using WT and MZrlig1 comparisons. However, at minimum, authors should consider performing essential behavior and RNA-seq (see point b) experiments with heterozygous incrosses of single-pair matings, and genotyping the animals post-hoc. Including this critical data in a main figure, as the basis for using MZ animals for the rest of the paper, would induce some confidence that the phenotypes and claims presented are not a result of inherent variability. If the authors already have adult heterozygous animals of mating age, I estimate that these experiments may be completed very reasonably within 3-4 weeks; if new animals need to be generated, this request would take ~4 months. Typically, these kinds of experiments would not be considered a financial burden to perform.

b. For transcriptomic analyses, I have two main points: i) again, it is difficult to statistically rigorously compare transcriptomes of nonsibling-matched animals with such low numbers of single 5 dpf brains. In line with point a, it would be essential to pool at least a few WT and rlig1 mutant siblings for at least 3 biological replicates per samples and compare those analyses with the results from MZ animals. ii) Typically this would not be a major concern, however given the nature of the gene of interest and published in vitro findings, I do consider that the rlig1 enzyme catalyzes 5'-3' RNA ligation, has been shown to be implicated in rRNA integrity and tRNA targeting, and is broadly essential for repair, splicing, and editing of RNAs. Thus, while the poly(A)-enriched RNA sequencing can provide context about gene networks that are affected (either primarily or secondarily), sequencing that enriches for tRNAs, polysome profiling or ribosome profiling, or some more targeted sequencing approach would be more appropriate to more rigorously support the claims in the paper. Depending on readiness of mating-age animals, this experiment and analyses may reasonably take up to 3 months; this approach may be considered a financial burden. Alternatively, with the current mRNA sequencing, the authors could delve into whether they can identify altered splicing or RNA editing dynamics in different RNA modules. I estimate that this alternative analysis approach may take up to one month to develop and interpret.

The experiments as documented are adequately replicated and statistical analyses adequate (minus the nonsibling-matched point 1). I note that labels should more clearly state or denote individual (n) or experimental (N) numbers, some of which I provide in Minor comments below.

Minor comments

Comments on figures or figure legends:

1. Figure 1e, align the "#" labels better, they look diagonal.
2. For 1f, consider labeling independent replicates directly on the graph instead of just the label, otherwise not very clear to the reader.
3. Figure 2a, consider adding the reference gene (eef1a) in the legend.
4. Figure 2a - if I understand the experiment correctly, the current label n=3 (which would mean 3 individual embryos/larvae) should read N=3 (three independent experiments of x number of embryos/larvae per run)
5. Supplementary Figure 1 was very unconvincing comparing WT to MZ mutants, I'm sorry to say I really could not tell much difference. When compared to Figure 3c, they look quite different. The DRAQ7 labeling also appeared uneven in Supplementary Figure 1. Consider optimizing the imaging strategy and providing more interpretably images. A separate, aesthetic comment - magenta was very difficult for me to see against a black background, consider switching the rlig1 channel to grayscale or flip the colors so that rlig1 mRNA is cyan, for example.
6. Calcium imaging - related to Major comments above, consider performing this experiment in sibling-matched animals, especially with only one copy of the transgene. If WT vs. sibling mutant results look similar to the WT vs MZ mutant results, this would be more convincing.

Referees cross-commenting

I agree with Reviewer #1 that at least the raw code is uploaded to GitHub or Zenodo, and raw data to be uploaded to Zenodo.

I agree with Reviewer #1 that brain size can and should also be assessed, presumably using the same images already collected. For example, in Figure 5b, number of neural cells (even when normalized) could be lower if brain size is small. Reasonable control analysis.

I agree with Reviewer #2 that addressing, either by writing or experimentally, a bit more about direct targets of the ligase (including tRNAs and rRNAs) will strengthen the manuscript significantly.

I agree with Reviewer #1 first comment (last sentence) that, if RNA-seq (or other appropriate sequencing) of sibling-matched samples is financially prohibitive, then at least qPCR of some top genes would be acceptable.

I agree with the additional comment from Reviewer #1 - the manuscript details cousin-matched samples in lines 666-667, but I'd like to add a suggestion that the authors include details about "single-pair" versus "group-mating". For behavior and all analyses in these kinds of zebrafish experiments, it is very important that multiple replicates of single-pair (one female crossed to one male), sibling-matched groups are used.

Significance

This study provides a good increase in our knowledge about a newly described RNA ligase enzyme - rlig1 - in vivo. The authors integrate their results across organismal behavior, brain cell activity, and transcriptomes using a newly generated stable genetic mutant to uncover a new link between neuronal RNA processing, development, and sensory-motor computation. Given that the human orthologue of this gene has been associated with neurological and cognitive conditions, including neurodevelopmental and neuroinflammatory disorders and Alzheimer's disease, the generation and characterization of this stable mutant line proves valuable. There are important technical limitations, specifically related to the comparison of wild type and maternal-zygotic mutant animals, that may not faithfully represent statistical differences compared to sibling-matched animals. Basic biological audiences, including in neurodevelopment, genetics, and RNA biology, would be interested in this research.

Insufficient expertise to evaluate: While I understand the first part of Figure 1, I do not have expertise in these sorts of assays. The rest of the experiments I do have sufficient expertise to evaluate. And thank you to the authors for providing direct DOI links to references.

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Referee #2

Evidence, reproducibility and clarity

Summary

Klusman et al have investigated the function of the RNA ligase rlig1 in zebrafish. They first document expression of the gene, by quantitative RT-PCR and HCR-fluorescent in situ hybridization. They then test ligase activity of the Rlig1 protein in vitro. They next generate a null mutant and test function of the visual system using behaviour as well as calcium imaging. The data indicate that rlig1 is broadly expressed and capable of ligating RNA; loss of rlig1 has mild effects on overall development and pronounced effects on behavioural and neuronal response to visual stimuli. Finally, the authors use bulk transcriptome analysis to identify changes in gene expression in the mutants.

Referees cross-commenting

I agree that more details are required about the crosses would be useful.

Significance

Overall, the conclusions that rlig1 is required for normal development of the embryo, especially of a fully functioning visual system, are well supported. The optomotor response experiments have high power and, together with functional imaging, show a clear difference between mutant and wildtype.

One limitation of this manuscript is in the characterization of gene expression. The gene expression database in Zfin contains one image of rlig1 (https://zfin.org/ZDB-IMAGE-060710-1925#image), which shows broad expression in cells of the embryo and larvae and no expression in the yolk. The images here, with the exception of the mutant in Figure 3C, show expression in the yolk. This would suggest that the yolk signal is not autofluorescence, which is inconsistent with the Thisses' data. Additonally, Figure S1 indicates a variable level of non-specific signal, especially in panel g. Thus, the distribution of rlig1 mRNA is unclear.

The transcriptome analysis identified changes in gene expression in the mutant. This establishes a role for rlig1 in development, and identifies several processes that are disrupted by loss of rlig1. However, the molecular analysis sheds little light on direct targets of the ligase. Given the established effects on tRNA, for example, it is unclear why RNA was analysed only by short reads on poly(A) RNA. The reader is left wondering whether zebrafish tRNA contains introns that require Rlig1 for processing. In this context, it would be useful for the authors to provide more background on tRNA splicing in vertebrates, including a mention of tricRNA, and potentially the role of TSEN complex in brain development.

To summarize, this manuscript extends work in the mouse and in cell lines that demonstrate a requirement for rlig1. It does not shed light on direct targets of Rlig1, but provides a strong foundation for future work on the role of RNA ligation in vertebrate development and brain function.

This paper is expected to be of interest to a specialised audience.

Minor points:

The images showing gene expression in Figure 2 are not easy to see, due to the LUT used and low intensity of the signal. To aid the reader, the HCR channel should be shown in grayscale, possibly with the contrast enhanced (to the same extent in all images).

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Referee #1

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

This study characterizes the function of RNA ligase 1 (Rlig1) in the vertebrate model zebrafish. Rlig1 is one of only two known RNA ligases in vertebrates, and its biological roles remain poorly understood. The authors combine gene expression analysis, loss-of-function approaches, transcriptomic profiling, calcium imaging, and behavioral assays to investigate its function during development. They show that loss of rlig1 (including maternal-zygotic loss) has no major effects on development or morphology, but that it leads to impairments in visually-guided behavior and altered neuronal activity in response to visual stimuli. Transcriptomic analyses reveal widespread dysregulation across multiple developmental stages, nominating genes that may underly the observed neural phenotypes. Together, the findings support a role for Rlig1 in neural development and function in vertebrates.

Major comments:

• Are the key conclusions convincing?

The key conclusion of this study is that Rlig1 plays an important role in the development and function of vertebrate neural circuits. Overall, this overarching conclusion, as well as the individual conclusions from each set of experiments, are well supported by the data presented. The combination of tissue-specific expression of rlig1, robust behavioral phenotypes in mutants, transcriptomic changes across multiple developmental stages, and circuit differences observed through calcium imaging provides a coherent, multi-faceted argument for the importance of this enzyme in brain development and function. While the precise RNA substrates of Rlig1 and the mechanistic link between transcriptomic changes and neural phenotypes remain to be defined, the authors clearly acknowledge these next steps and limitations. This study is a critical foundation for those future experiments. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

The claims in the manuscript are generally well-supported. The authors clearly acknowledge limitations and future experiments to further dissect mechanism in the Discussion section. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

No major additional experiments appear essential for supporting the current claims. - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

No experiments are required for the current claims of the manuscript. - Are the data and the methods presented in such a way that they can be reproduced?

The methods are generally well described. I would suggest that the "raw images, data, and source code for custom scripts used in this work" be made accessible without having to request from the authors. Zenodo provides up to 50 GB of storage, which is likely sufficient for the data presented in this manuscript. In particular, I think it is important to share the behavior analysis, calcium imaging pipeline, and transcriptomics analysis. Even if all the data is too large, a sample dataset and analysis scripts should be publicly available. - Are the experiments adequately replicated and statistical analysis adequate?

The experiments appear adequately replicated, and statistical analyses are appropriate for the types of data presented.

Minor comments:

• Specific experimental issues that are easily addressable.
• Are prior studies referenced appropriately?
• Are the text and figures clear and accurate?
• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
• Throughout the manuscript: use the prime symbol for 5/3 DNA/RNA instead of an apostrophe. The prime symbol is present in a small number of sentences, but mostly the apostrophe is used.
• Line 227: "Next, we compared the total number of neurons". The elavl3 driver labels brain cells in addition to neurons.
• The authors compared to the total number of brain cells, but can they make any comments on the size of the brain across the various areas? I imagine this data is also accessible by analyzing the imaging already collected.
• Given that there is already a mouse mutant for this gene and transcriptomics, can the authors do a more thorough job comparing the transcriptomics from that study with their own?
• A clearer statement on the similarities and differences of Rlig1 and RtcB would be helpful. Is it possible RtcB is compensating at all?
• I examined the DEG tables, and I did not notice an obvious substantial enrichment of genes on chromosome 25 (White et al., 2022, https://doi.org/10.7554/eLife.72825). Were the different samples from different clutches or the same clutch? I may have missed it. Regardless, I would carefully check the DEGs that are important for conclusions and check that they are not on the same chromosome as rlig1. It is likely worth rerunning all of the GO/GSEA with genes on chromosome 25 excluded.

Referees cross-commenting

I missed the point about the RNA-seq samples being cousin-matched. While I am optimistic that the results won't change, I agree with Reviewer #3 that some confirmation is necessary. It was unclear to me whether the samples were from the same or different clutches - if they are from different clutches and share overlapping genes, that would also add support to the results. I think that detail was missing from the methods, and I had pointed it out. Either additional RNA-seq or even qPCR of some top genes from a heterozygous incross is a reasonable request.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

This study provides a conceptual and biological advance by identifying a role for a vertebrate RNA ligase in brain development, behavior, and transcriptional regulation. - Place the work in the context of the existing literature (provide references, where appropriate).

Although RNA ligases from single-cell organisms and phage are well-characterized, the roles of RNA ligases in vertebrates are relatively understudied. There are only two, including the one the one that is the focus of this manuscript. This study demonstrates an in vivo function for Rlig1, linking molecular changes to neural development and function. The Rlig1 enzyme was only very recently discovered (2023), making this work timely and an important addition to an area with relatively few studies.

A major strength of the study is its multi-level approach, integrating diverse techniques to coherently link this gene to organism-level phenotypes. This work provides a strong conceptual and functional advance by demonstrating a role for Rlig1 in vertebrate neural circuit function and behavior. A remaining mechanistic gap is that the direct RNA substrates of Rlig1 are not identified, and the observed transcriptomic changes in mRNA are likely downstream consequences of its loss. However, these points are clearly acknowledged in the discussion, making the study a well-balanced contribution. Given the existence of a mouse knockout model, further discussion comparing the zebrafish transcriptomic results and phenotypes to those observed in mouse would help place this work in the context of prior studies. Overall, the main conclusions are well supported, and the limitations do not undermine them. This study represents an important contribution that establishes a foundation for future mechanistic work linking Rlig1 substrates to the observed phenotypes. - State what audience might be interested in and influenced by the reported findings.

Zebrafish basic science researchers, particuarly those studying how genes lead to altered neural circuits and behavior, are the most direct target audience. However, the work is of more broad interest to those in the fields of neurodevelopment, gene regulation, and RNA biology / processing. - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I am comfortable evaluating zebrafish mutants, transcriptomics, and behavioral assay design. I have more limited experiment in neural circuit anaysis and interpretation of calcium imaging data, though this part of the manuscript was also clearly presented and understandable.

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Reply to the reviewers

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

This study from the Niedergang lab establishes SNAT7 as a host-dependency factor in human macrophages that supports HIV-1 replication. They show a modest increase in SNAT7 levels HIV-1 infected macrophages and suggest that SNAT7 levels are transiently increased. Employing siRNA against SNAT7 they show reduction in HIV-1 protein levels and viral RNAs and claim that there is a block of reverse transcription in SNAT7 KD cells. Focusing on a known HIV-1 restriction factor in macrophages, SAMHD1, they interconnect the SNAT7 depletion with a reduction in phosphorylated, i.e. catalytical inactive SAMHD1 arguing that SNAT7 regulates the phosphorylation and thereby antiviral activity of SAMHD1. Since SNAT7 is a glutamine transporter that provides this AA from lysosomes, they lastly supplement glutamine and this somehow rescues the reduction of HIV-1 production in SNAT7 KD cells.

Major comments:

The strength of this manuscript is the clear focus on primary human macrophages that are HIV-1 infected and the interconnection of HIV-1 replication to the SNAT7 siRNA KD experiments in combination with SAMHD1 depletion and lastly glutamine supplementation. This establishes a stringent and coherent story line. The effects reported are modest; high variability is not a problem since using primary hMDM this is expected and can be addressed by testing several donors and applying stringent statistics.

1. Having said so, I realize that while they give information on the statistical test used, i.e. one-way ANOVA they miss to explain the post-test used to assess significance (i.e. Bonferroni, Fishers LSD, whatsoever). Please add this information.

We thank the reviewer for this comment. The figure legends have been updated to include more details of all the statistical tests used.

1. Another issue that might underestimate the effects of HIV-1 infection on SNAT7 levels and vice versa of SNAT7 KD on HIV-1 replication is the non-single cell approach employed, i.e. WBlots. I assume that HIV-1 infection rates in macrophages are not super high, usually not exceeding 20-30%. So indeed the effects the authors observe could be much higher, when checking at the single cell level. I do not know about the SNAT7 ab, but all the other reagents should work via flow cytometry and could hence improve the readout a lot.

We agree with the reviewer and indeed, in previous studies on HIV-1 infection of human macrophages performed in the lab, we observed via immunofluorescence that the proportion of infected cells ranged from 20 to 40 %. At the time of submission, we did not have the possibility to label the native SNAT7 protein by immunofluorescence, as the commercial antibody used only works for western blotting.

In the meantime, we have been validating a new antibody (Proteintech) targeting SNAT7 for immunofluorescence. If this is confirmed, we will be able to detect and quantify HIV-1 p24 by immunofluorescence in SNAT7-depleted human macrophages and control cells, thus confirming our results in single-cell analysis.

Flow cytometry analyses are difficult to perform on primary human macrophages because these cells are highly adherent and must be detached first. The process induces significant cell death and damage. This is why we would prefer to carry out these analyses using immunofluorescence and microscopy on adhered cells. This option will be undoubtedly pursued.

1. Furthermore the authors never commented about a dose-response effect in terms of HIV-1 infection levels. There is a MOI dependency described for Suppl.Fig.1 C-F, unfortunately the data is missing in the manuscript.

We apologize for this omission. The figures showing the increase in SNAT7 protein expression following HIV-1 infection at MOIs ranging from 0.05 to 0.5 were added to the new version of the manuscript (Supp. Fig. 1 C-F).

1. Figure1: specify circulating T lymphocytes. I would expect to see levels of SNAT7 in PHA or CD3/CD28 activated lymphocytes versus resting T cells and a time course of SNAT7 levels upon activation. I think even though SNAT7 levels in T cells might be low, they could also be increased by HIV-1 infection and it is essential that the authors test for this. If not, the result is a valid negative control. For this they should employ HIV-1 primary strains with a tropism for T cells, or at least lab-adapted HIV-1 NL4-3

We thank the reviewer for this comment. Circulating T lymphocytes isolated from the blood of healthy donors are now referred to resting lymphocytes in the new version of the manuscript, as opposed to activated T lymphocytes stimulated with IL2 and PHA-P for several days (Fig. 1 A-C).

The expression levels of SNAT7, both at the gene and protein levels, are lower in resting or IL2/PHA-P-activated T cells than in macrophages from the same donors. As suggested, we will perform a kinetic of T-cell activation upon HIV-1 infection to investigate how SNAT7 expression varies in these conditions.

1. Figure 2 again single cell measurements could reveal much more pronounced effects; it is a bit counterintuitive that siRNA #2 is more efficient in SNAT7 KD but has higher levels of HIV-1 replication in terms of Gag levels. I assume when looking at the stats it is always a comparison to the Ctl treated cells (C-G), but this is not entirely clear. Unify labeling as compared to the stats in Fig.2 I (this also applies for all the other figs).

We thank the reviewer for this comment. Fig. 2B indeed shows one of the different donors analyzed. However, protein quantification across six different donors shows that SNAT7 is more depleted with siRNA #2 (Fig. 2C), and that Gag Pr55 protein levels are consequently more reduced, than with siRNA #1 (Fig. 2D).

We use GraphPad Prism software to perform statistical analysis. Depending on the test used, the software automatically plots the comparison bar and displays the p-value above it. We changed the representation of statistics as suggested.

Figure 3: It is a bit odd that they finally conclude on RT as essential step that is reduced in the absence of SNAT7 and then they fail to provide statistical significance for this (Fig.3 panels F and G). One would expect that RT is much more affected given the huge effects on HIV-1 capsid and particle production shown in Fig.2 F, G and I.

The reviewer is right in pointing that we observed a stronger effect during the later stages of the viral cycle, from transcription of viral RNAs (Fig. 2I and Supp. Fig. 2G) to the production of viral particles in the supernatant (Fig. 2D-G), than during the earlier stage of reverse transcription (Fig. 3F, G). Also, it is also possible that we might have missed the peak in ERT/LRT production, which is transient.

It should be noted that SAMHD1 exhibits both dNTPase (Goldstone et al., 2011) and nuclease (Beloglazova et al., 2013) activities. The ability of SAMHD1 to restrict the virus, through dephosphorylation at T592, is mediated by its RNase activity (Ryoo et al., 2014), and not by the dNTPase activity (Welbourn et al., 2013; White et al., 2013).This could explain why SNAT7 exhibit a stronger impact on viral transcription than on reverse transcription.

Figure 4; again single cell flow measurements of SAMHD1, pSAMHD1 and p24 /SNAT7 might help to more clearly discriminate effects that are specifically induced upon infection or happen in virally infected cells. Maybe alternatively IF?

We thank the reviewer for this suggestion. As mentioned under comment #2, flow cytometry analyses are difficult to perform on strongly adherent primary human macrophages.

With regard to immunofluorescence, there is a technical limitation based on the species in which the antibodies are produced. The antibody that targets the native SNAT7 protein, which is currently being validated in our laboratory, is produced in rabbits. An anti-CAp24 antibody produced in goats can be used. It will then be necessary to co-label the cells with anti SAMHD1 and phospho-SAMHD1produced in mouse. We will try to find options to co-label the cells.

The wblot shown in panel D does not really reflect the point the authors want to make by the quantification in panels G-I. Primary data (D) suggests that SNAT7 KD reduces HIV-1 production even in the absence of SAMHD1. The quantification rather indicates that SNAT7 KD does not affect HIV-1 production in the absence of SAMHD1. This needs clarification/corroboration by orthogonal approaches.

We respectfully disagree with the reviewer.

Figure 4D shows a representative blot of the six donors analysed. As mentioned, the depletion of SNAT7 in the absence of SAMHD1 reduces the production of the viral proteins GagPr55 and CAp24 (see Fig. 4D). This is illustrated by the quantifications (Fig. 4G–I). Following treatment with Vpx, GagPr55 protein expression in SNAT7 KD macrophages is reduced by a factor of 2.6 for siRNA #1 (mean = 1.48, light grey bar) and by a factor of 1.83 for siRNA #2 (mean = 2.13, orange bar), compared to the control (mean = 3.9, pink bar) (Fig. 4G). Similarly, CAp24 protein expression was reduced by a factor of 2.2 for siRNA #1 (mean = 2.05, light grey bar) and by a factor of 1.36 for siRNA #2 (mean = 3.34, orange bar), compared to the control (mean = 4.52, pink bar) (Fig. 4H).

These differences are therefore consistent between the Western blot and the quantifications. However, they are not significantly different to those observed in cells treated with Vpx and depleted with control siRNA, suggesting that the viral restriction observed in SNAT7 KD cells is primarily due to SAMHD1.

Figure 5: show SAMHD1 and pSAMHD1 levels upon glutamine supplementation.

We thank the reviewer for this comment, we will perform the suggested experiment.

1. I think the discussion is very thin, mainly summarizing the results; but fails to give broader context or critically discuss the limitations and further directions.

We thank the reviewer for this comment. The discussion will be modified further accordingly.

Looking at the data as a whole, I think the results support a modest functional importance of SNAT7 for HIV-1 production in macrophages. I acknowledge that the experiments in primary macrophages are prone to high variability in different donors and the authors transparently depicted their data. However clearly, I would advice the authors to tune down the extend in which they claim SNAT7-dependency given this huge variability and the sometimes-borderline statistics. We respectfully disagree with the reviewer.

The cells used here imply greater variability than a cell line, but are also more relevant.

Indeed, the effects observed in the late stages of HIV-1 production are:

• ~80 % decrease in viral transcription compared to the control (Fig. 2I),

• ~85 % decrease in CAp24 protein expression compared to the control, as quantified by western blot (Fig. 2E), or ~90 % by ELISA measurement (Fig. 2F),

• a reduction of more than 90 % in the release of infectious particles (Fig. 2G).

These results were all significant across donors, while SNAT7 depletion was always partial (Fig. 2C, between 31 to 62 % of depletion compared to the control in infected cells).

Therefore, the data were obtained from a mixture of depleted and non-depleted macrophages. This means that the results may be underestimated.

Together, our results show that SNAT7 is necessary for HIV-1 production.

However, reading the comments, we realized that our conclusions regarding reverse transcription were too strong. SNAT7 depletion does not affect viral fusion and reverse transcription. The manuscript was modified accordingly.

On top, there are a lot of optional experiments I am sure the authors are aware of that should be done at least in the future.

For instance, how does HIV-1 upregulate SNAT7, is a viral accessory protein involved? What is the mechanism of SNAT7 dependent SAMHD1 phosphorylation? Does SNAT7 (or glutamine) regulate the activity of the SAMHD1 associated kinase / phosphatase) If so, does this impact on other targets of these enzymes? We thank the reviewer for these questions.

To address the role of accessory viral proteins, we have already performed one experiment infecting hMDM with HIV-1 strains deleted for genes such as Nef, Vpr, Vpu and Vif, and have found no clear effect on SNAT7 protein expression compared to WT strains. As an alternative experiment, we could overexpress individual viral genes, such as Nef or Vpr, in HeLa cells and analyze their impact on SNAT7 expression by Western blot.

It is also possible that SNAT7 expression and recycling of lysosomal glutamine are modulated by the macrophage intrinsic immunity in response to HIV-1 infection.

The Thr592 motif of the SAMHD1 protein is phosphorylated by Cyclin A2/CDK1 and type 1 IFN in non-cycling cells, such as MDMs (Cribier et al., 2013). For now, the relationship between SNAT7 and SAMHD1 remains unclear. However, (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This has been added to the discussion to explain the relationship between the 3 partners.

**Referees cross-commenting** I think the comments from the other referees are reasonable and consistent with my assessment

Reviewer #1 (Significance (Required)):

Strength and limitations see above;

Significance: I think this work is of high interest for virologists working in the field of HIV-1 and infection of myeloid cells. In case SNAT7 (and hence glutamine) indeed regulates the phosphorylation of SAMHD1, there could potentially be broad relevance of this work. However unfortunately, this aspect remains underdeveloped and is also not discussed

Field of expertise: HIV-1, immunology, cell biology

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

In this report, Herit and colleagues describe the role of a HIV-1 dependency factor that promotes virus replication in macrophages. The authors suggest that the lysosomal membrane-associated SNAT7 glutamine transporter is a HIV dependency factor, that promotes virus replication by enhancing reverse transcription and Gag synthesis. The authors use transient knock-down approaches in primary macrophages to identify that SNAT7 depletion does not impact viral entry but inhibits early reverse transcription which was reversed by exogenous glutamine addition. While reverse transcription enhancement was likely due to selective increase in phosho-SAMHD1 expression, mechanisms by which SNAT7 enhanced viral gene expression were not clearly defined. These are well-controlled studies that pinpoint the role of SNAT7 in the early steps of viral life cycle and highlight the intricate interplay between macrophage metabolism and HIV-1 replication. While the question that is addressed is important, and the hypothesis overall sound, the data presented needs to be strengthened to support the conclusions. There are numerous weaknesses in data interpretation as well.

1. Figure 1: SNAT7 expression was selectively enhanced upon differentiation of monocytes into macrophages but absent in CD4+ T cells. Though there is a claim of enhancement of SNAT7 expression upon HIV-1 infection of macrophages, RT-qPCR analysis shows the opposite trend (Fig 1E) and SNAT7 protein expression changes are modest. Statistical analysis in Fig. 1H needs to be revisited. The number of replicates vary for the lysates harvested at different day post infection, which might have an impact on the statistical test. To determine if SNAT7 expression enhancement is dependent on establishment of virus infection, as the authors imply, control lysates of virus infections in presence of replication inhibitors should be included.

We thank the reviewer for this comment. Indeed, there is a modest, but statistically significant increase in SNAT7 protein expression upon HIV-1 infection over time (Fig. 1G, H), without any modulation of SNAT7 gene expression (Fig. 1E). This indicates that the regulation of SNAT7 expression in this context is only at the translation level (i.e. increase of translation or stabilization of the SNAT7 protein).

As mentioned, Fig. 1H aggregates between 3 to 7 independent experiments on different donors depending on the infection time point. SNAT7 protein expression is increased already at 1 day post-infection and until 8 days. The statistical test used here, i.e. 2 way-ANOVA, compared Mock-infected and HIV-1-infected condition for each time point with the same number of donors. In this figure, the comparison is statistically different only at day 6 of the time course (7 donors). We agree that increasing the number of donors of the other time points could help to improve the statistical difference between control and infection condition.

We thank the reviewer for the suggestion mentioning the use of replication inhibitors in this experiment. We plan to use inhibitors of reverse transcription (Nevirapin) and integration (Dolutegravir).

The authors rely exclusively on western blot analysis for HIV-1 Gag expression in cell lysates as a measure of effects of SNAT7 on virus replication. Single cell analysis such as intracellular p24gag analysis by FACS should be included; this will provide a better measure of effects of SNAT7 onHIV-1 infection establishment.

We respectfully disagree with the reviewer for this question. Indeed, to evaluate the effects of SNAT7 on HIV-1 replication, we measured Gag Pr55 and Cap24 using a Western blot approach (Fig. 2B, D and E), but also assessed the quantity of Cap24 in the supernatants and lysates using an ELISA measurement, the quantity of infectious particles using TZM reporter cells, and total viral transcription or more specifically Gag Pr55 transcription using qPCR (Fig. 2F, G and I and Supp. Fig. 2G).

Regarding the quantification of CAp24 at the cell single level, please refer to comment #2 under Reviewer #1.

Knockdown of SNAT7 in MDMs was partial at best; only 30-50% decrease in expression (Fig 2C), but the effects on viral gene expression (Fig. 2I), p24 release and infectious particle production is dramatic (Fig. 2F and G). This discrepancy is not addressed. Does SNAT7 knock-down negatively impact virus particle release? Please note that the representative WB in Fig 2B does not correlate with the quantification in Fig. 2D. There are no p55gag or p24gag bands in SNAT7#1 siRNA condition (Fig. 2B)? Data could also be rearranged to follow the logical sequence of virus replication cycle (viral RNa expression followed by Gag expression, and then release).

We thank the reviewer for this comment. Our samples are indeed a mixture of SNAT7-depleted and non-depleted macrophages and RNA interference in these cells often leads to a decrease of 50 % of the protein expression.

To determine whether SNAT7 is involved in the release of particles, we quantified Cap24 in cell lysates and in the cell culture medium separately, and normalized the results to the total protein content. The absence of SNAT7 reduced the amount of Cap24 measured by ELISA in both samples to the same extent, showing that there is no storage of Cap24-positive viral particles inside the infected macrophages. These data were initially pooled in one graph (Fig. 2F), but separate graphs are now provided in new Supp. Fig. 2 E, F.

Regarding the western blot shown in Fig. 2B, please refer to comment #5 under Reviewer #1.

In the new version of the manuscript, we arranged the figures and placed the later stages of the viral cycle in Fig. 2 and the earlier stages, such as fusion, reverse transcription and transcription, in Fig. 3.

Data interpretation would be greatly improved by including infection controls (RT or integrase inhibitors) to confirm that measurements of viral RNA and Gag are indeed modulated by SNAT7 expression.

We thank the reviewer for this suggestion to include inhibitors of viral replication as controls. In our experiments, cells were Mock-infected in parallel as a negative control of viral detection. We provide the results in the new version of the manuscript to show that (i) there is no detection of viral or Gag RNA in the absence of the virus, (ii) the expression of viral genes measured in HIV-1-infected SNAT7-depleted cells is not different from Mock-infected cells, indicating almost complete inhibition of viral transcription (Fig. 3H and Supp. Fig. 3B), also confirmed at the protein level (Fig. 2B, D-F).

Figure 3: Decrease in SNAT7 expression in macrophages resulted in lower levels of early reverse transcripts. But surprisingly, LRT levels were not as affected by decreases in SNAT7 expression. The authors go on to suggest that decreases in early RT are due to loss of phospho-SAMHD1 and increases in catalytically active form of SAMHD1. Mechanistically this does not make sense: LRT should be similarly affected by increase in catalytically active SAMHD1. dNTP concentrations should be measured to determine if the rescue of RT is dependent on SAMHD1 dNTPase activity.

We thank the reviewer for this comment. LRT concentrations are very low in human macrophages and more challenging to detect than ERT concentrations. This might explain why the differences observed between the SNAT7-depleted and control conditions appear less pronounced for LRT than for ERT.

Furthermore, we cannot rule out the possibility that SNAT7 has a cumulative effect throughout the viral cycle. While reverse transcription remains statistically unaltered, and despite the reduced levels of ERT and LRT in SNAT7-depleted macrophages (Fig. 3 F, G), there is a significant impact on the transcription of viral RNAs (Fig. 2I) and Gag (Supp. Fig. 2G). This step may also be altered by the ribonuclease activity of SAMHD1 (Beloglazova et al., 2013; Ryoo et al., 2014).

Finally, with the help of Dr Baek Kim in Atlanta, we attempted to quantify dNTP concentrations in our human macrophages. Unfortunately, it was not possible to draw any conclusions, as the concentrations of dNTPs extracted from our cells were far too low.

Furthermore, it should be noted that SAMHD1 viral restriction through its phosphorylation at T592 is not correlated with its dNTPase activity (Welbourn et al., 2013; White et al., 2013), but with its ribonuclease activity (Beloglazova et al., 2013; Ryoo et al., 2014). This is supporting why SNAT7, by modulating the ribonuclease activity of SAMHD1, could have a greater effect on viral transcription than on reverse transcription.

There is lack of consistency in the data: p24 release upon SNAT7 depletion is highly variable. While there is a dramatic >90-95% decrease in p24 release (Fig. 2G), the effects are much more moderate in Fig. 4H (50-60% attenuation), even though siRNA-mediated depletion was similar across the data sets. The authors should comment on the variability in their findings.

We thank the reviewer for this comment, but believe that Figure 2E rather than Figure 2G is to be mentioned regarding the quantification of CAp24 by Western blot and to be compared with Figure 4H.

In Fig. 2E, we observed an average reduction of 85 % in CAp24 expression normalized to Clathrin HC expression across different donors for both siRNAs targeting SNAT7. For Fig. 4H, there was a 73 % reduction in CAp24 levels for siRNA #1 and a 56 % reduction for siRNA #2. In addition, it should be noted that the reduction in Gag levels is greater in Fig. 4G (between 77 % and 83 %) than in Fig. 2D (between 55 % and 72 %).

Therefore, there is some variation in the results obtained with the different donors, which could be explained by variations in Gag cleavage among donors, but this does not impact the conclusions for both figures.

SNAT7 is postulated to affect 2 steps in the virus life cycle: reverse transcription and viral transcription. But Vpx-mediated SAMHD1 degradation reversed both. Its not clear to me as to how SAMHD1 degradation impacts the role of SNAT7 in viral transcription. No explanation is provided.

We thank the reviewer for this comment. As suggested, we will perform experiments to assess the impact of Vpx-mediated SAMHD1 degradation on viral transcription.

Exogenous addition of glutamine only partially restored Gag synthesis and p24 release, which could be attributed to increased cytoplasmic levels and viral protein synthesis. What about effects on reverse transcription and viral gene expression?

We thank the reviewer for this comment. We will perform the suggested experiments to assess the impact of glutamine supplementation on viral transcription.

Reviewer #2 (Significance (Required)):

This is a novel finding, as there are limited number of studies on amino acid transporters and HIV-1 replication enhancement in macrophages. Most of the previous work has focused on CD4 T cells. These studies on SNAT7 and HIV-1 infection establishment in macrophages might better inform the influences of macrophage metabolism on HIV-1 persistence and inflammatory responses.

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

This study investigates the role of the lysosomal glutamine transporter SLC38A7/SNAT7 in HIV‑1 replication in primary human macrophages. The authors demonstrate that SNAT7 is highly expressed in macrophages and upregulated upon HIV‑1 infection. They show that SNAT7 depletion inhibits HIV‑1 production at the reverse transcription step without affecting viral fusion or global cellular translation/transcription. Mechanistically, SNAT7 knockdown reduces the inhibitory phosphorylation of SAMHD1 at T592, and degradation of SAMHD1 by Vpx fully rescues viral replication. Extracellular glutamine supplementation partially restores HIV‑1 production in SNAT7‑deficient cells. Overall, the authors report interesting observations; however, the mechanistic investigation remains preliminary, raising concerns about whether the data fully support all the conclusions drawn. Major Concerns： 1. The mechanistic depth is insufficient. The authors do not elucidate how glutamine regulates SAMHD1 T592 phosphorylation, whether through metabolite‑mediated control of kinases/phosphatases or via indirect effects.

We thank the reviewer for this comment. It is worth noting that (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity using drugs decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This is now further discussed in the discussion section of the manuscript.

The authors do not measure intracellular dNTP levels upon SNAT7 knockdown, which is the key functional substrate of SAMHD1. They also do not directly demonstrate that glutamine supplementation restores dNTP pools.

We thank the reviewer for this comment. Please, refer to comment #5 under Reviewer #2.

Extracellular glutamine only partially rescues viral production, implying the existence of transport‑independent functions of SNAT7 or additional pathways. This important observation is not discussed.

We thank the reviewer for this comment. The discussion has been modified accordingly.

It is suggested that the key findings be validated in immortalized THP‑1 cells differentiated into macrophage‑like cells by PMA.

We thank the reviewer for this suggestion but don’t really understand why this would strengthen our conclusions. Indeed, despite the known variability between donors and technical limitations to transduce cells, we chose human blood monocyte-derived macrophages as a relevant non-transformed model for HIV-1 infection of macrophages. They also represent to some extent the human diversity.

The Discussion section should be expanded to include the potential translational implications and limitations of the present study.

We thank the reviewer for this comment. The discussion points to some elements of potential translation and limitations of the study.

Reviewer #3 (Significance (Required)):

General assessment: This study identifies the lysosomal glutamine transporter SLC38A7/SNAT7 as a novel host dependency factor for HIV‑1 replication in primary human macrophages. The major strengths include the use of physiologically relevant primary macrophage models, a well-organized experimental pipeline from expression profiling to functional validation, and the establishment of a link between SNAT7, glutamine metabolism, and the HIV restriction factor SAMHD1.

Advance: It extends current understanding of HIV‑1 host dependency factors and immunometabolism by revealing a compartment‑specific metabolic pathway that supports viral reverse transcription.

Audience:This work will primarily interest specialized researchers in HIV‑1 biology, host-virus interactions, restriction factors, and antiviral innate immunity.

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

This study from the Niedergang lab establishes SNAT7 as a host-dependency factor in human macrophages that supports HIV-1 replication. They show a modest increase in SNAT7 levels HIV-1 infected macrophages and suggest that SNAT7 levels are transiently increased. Employing siRNA against SNAT7 they show reduction in HIV-1 protein levels and viral RNAs and claim that there is a block of reverse transcription in SNAT7 KD cells. Focusing on a known HIV-1 restriction factor in macrophages, SAMHD1, they interconnect the SNAT7 depletion with a reduction in phosphorylated, i.e. catalytical inactive SAMHD1 arguing that SNAT7 regulates the phosphorylation and thereby antiviral activity of SAMHD1. Since SNAT7 is a glutamine transporter that provides this AA from lysosomes, they lastly supplement glutamine and this somehow rescues the reduction of HIV-1 production in SNAT7 KD cells.

Major comments:

The strength of this manuscript is the clear focus on primary human macrophages that are HIV-1 infected and the interconnection of HIV-1 replication to the SNAT7 siRNA KD experiments in combination with SAMHD1 depletion and lastly glutamine supplementation. This establishes a stringent and coherent story line. The effects reported are modest; high variability is not a problem since using primary hMDM this is expected and can be addressed by testing several donors and applying stringent statistics.

1. Having said so, I realize that while they give information on the statistical test used, i.e. one-way ANOVA they miss to explain the post-test used to assess significance (i.e. Bonferroni, Fishers LSD, whatsoever). Please add this information.

We thank the reviewer for this comment. The figure legends have been updated to include more details of all the statistical tests used.

1. Another issue that might underestimate the effects of HIV-1 infection on SNAT7 levels and vice versa of SNAT7 KD on HIV-1 replication is the non-single cell approach employed, i.e. WBlots. I assume that HIV-1 infection rates in macrophages are not super high, usually not exceeding 20-30%. So indeed the effects the authors observe could be much higher, when checking at the single cell level. I do not know about the SNAT7 ab, but all the other reagents should work via flow cytometry and could hence improve the readout a lot.

We agree with the reviewer and indeed, in previous studies on HIV-1 infection of human macrophages performed in the lab, we observed via immunofluorescence that the proportion of infected cells ranged from 20 to 40 %. At the time of submission, we did not have the possibility to label the native SNAT7 protein by immunofluorescence, as the commercial antibody used only works for western blotting.

In the meantime, we have been validating a new antibody (Proteintech) targeting SNAT7 for immunofluorescence. If this is confirmed, we will be able to detect and quantify HIV-1 p24 by immunofluorescence in SNAT7-depleted human macrophages and control cells, thus confirming our results in single-cell analysis.

Flow cytometry analyses are difficult to perform on primary human macrophages because these cells are highly adherent and must be detached first. The process induces significant cell death and damage. This is why we would prefer to carry out these analyses using immunofluorescence and microscopy on adhered cells. This option will be undoubtedly pursued.

1. Furthermore the authors never commented about a dose-response effect in terms of HIV-1 infection levels. There is a MOI dependency described for Suppl.Fig.1 C-F, unfortunately the data is missing in the manuscript.

We apologize for this omission. The figures showing the increase in SNAT7 protein expression following HIV-1 infection at MOIs ranging from 0.05 to 0.5 were added to the new version of the manuscript (Supp. Fig. 1 C-F).

1. Figure1: specify circulating T lymphocytes. I would expect to see levels of SNAT7 in PHA or CD3/CD28 activated lymphocytes versus resting T cells and a time course of SNAT7 levels upon activation. I think even though SNAT7 levels in T cells might be low, they could also be increased by HIV-1 infection and it is essential that the authors test for this. If not, the result is a valid negative control. For this they should employ HIV-1 primary strains with a tropism for T cells, or at least lab-adapted HIV-1 NL4-3

We thank the reviewer for this comment. Circulating T lymphocytes isolated from the blood of healthy donors are now referred to resting lymphocytes in the new version of the manuscript, as opposed to activated T lymphocytes stimulated with IL2 and PHA-P for several days (Fig. 1 A-C).

The expression levels of SNAT7, both at the gene and protein levels, are lower in resting or IL2/PHA-P-activated T cells than in macrophages from the same donors. As suggested, we will perform a kinetic of T-cell activation upon HIV-1 infection to investigate how SNAT7 expression varies in these conditions.

1. Figure 2 again single cell measurements could reveal much more pronounced effects; it is a bit counterintuitive that siRNA #2 is more efficient in SNAT7 KD but has higher levels of HIV-1 replication in terms of Gag levels. I assume when looking at the stats it is always a comparison to the Ctl treated cells (C-G), but this is not entirely clear. Unify labeling as compared to the stats in Fig.2 I (this also applies for all the other figs).

We thank the reviewer for this comment. Fig. 2B indeed shows one of the different donors analyzed. However, protein quantification across six different donors shows that SNAT7 is more depleted with siRNA #2 (Fig. 2C), and that Gag Pr55 protein levels are consequently more reduced, than with siRNA #1 (Fig. 2D).

We use GraphPad Prism software to perform statistical analysis. Depending on the test used, the software automatically plots the comparison bar and displays the p-value above it. We changed the representation of statistics as suggested.

Figure 3: It is a bit odd that they finally conclude on RT as essential step that is reduced in the absence of SNAT7 and then they fail to provide statistical significance for this (Fig.3 panels F and G). One would expect that RT is much more affected given the huge effects on HIV-1 capsid and particle production shown in Fig.2 F, G and I.

The reviewer is right in pointing that we observed a stronger effect during the later stages of the viral cycle, from transcription of viral RNAs (Fig. 2I and Supp. Fig. 2G) to the production of viral particles in the supernatant (Fig. 2D-G), than during the earlier stage of reverse transcription (Fig. 3F, G). Also, it is also possible that we might have missed the peak in ERT/LRT production, which is transient.

It should be noted that SAMHD1 exhibits both dNTPase (Goldstone et al., 2011) and nuclease (Beloglazova et al., 2013) activities. The ability of SAMHD1 to restrict the virus, through dephosphorylation at T592, is mediated by its RNase activity (Ryoo et al., 2014), and not by the dNTPase activity (Welbourn et al., 2013; White et al., 2013).This could explain why SNAT7 exhibit a stronger impact on viral transcription than on reverse transcription.

Figure 4; again single cell flow measurements of SAMHD1, pSAMHD1 and p24 /SNAT7 might help to more clearly discriminate effects that are specifically induced upon infection or happen in virally infected cells. Maybe alternatively IF?

We thank the reviewer for this suggestion. As mentioned under comment #2, flow cytometry analyses are difficult to perform on strongly adherent primary human macrophages.

With regard to immunofluorescence, there is a technical limitation based on the species in which the antibodies are produced. The antibody that targets the native SNAT7 protein, which is currently being validated in our laboratory, is produced in rabbits. An anti-CAp24 antibody produced in goats can be used. It will then be necessary to co-label the cells with anti SAMHD1 and phospho-SAMHD1produced in mouse. We will try to find options to co-label the cells.

The wblot shown in panel D does not really reflect the point the authors want to make by the quantification in panels G-I. Primary data (D) suggests that SNAT7 KD reduces HIV-1 production even in the absence of SAMHD1. The quantification rather indicates that SNAT7 KD does not affect HIV-1 production in the absence of SAMHD1. This needs clarification/corroboration by orthogonal approaches.

We respectfully disagree with the reviewer.

Figure 4D shows a representative blot of the six donors analysed. As mentioned, the depletion of SNAT7 in the absence of SAMHD1 reduces the production of the viral proteins GagPr55 and CAp24 (see Fig. 4D). This is illustrated by the quantifications (Fig. 4G–I). Following treatment with Vpx, GagPr55 protein expression in SNAT7 KD macrophages is reduced by a factor of 2.6 for siRNA #1 (mean = 1.48, light grey bar) and by a factor of 1.83 for siRNA #2 (mean = 2.13, orange bar), compared to the control (mean = 3.9, pink bar) (Fig. 4G). Similarly, CAp24 protein expression was reduced by a factor of 2.2 for siRNA #1 (mean = 2.05, light grey bar) and by a factor of 1.36 for siRNA #2 (mean = 3.34, orange bar), compared to the control (mean = 4.52, pink bar) (Fig. 4H).

These differences are therefore consistent between the Western blot and the quantifications. However, they are not significantly different to those observed in cells treated with Vpx and depleted with control siRNA, suggesting that the viral restriction observed in SNAT7 KD cells is primarily due to SAMHD1.

Figure 5: show SAMHD1 and pSAMHD1 levels upon glutamine supplementation.

We thank the reviewer for this comment, we will perform the suggested experiment.

1. I think the discussion is very thin, mainly summarizing the results; but fails to give broader context or critically discuss the limitations and further directions.

We thank the reviewer for this comment. The discussion will be modified further accordingly.

Looking at the data as a whole, I think the results support a modest functional importance of SNAT7 for HIV-1 production in macrophages. I acknowledge that the experiments in primary macrophages are prone to high variability in different donors and the authors transparently depicted their data. However clearly, I would advice the authors to tune down the extend in which they claim SNAT7-dependency given this huge variability and the sometimes-borderline statistics. We respectfully disagree with the reviewer.

The cells used here imply greater variability than a cell line, but are also more relevant.

Indeed, the effects observed in the late stages of HIV-1 production are:

• ~80 % decrease in viral transcription compared to the control (Fig. 2I),

• ~85 % decrease in CAp24 protein expression compared to the control, as quantified by western blot (Fig. 2E), or ~90 % by ELISA measurement (Fig. 2F),

• a reduction of more than 90 % in the release of infectious particles (Fig. 2G).

These results were all significant across donors, while SNAT7 depletion was always partial (Fig. 2C, between 31 to 62 % of depletion compared to the control in infected cells).

Therefore, the data were obtained from a mixture of depleted and non-depleted macrophages. This means that the results may be underestimated.

Together, our results show that SNAT7 is necessary for HIV-1 production.

However, reading the comments, we realized that our conclusions regarding reverse transcription were too strong. SNAT7 depletion does not affect viral fusion and reverse transcription. The manuscript was modified accordingly.

On top, there are a lot of optional experiments I am sure the authors are aware of that should be done at least in the future.

For instance, how does HIV-1 upregulate SNAT7, is a viral accessory protein involved? What is the mechanism of SNAT7 dependent SAMHD1 phosphorylation? Does SNAT7 (or glutamine) regulate the activity of the SAMHD1 associated kinase / phosphatase) If so, does this impact on other targets of these enzymes? We thank the reviewer for these questions.

To address the role of accessory viral proteins, we have already performed one experiment infecting hMDM with HIV-1 strains deleted for genes such as Nef, Vpr, Vpu and Vif, and have found no clear effect on SNAT7 protein expression compared to WT strains. As an alternative experiment, we could overexpress individual viral genes, such as Nef or Vpr, in HeLa cells and analyze their impact on SNAT7 expression by Western blot.

It is also possible that SNAT7 expression and recycling of lysosomal glutamine are modulated by the macrophage intrinsic immunity in response to HIV-1 infection.

The Thr592 motif of the SAMHD1 protein is phosphorylated by Cyclin A2/CDK1 and type 1 IFN in non-cycling cells, such as MDMs (Cribier et al., 2013). For now, the relationship between SNAT7 and SAMHD1 remains unclear. However, (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This has been added to the discussion to explain the relationship between the 3 partners.

**Referees cross-commenting** I think the comments from the other referees are reasonable and consistent with my assessment

Reviewer #1 (Significance (Required)):

Strength and limitations see above;

Significance: I think this work is of high interest for virologists working in the field of HIV-1 and infection of myeloid cells. In case SNAT7 (and hence glutamine) indeed regulates the phosphorylation of SAMHD1, there could potentially be broad relevance of this work. However unfortunately, this aspect remains underdeveloped and is also not discussed

Field of expertise: HIV-1, immunology, cell biology

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

In this report, Herit and colleagues describe the role of a HIV-1 dependency factor that promotes virus replication in macrophages. The authors suggest that the lysosomal membrane-associated SNAT7 glutamine transporter is a HIV dependency factor, that promotes virus replication by enhancing reverse transcription and Gag synthesis. The authors use transient knock-down approaches in primary macrophages to identify that SNAT7 depletion does not impact viral entry but inhibits early reverse transcription which was reversed by exogenous glutamine addition. While reverse transcription enhancement was likely due to selective increase in phosho-SAMHD1 expression, mechanisms by which SNAT7 enhanced viral gene expression were not clearly defined. These are well-controlled studies that pinpoint the role of SNAT7 in the early steps of viral life cycle and highlight the intricate interplay between macrophage metabolism and HIV-1 replication. While the question that is addressed is important, and the hypothesis overall sound, the data presented needs to be strengthened to support the conclusions. There are numerous weaknesses in data interpretation as well.

1. Figure 1: SNAT7 expression was selectively enhanced upon differentiation of monocytes into macrophages but absent in CD4+ T cells. Though there is a claim of enhancement of SNAT7 expression upon HIV-1 infection of macrophages, RT-qPCR analysis shows the opposite trend (Fig 1E) and SNAT7 protein expression changes are modest. Statistical analysis in Fig. 1H needs to be revisited. The number of replicates vary for the lysates harvested at different day post infection, which might have an impact on the statistical test. To determine if SNAT7 expression enhancement is dependent on establishment of virus infection, as the authors imply, control lysates of virus infections in presence of replication inhibitors should be included.

We thank the reviewer for this comment. Indeed, there is a modest, but statistically significant increase in SNAT7 protein expression upon HIV-1 infection over time (Fig. 1G, H), without any modulation of SNAT7 gene expression (Fig. 1E). This indicates that the regulation of SNAT7 expression in this context is only at the translation level (i.e. increase of translation or stabilization of the SNAT7 protein).

As mentioned, Fig. 1H aggregates between 3 to 7 independent experiments on different donors depending on the infection time point. SNAT7 protein expression is increased already at 1 day post-infection and until 8 days. The statistical test used here, i.e. 2 way-ANOVA, compared Mock-infected and HIV-1-infected condition for each time point with the same number of donors. In this figure, the comparison is statistically different only at day 6 of the time course (7 donors). We agree that increasing the number of donors of the other time points could help to improve the statistical difference between control and infection condition.

We thank the reviewer for the suggestion mentioning the use of replication inhibitors in this experiment. We plan to use inhibitors of reverse transcription (Nevirapin) and integration (Dolutegravir).

The authors rely exclusively on western blot analysis for HIV-1 Gag expression in cell lysates as a measure of effects of SNAT7 on virus replication. Single cell analysis such as intracellular p24gag analysis by FACS should be included; this will provide a better measure of effects of SNAT7 onHIV-1 infection establishment.

We respectfully disagree with the reviewer for this question. Indeed, to evaluate the effects of SNAT7 on HIV-1 replication, we measured Gag Pr55 and Cap24 using a Western blot approach (Fig. 2B, D and E), but also assessed the quantity of Cap24 in the supernatants and lysates using an ELISA measurement, the quantity of infectious particles using TZM reporter cells, and total viral transcription or more specifically Gag Pr55 transcription using qPCR (Fig. 2F, G and I and Supp. Fig. 2G).

Regarding the quantification of CAp24 at the cell single level, please refer to comment #2 under Reviewer #1.

Knockdown of SNAT7 in MDMs was partial at best; only 30-50% decrease in expression (Fig 2C), but the effects on viral gene expression (Fig. 2I), p24 release and infectious particle production is dramatic (Fig. 2F and G). This discrepancy is not addressed. Does SNAT7 knock-down negatively impact virus particle release? Please note that the representative WB in Fig 2B does not correlate with the quantification in Fig. 2D. There are no p55gag or p24gag bands in SNAT7#1 siRNA condition (Fig. 2B)? Data could also be rearranged to follow the logical sequence of virus replication cycle (viral RNa expression followed by Gag expression, and then release).

We thank the reviewer for this comment. Our samples are indeed a mixture of SNAT7-depleted and non-depleted macrophages and RNA interference in these cells often leads to a decrease of 50 % of the protein expression.

To determine whether SNAT7 is involved in the release of particles, we quantified Cap24 in cell lysates and in the cell culture medium separately, and normalized the results to the total protein content. The absence of SNAT7 reduced the amount of Cap24 measured by ELISA in both samples to the same extent, showing that there is no storage of Cap24-positive viral particles inside the infected macrophages. These data were initially pooled in one graph (Fig. 2F), but separate graphs are now provided in new Supp. Fig. 2 E, F.

Regarding the western blot shown in Fig. 2B, please refer to comment #5 under Reviewer #1.

In the new version of the manuscript, we arranged the figures and placed the later stages of the viral cycle in Fig. 2 and the earlier stages, such as fusion, reverse transcription and transcription, in Fig. 3.

Data interpretation would be greatly improved by including infection controls (RT or integrase inhibitors) to confirm that measurements of viral RNA and Gag are indeed modulated by SNAT7 expression.

We thank the reviewer for this suggestion to include inhibitors of viral replication as controls. In our experiments, cells were Mock-infected in parallel as a negative control of viral detection. We provide the results in the new version of the manuscript to show that (i) there is no detection of viral or Gag RNA in the absence of the virus, (ii) the expression of viral genes measured in HIV-1-infected SNAT7-depleted cells is not different from Mock-infected cells, indicating almost complete inhibition of viral transcription (Fig. 3H and Supp. Fig. 3B), also confirmed at the protein level (Fig. 2B, D-F).

Figure 3: Decrease in SNAT7 expression in macrophages resulted in lower levels of early reverse transcripts. But surprisingly, LRT levels were not as affected by decreases in SNAT7 expression. The authors go on to suggest that decreases in early RT are due to loss of phospho-SAMHD1 and increases in catalytically active form of SAMHD1. Mechanistically this does not make sense: LRT should be similarly affected by increase in catalytically active SAMHD1. dNTP concentrations should be measured to determine if the rescue of RT is dependent on SAMHD1 dNTPase activity.

We thank the reviewer for this comment. LRT concentrations are very low in human macrophages and more challenging to detect than ERT concentrations. This might explain why the differences observed between the SNAT7-depleted and control conditions appear less pronounced for LRT than for ERT.

Furthermore, we cannot rule out the possibility that SNAT7 has a cumulative effect throughout the viral cycle. While reverse transcription remains statistically unaltered, and despite the reduced levels of ERT and LRT in SNAT7-depleted macrophages (Fig. 3 F, G), there is a significant impact on the transcription of viral RNAs (Fig. 2I) and Gag (Supp. Fig. 2G). This step may also be altered by the ribonuclease activity of SAMHD1 (Beloglazova et al., 2013; Ryoo et al., 2014).

Finally, with the help of Dr Baek Kim in Atlanta, we attempted to quantify dNTP concentrations in our human macrophages. Unfortunately, it was not possible to draw any conclusions, as the concentrations of dNTPs extracted from our cells were far too low.

Furthermore, it should be noted that SAMHD1 viral restriction through its phosphorylation at T592 is not correlated with its dNTPase activity (Welbourn et al., 2013; White et al., 2013), but with its ribonuclease activity (Beloglazova et al., 2013; Ryoo et al., 2014). This is supporting why SNAT7, by modulating the ribonuclease activity of SAMHD1, could have a greater effect on viral transcription than on reverse transcription.

There is lack of consistency in the data: p24 release upon SNAT7 depletion is highly variable. While there is a dramatic >90-95% decrease in p24 release (Fig. 2G), the effects are much more moderate in Fig. 4H (50-60% attenuation), even though siRNA-mediated depletion was similar across the data sets. The authors should comment on the variability in their findings.

We thank the reviewer for this comment, but believe that Figure 2E rather than Figure 2G is to be mentioned regarding the quantification of CAp24 by Western blot and to be compared with Figure 4H.

In Fig. 2E, we observed an average reduction of 85 % in CAp24 expression normalized to Clathrin HC expression across different donors for both siRNAs targeting SNAT7. For Fig. 4H, there was a 73 % reduction in CAp24 levels for siRNA #1 and a 56 % reduction for siRNA #2. In addition, it should be noted that the reduction in Gag levels is greater in Fig. 4G (between 77 % and 83 %) than in Fig. 2D (between 55 % and 72 %).

Therefore, there is some variation in the results obtained with the different donors, which could be explained by variations in Gag cleavage among donors, but this does not impact the conclusions for both figures.

SNAT7 is postulated to affect 2 steps in the virus life cycle: reverse transcription and viral transcription. But Vpx-mediated SAMHD1 degradation reversed both. Its not clear to me as to how SAMHD1 degradation impacts the role of SNAT7 in viral transcription. No explanation is provided.

We thank the reviewer for this comment. As suggested, we will perform experiments to assess the impact of Vpx-mediated SAMHD1 degradation on viral transcription.

Exogenous addition of glutamine only partially restored Gag synthesis and p24 release, which could be attributed to increased cytoplasmic levels and viral protein synthesis. What about effects on reverse transcription and viral gene expression?

We thank the reviewer for this comment. We will perform the suggested experiments to assess the impact of glutamine supplementation on viral transcription.

Reviewer #2 (Significance (Required)):

This is a novel finding, as there are limited number of studies on amino acid transporters and HIV-1 replication enhancement in macrophages. Most of the previous work has focused on CD4 T cells. These studies on SNAT7 and HIV-1 infection establishment in macrophages might better inform the influences of macrophage metabolism on HIV-1 persistence and inflammatory responses.

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

This study investigates the role of the lysosomal glutamine transporter SLC38A7/SNAT7 in HIV‑1 replication in primary human macrophages. The authors demonstrate that SNAT7 is highly expressed in macrophages and upregulated upon HIV‑1 infection. They show that SNAT7 depletion inhibits HIV‑1 production at the reverse transcription step without affecting viral fusion or global cellular translation/transcription. Mechanistically, SNAT7 knockdown reduces the inhibitory phosphorylation of SAMHD1 at T592, and degradation of SAMHD1 by Vpx fully rescues viral replication. Extracellular glutamine supplementation partially restores HIV‑1 production in SNAT7‑deficient cells. Overall, the authors report interesting observations; however, the mechanistic investigation remains preliminary, raising concerns about whether the data fully support all the conclusions drawn. Major Concerns： 1. The mechanistic depth is insufficient. The authors do not elucidate how glutamine regulates SAMHD1 T592 phosphorylation, whether through metabolite‑mediated control of kinases/phosphatases or via indirect effects.

We thank the reviewer for this comment. It is worth noting that (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity using drugs decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This is now further discussed in the discussion section of the manuscript.

The authors do not measure intracellular dNTP levels upon SNAT7 knockdown, which is the key functional substrate of SAMHD1. They also do not directly demonstrate that glutamine supplementation restores dNTP pools.

We thank the reviewer for this comment. Please, refer to comment #5 under Reviewer #2.

Extracellular glutamine only partially rescues viral production, implying the existence of transport‑independent functions of SNAT7 or additional pathways. This important observation is not discussed.

We thank the reviewer for this comment. The discussion has been modified accordingly.

It is suggested that the key findings be validated in immortalized THP‑1 cells differentiated into macrophage‑like cells by PMA.

We thank the reviewer for this suggestion but don’t really understand why this would strengthen our conclusions. Indeed, despite the known variability between donors and technical limitations to transduce cells, we chose human blood monocyte-derived macrophages as a relevant non-transformed model for HIV-1 infection of macrophages. They also represent to some extent the human diversity.

The Discussion section should be expanded to include the potential translational implications and limitations of the present study.

We thank the reviewer for this comment. The discussion points to some elements of potential translation and limitations of the study.

Reviewer #3 (Significance (Required)):

General assessment: This study identifies the lysosomal glutamine transporter SLC38A7/SNAT7 as a novel host dependency factor for HIV‑1 replication in primary human macrophages. The major strengths include the use of physiologically relevant primary macrophage models, a well-organized experimental pipeline from expression profiling to functional validation, and the establishment of a link between SNAT7, glutamine metabolism, and the HIV restriction factor SAMHD1.

Advance: It extends current understanding of HIV‑1 host dependency factors and immunometabolism by revealing a compartment‑specific metabolic pathway that supports viral reverse transcription.

Audience:This work will primarily interest specialized researchers in HIV‑1 biology, host-virus interactions, restriction factors, and antiviral innate immunity.

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

This study from the Niedergang lab establishes SNAT7 as a host-dependency factor in human macrophages that supports HIV-1 replication. They show a modest increase in SNAT7 levels HIV-1 infected macrophages and suggest that SNAT7 levels are transiently increased. Employing siRNA against SNAT7 they show reduction in HIV-1 protein levels and viral RNAs and claim that there is a block of reverse transcription in SNAT7 KD cells. Focusing on a known HIV-1 restriction factor in macrophages, SAMHD1, they interconnect the SNAT7 depletion with a reduction in phosphorylated, i.e. catalytical inactive SAMHD1 arguing that SNAT7 regulates the phosphorylation and thereby antiviral activity of SAMHD1. Since SNAT7 is a glutamine transporter that provides this AA from lysosomes, they lastly supplement glutamine and this somehow rescues the reduction of HIV-1 production in SNAT7 KD cells.

Major comments:

The strength of this manuscript is the clear focus on primary human macrophages that are HIV-1 infected and the interconnection of HIV-1 replication to the SNAT7 siRNA KD experiments in combination with SAMHD1 depletion and lastly glutamine supplementation. This establishes a stringent and coherent story line. The effects reported are modest; high variability is not a problem since using primary hMDM this is expected and can be addressed by testing several donors and applying stringent statistics.

1. Having said so, I realize that while they give information on the statistical test used, i.e. one-way ANOVA they miss to explain the post-test used to assess significance (i.e. Bonferroni, Fishers LSD, whatsoever). Please add this information.

We thank the reviewer for this comment. The figure legends have been updated to include more details of all the statistical tests used.

1. Another issue that might underestimate the effects of HIV-1 infection on SNAT7 levels and vice versa of SNAT7 KD on HIV-1 replication is the non-single cell approach employed, i.e. WBlots. I assume that HIV-1 infection rates in macrophages are not super high, usually not exceeding 20-30%. So indeed the effects the authors observe could be much higher, when checking at the single cell level. I do not know about the SNAT7 ab, but all the other reagents should work via flow cytometry and could hence improve the readout a lot.

We agree with the reviewer and indeed, in previous studies on HIV-1 infection of human macrophages performed in the lab, we observed via immunofluorescence that the proportion of infected cells ranged from 20 to 40 %. At the time of submission, we did not have the possibility to label the native SNAT7 protein by immunofluorescence, as the commercial antibody used only works for western blotting.

In the meantime, we have been validating a new antibody (Proteintech) targeting SNAT7 for immunofluorescence. If this is confirmed, we will be able to detect and quantify HIV-1 p24 by immunofluorescence in SNAT7-depleted human macrophages and control cells, thus confirming our results in single-cell analysis.

Flow cytometry analyses are difficult to perform on primary human macrophages because these cells are highly adherent and must be detached first. The process induces significant cell death and damage. This is why we would prefer to carry out these analyses using immunofluorescence and microscopy on adhered cells. This option will be undoubtedly pursued.

1. Furthermore the authors never commented about a dose-response effect in terms of HIV-1 infection levels. There is a MOI dependency described for Suppl.Fig.1 C-F, unfortunately the data is missing in the manuscript.

We apologize for this omission. The figures showing the increase in SNAT7 protein expression following HIV-1 infection at MOIs ranging from 0.05 to 0.5 were added to the new version of the manuscript (Supp. Fig. 1 C-F).

1. Figure1: specify circulating T lymphocytes. I would expect to see levels of SNAT7 in PHA or CD3/CD28 activated lymphocytes versus resting T cells and a time course of SNAT7 levels upon activation. I think even though SNAT7 levels in T cells might be low, they could also be increased by HIV-1 infection and it is essential that the authors test for this. If not, the result is a valid negative control. For this they should employ HIV-1 primary strains with a tropism for T cells, or at least lab-adapted HIV-1 NL4-3

We thank the reviewer for this comment. Circulating T lymphocytes isolated from the blood of healthy donors are now referred to resting lymphocytes in the new version of the manuscript, as opposed to activated T lymphocytes stimulated with IL2 and PHA-P for several days (Fig. 1 A-C).

The expression levels of SNAT7, both at the gene and protein levels, are lower in resting or IL2/PHA-P-activated T cells than in macrophages from the same donors. As suggested, we will perform a kinetic of T-cell activation upon HIV-1 infection to investigate how SNAT7 expression varies in these conditions.

1. Figure 2 again single cell measurements could reveal much more pronounced effects; it is a bit counterintuitive that siRNA #2 is more efficient in SNAT7 KD but has higher levels of HIV-1 replication in terms of Gag levels. I assume when looking at the stats it is always a comparison to the Ctl treated cells (C-G), but this is not entirely clear. Unify labeling as compared to the stats in Fig.2 I (this also applies for all the other figs).

We thank the reviewer for this comment. Fig. 2B indeed shows one of the different donors analyzed. However, protein quantification across six different donors shows that SNAT7 is more depleted with siRNA #2 (Fig. 2C), and that Gag Pr55 protein levels are consequently more reduced, than with siRNA #1 (Fig. 2D).

We use GraphPad Prism software to perform statistical analysis. Depending on the test used, the software automatically plots the comparison bar and displays the p-value above it. We changed the representation of statistics as suggested.

Figure 3: It is a bit odd that they finally conclude on RT as essential step that is reduced in the absence of SNAT7 and then they fail to provide statistical significance for this (Fig.3 panels F and G). One would expect that RT is much more affected given the huge effects on HIV-1 capsid and particle production shown in Fig.2 F, G and I.

The reviewer is right in pointing that we observed a stronger effect during the later stages of the viral cycle, from transcription of viral RNAs (Fig. 2I and Supp. Fig. 2G) to the production of viral particles in the supernatant (Fig. 2D-G), than during the earlier stage of reverse transcription (Fig. 3F, G). Also, it is also possible that we might have missed the peak in ERT/LRT production, which is transient.

It should be noted that SAMHD1 exhibits both dNTPase (Goldstone et al., 2011) and nuclease (Beloglazova et al., 2013) activities. The ability of SAMHD1 to restrict the virus, through dephosphorylation at T592, is mediated by its RNase activity (Ryoo et al., 2014), and not by the dNTPase activity (Welbourn et al., 2013; White et al., 2013).This could explain why SNAT7 exhibit a stronger impact on viral transcription than on reverse transcription.

Figure 4; again single cell flow measurements of SAMHD1, pSAMHD1 and p24 /SNAT7 might help to more clearly discriminate effects that are specifically induced upon infection or happen in virally infected cells. Maybe alternatively IF?

We thank the reviewer for this suggestion. As mentioned under comment #2, flow cytometry analyses are difficult to perform on strongly adherent primary human macrophages.

With regard to immunofluorescence, there is a technical limitation based on the species in which the antibodies are produced. The antibody that targets the native SNAT7 protein, which is currently being validated in our laboratory, is produced in rabbits. An anti-CAp24 antibody produced in goats can be used. It will then be necessary to co-label the cells with anti SAMHD1 and phospho-SAMHD1produced in mouse. We will try to find options to co-label the cells.

The wblot shown in panel D does not really reflect the point the authors want to make by the quantification in panels G-I. Primary data (D) suggests that SNAT7 KD reduces HIV-1 production even in the absence of SAMHD1. The quantification rather indicates that SNAT7 KD does not affect HIV-1 production in the absence of SAMHD1. This needs clarification/corroboration by orthogonal approaches.

We respectfully disagree with the reviewer.

Figure 4D shows a representative blot of the six donors analysed. As mentioned, the depletion of SNAT7 in the absence of SAMHD1 reduces the production of the viral proteins GagPr55 and CAp24 (see Fig. 4D). This is illustrated by the quantifications (Fig. 4G–I). Following treatment with Vpx, GagPr55 protein expression in SNAT7 KD macrophages is reduced by a factor of 2.6 for siRNA #1 (mean = 1.48, light grey bar) and by a factor of 1.83 for siRNA #2 (mean = 2.13, orange bar), compared to the control (mean = 3.9, pink bar) (Fig. 4G). Similarly, CAp24 protein expression was reduced by a factor of 2.2 for siRNA #1 (mean = 2.05, light grey bar) and by a factor of 1.36 for siRNA #2 (mean = 3.34, orange bar), compared to the control (mean = 4.52, pink bar) (Fig. 4H).

These differences are therefore consistent between the Western blot and the quantifications. However, they are not significantly different to those observed in cells treated with Vpx and depleted with control siRNA, suggesting that the viral restriction observed in SNAT7 KD cells is primarily due to SAMHD1.

Figure 5: show SAMHD1 and pSAMHD1 levels upon glutamine supplementation.

We thank the reviewer for this comment, we will perform the suggested experiment.

1. I think the discussion is very thin, mainly summarizing the results; but fails to give broader context or critically discuss the limitations and further directions.

We thank the reviewer for this comment. The discussion will be modified further accordingly.

Looking at the data as a whole, I think the results support a modest functional importance of SNAT7 for HIV-1 production in macrophages. I acknowledge that the experiments in primary macrophages are prone to high variability in different donors and the authors transparently depicted their data. However clearly, I would advice the authors to tune down the extend in which they claim SNAT7-dependency given this huge variability and the sometimes-borderline statistics. We respectfully disagree with the reviewer.

The cells used here imply greater variability than a cell line, but are also more relevant.

Indeed, the effects observed in the late stages of HIV-1 production are:

• ~80 % decrease in viral transcription compared to the control (Fig. 2I),

• ~85 % decrease in CAp24 protein expression compared to the control, as quantified by western blot (Fig. 2E), or ~90 % by ELISA measurement (Fig. 2F),

• a reduction of more than 90 % in the release of infectious particles (Fig. 2G).

These results were all significant across donors, while SNAT7 depletion was always partial (Fig. 2C, between 31 to 62 % of depletion compared to the control in infected cells).

Therefore, the data were obtained from a mixture of depleted and non-depleted macrophages. This means that the results may be underestimated.

Together, our results show that SNAT7 is necessary for HIV-1 production.

However, reading the comments, we realized that our conclusions regarding reverse transcription were too strong. SNAT7 depletion does not affect viral fusion and reverse transcription. The manuscript was modified accordingly.

On top, there are a lot of optional experiments I am sure the authors are aware of that should be done at least in the future.

For instance, how does HIV-1 upregulate SNAT7, is a viral accessory protein involved? What is the mechanism of SNAT7 dependent SAMHD1 phosphorylation? Does SNAT7 (or glutamine) regulate the activity of the SAMHD1 associated kinase / phosphatase) If so, does this impact on other targets of these enzymes? We thank the reviewer for these questions.

To address the role of accessory viral proteins, we have already performed one experiment infecting hMDM with HIV-1 strains deleted for genes such as Nef, Vpr, Vpu and Vif, and have found no clear effect on SNAT7 protein expression compared to WT strains. As an alternative experiment, we could overexpress individual viral genes, such as Nef or Vpr, in HeLa cells and analyze their impact on SNAT7 expression by Western blot.

It is also possible that SNAT7 expression and recycling of lysosomal glutamine are modulated by the macrophage intrinsic immunity in response to HIV-1 infection.

The Thr592 motif of the SAMHD1 protein is phosphorylated by Cyclin A2/CDK1 and type 1 IFN in non-cycling cells, such as MDMs (Cribier et al., 2013). For now, the relationship between SNAT7 and SAMHD1 remains unclear. However, (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This has been added to the discussion to explain the relationship between the 3 partners.

**Referees cross-commenting** I think the comments from the other referees are reasonable and consistent with my assessment

Reviewer #1 (Significance (Required)):

Strength and limitations see above;

Significance: I think this work is of high interest for virologists working in the field of HIV-1 and infection of myeloid cells. In case SNAT7 (and hence glutamine) indeed regulates the phosphorylation of SAMHD1, there could potentially be broad relevance of this work. However unfortunately, this aspect remains underdeveloped and is also not discussed

Field of expertise: HIV-1, immunology, cell biology

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

In this report, Herit and colleagues describe the role of a HIV-1 dependency factor that promotes virus replication in macrophages. The authors suggest that the lysosomal membrane-associated SNAT7 glutamine transporter is a HIV dependency factor, that promotes virus replication by enhancing reverse transcription and Gag synthesis. The authors use transient knock-down approaches in primary macrophages to identify that SNAT7 depletion does not impact viral entry but inhibits early reverse transcription which was reversed by exogenous glutamine addition. While reverse transcription enhancement was likely due to selective increase in phosho-SAMHD1 expression, mechanisms by which SNAT7 enhanced viral gene expression were not clearly defined. These are well-controlled studies that pinpoint the role of SNAT7 in the early steps of viral life cycle and highlight the intricate interplay between macrophage metabolism and HIV-1 replication. While the question that is addressed is important, and the hypothesis overall sound, the data presented needs to be strengthened to support the conclusions. There are numerous weaknesses in data interpretation as well.

1. Figure 1: SNAT7 expression was selectively enhanced upon differentiation of monocytes into macrophages but absent in CD4+ T cells. Though there is a claim of enhancement of SNAT7 expression upon HIV-1 infection of macrophages, RT-qPCR analysis shows the opposite trend (Fig 1E) and SNAT7 protein expression changes are modest. Statistical analysis in Fig. 1H needs to be revisited. The number of replicates vary for the lysates harvested at different day post infection, which might have an impact on the statistical test. To determine if SNAT7 expression enhancement is dependent on establishment of virus infection, as the authors imply, control lysates of virus infections in presence of replication inhibitors should be included.

We thank the reviewer for this comment. Indeed, there is a modest, but statistically significant increase in SNAT7 protein expression upon HIV-1 infection over time (Fig. 1G, H), without any modulation of SNAT7 gene expression (Fig. 1E). This indicates that the regulation of SNAT7 expression in this context is only at the translation level (i.e. increase of translation or stabilization of the SNAT7 protein).

As mentioned, Fig. 1H aggregates between 3 to 7 independent experiments on different donors depending on the infection time point. SNAT7 protein expression is increased already at 1 day post-infection and until 8 days. The statistical test used here, i.e. 2 way-ANOVA, compared Mock-infected and HIV-1-infected condition for each time point with the same number of donors. In this figure, the comparison is statistically different only at day 6 of the time course (7 donors). We agree that increasing the number of donors of the other time points could help to improve the statistical difference between control and infection condition.

We thank the reviewer for the suggestion mentioning the use of replication inhibitors in this experiment. We plan to use inhibitors of reverse transcription (Nevirapin) and integration (Dolutegravir).

The authors rely exclusively on western blot analysis for HIV-1 Gag expression in cell lysates as a measure of effects of SNAT7 on virus replication. Single cell analysis such as intracellular p24gag analysis by FACS should be included; this will provide a better measure of effects of SNAT7 onHIV-1 infection establishment.

We respectfully disagree with the reviewer for this question. Indeed, to evaluate the effects of SNAT7 on HIV-1 replication, we measured Gag Pr55 and Cap24 using a Western blot approach (Fig. 2B, D and E), but also assessed the quantity of Cap24 in the supernatants and lysates using an ELISA measurement, the quantity of infectious particles using TZM reporter cells, and total viral transcription or more specifically Gag Pr55 transcription using qPCR (Fig. 2F, G and I and Supp. Fig. 2G).

Regarding the quantification of CAp24 at the cell single level, please refer to comment #2 under Reviewer #1.

Knockdown of SNAT7 in MDMs was partial at best; only 30-50% decrease in expression (Fig 2C), but the effects on viral gene expression (Fig. 2I), p24 release and infectious particle production is dramatic (Fig. 2F and G). This discrepancy is not addressed. Does SNAT7 knock-down negatively impact virus particle release? Please note that the representative WB in Fig 2B does not correlate with the quantification in Fig. 2D. There are no p55gag or p24gag bands in SNAT7#1 siRNA condition (Fig. 2B)? Data could also be rearranged to follow the logical sequence of virus replication cycle (viral RNa expression followed by Gag expression, and then release).

We thank the reviewer for this comment. Our samples are indeed a mixture of SNAT7-depleted and non-depleted macrophages and RNA interference in these cells often leads to a decrease of 50 % of the protein expression.

To determine whether SNAT7 is involved in the release of particles, we quantified Cap24 in cell lysates and in the cell culture medium separately, and normalized the results to the total protein content. The absence of SNAT7 reduced the amount of Cap24 measured by ELISA in both samples to the same extent, showing that there is no storage of Cap24-positive viral particles inside the infected macrophages. These data were initially pooled in one graph (Fig. 2F), but separate graphs are now provided in new Supp. Fig. 2 E, F.

Regarding the western blot shown in Fig. 2B, please refer to comment #5 under Reviewer #1.

In the new version of the manuscript, we arranged the figures and placed the later stages of the viral cycle in Fig. 2 and the earlier stages, such as fusion, reverse transcription and transcription, in Fig. 3.

Data interpretation would be greatly improved by including infection controls (RT or integrase inhibitors) to confirm that measurements of viral RNA and Gag are indeed modulated by SNAT7 expression.

We thank the reviewer for this suggestion to include inhibitors of viral replication as controls. In our experiments, cells were Mock-infected in parallel as a negative control of viral detection. We provide the results in the new version of the manuscript to show that (i) there is no detection of viral or Gag RNA in the absence of the virus, (ii) the expression of viral genes measured in HIV-1-infected SNAT7-depleted cells is not different from Mock-infected cells, indicating almost complete inhibition of viral transcription (Fig. 3H and Supp. Fig. 3B), also confirmed at the protein level (Fig. 2B, D-F).

Figure 3: Decrease in SNAT7 expression in macrophages resulted in lower levels of early reverse transcripts. But surprisingly, LRT levels were not as affected by decreases in SNAT7 expression. The authors go on to suggest that decreases in early RT are due to loss of phospho-SAMHD1 and increases in catalytically active form of SAMHD1. Mechanistically this does not make sense: LRT should be similarly affected by increase in catalytically active SAMHD1. dNTP concentrations should be measured to determine if the rescue of RT is dependent on SAMHD1 dNTPase activity.

We thank the reviewer for this comment. LRT concentrations are very low in human macrophages and more challenging to detect than ERT concentrations. This might explain why the differences observed between the SNAT7-depleted and control conditions appear less pronounced for LRT than for ERT.

Furthermore, we cannot rule out the possibility that SNAT7 has a cumulative effect throughout the viral cycle. While reverse transcription remains statistically unaltered, and despite the reduced levels of ERT and LRT in SNAT7-depleted macrophages (Fig. 3 F, G), there is a significant impact on the transcription of viral RNAs (Fig. 2I) and Gag (Supp. Fig. 2G). This step may also be altered by the ribonuclease activity of SAMHD1 (Beloglazova et al., 2013; Ryoo et al., 2014).

Finally, with the help of Dr Baek Kim in Atlanta, we attempted to quantify dNTP concentrations in our human macrophages. Unfortunately, it was not possible to draw any conclusions, as the concentrations of dNTPs extracted from our cells were far too low.

Furthermore, it should be noted that SAMHD1 viral restriction through its phosphorylation at T592 is not correlated with its dNTPase activity (Welbourn et al., 2013; White et al., 2013), but with its ribonuclease activity (Beloglazova et al., 2013; Ryoo et al., 2014). This is supporting why SNAT7, by modulating the ribonuclease activity of SAMHD1, could have a greater effect on viral transcription than on reverse transcription.

There is lack of consistency in the data: p24 release upon SNAT7 depletion is highly variable. While there is a dramatic >90-95% decrease in p24 release (Fig. 2G), the effects are much more moderate in Fig. 4H (50-60% attenuation), even though siRNA-mediated depletion was similar across the data sets. The authors should comment on the variability in their findings.

We thank the reviewer for this comment, but believe that Figure 2E rather than Figure 2G is to be mentioned regarding the quantification of CAp24 by Western blot and to be compared with Figure 4H.

In Fig. 2E, we observed an average reduction of 85 % in CAp24 expression normalized to Clathrin HC expression across different donors for both siRNAs targeting SNAT7. For Fig. 4H, there was a 73 % reduction in CAp24 levels for siRNA #1 and a 56 % reduction for siRNA #2. In addition, it should be noted that the reduction in Gag levels is greater in Fig. 4G (between 77 % and 83 %) than in Fig. 2D (between 55 % and 72 %).

Therefore, there is some variation in the results obtained with the different donors, which could be explained by variations in Gag cleavage among donors, but this does not impact the conclusions for both figures.

SNAT7 is postulated to affect 2 steps in the virus life cycle: reverse transcription and viral transcription. But Vpx-mediated SAMHD1 degradation reversed both. Its not clear to me as to how SAMHD1 degradation impacts the role of SNAT7 in viral transcription. No explanation is provided.

We thank the reviewer for this comment. As suggested, we will perform experiments to assess the impact of Vpx-mediated SAMHD1 degradation on viral transcription.

Exogenous addition of glutamine only partially restored Gag synthesis and p24 release, which could be attributed to increased cytoplasmic levels and viral protein synthesis. What about effects on reverse transcription and viral gene expression?

We thank the reviewer for this comment. We will perform the suggested experiments to assess the impact of glutamine supplementation on viral transcription.

Reviewer #2 (Significance (Required)):

This is a novel finding, as there are limited number of studies on amino acid transporters and HIV-1 replication enhancement in macrophages. Most of the previous work has focused on CD4 T cells. These studies on SNAT7 and HIV-1 infection establishment in macrophages might better inform the influences of macrophage metabolism on HIV-1 persistence and inflammatory responses.

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

This study investigates the role of the lysosomal glutamine transporter SLC38A7/SNAT7 in HIV‑1 replication in primary human macrophages. The authors demonstrate that SNAT7 is highly expressed in macrophages and upregulated upon HIV‑1 infection. They show that SNAT7 depletion inhibits HIV‑1 production at the reverse transcription step without affecting viral fusion or global cellular translation/transcription. Mechanistically, SNAT7 knockdown reduces the inhibitory phosphorylation of SAMHD1 at T592, and degradation of SAMHD1 by Vpx fully rescues viral replication. Extracellular glutamine supplementation partially restores HIV‑1 production in SNAT7‑deficient cells. Overall, the authors report interesting observations; however, the mechanistic investigation remains preliminary, raising concerns about whether the data fully support all the conclusions drawn. Major Concerns： 1. The mechanistic depth is insufficient. The authors do not elucidate how glutamine regulates SAMHD1 T592 phosphorylation, whether through metabolite‑mediated control of kinases/phosphatases or via indirect effects.

We thank the reviewer for this comment. It is worth noting that (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity using drugs decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This is now further discussed in the discussion section of the manuscript.

The authors do not measure intracellular dNTP levels upon SNAT7 knockdown, which is the key functional substrate of SAMHD1. They also do not directly demonstrate that glutamine supplementation restores dNTP pools.

We thank the reviewer for this comment. Please, refer to comment #5 under Reviewer #2.

Extracellular glutamine only partially rescues viral production, implying the existence of transport‑independent functions of SNAT7 or additional pathways. This important observation is not discussed.

We thank the reviewer for this comment. The discussion has been modified accordingly.

It is suggested that the key findings be validated in immortalized THP‑1 cells differentiated into macrophage‑like cells by PMA.

We thank the reviewer for this suggestion but don’t really understand why this would strengthen our conclusions. Indeed, despite the known variability between donors and technical limitations to transduce cells, we chose human blood monocyte-derived macrophages as a relevant non-transformed model for HIV-1 infection of macrophages. They also represent to some extent the human diversity.

The Discussion section should be expanded to include the potential translational implications and limitations of the present study.

We thank the reviewer for this comment. The discussion points to some elements of potential translation and limitations of the study.

Reviewer #3 (Significance (Required)):

General assessment: This study identifies the lysosomal glutamine transporter SLC38A7/SNAT7 as a novel host dependency factor for HIV‑1 replication in primary human macrophages. The major strengths include the use of physiologically relevant primary macrophage models, a well-organized experimental pipeline from expression profiling to functional validation, and the establishment of a link between SNAT7, glutamine metabolism, and the HIV restriction factor SAMHD1.

Advance: It extends current understanding of HIV‑1 host dependency factors and immunometabolism by revealing a compartment‑specific metabolic pathway that supports viral reverse transcription.

Audience:This work will primarily interest specialized researchers in HIV‑1 biology, host-virus interactions, restriction factors, and antiviral innate immunity.

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

This study from the Niedergang lab establishes SNAT7 as a host-dependency factor in human macrophages that supports HIV-1 replication. They show a modest increase in SNAT7 levels HIV-1 infected macrophages and suggest that SNAT7 levels are transiently increased. Employing siRNA against SNAT7 they show reduction in HIV-1 protein levels and viral RNAs and claim that there is a block of reverse transcription in SNAT7 KD cells. Focusing on a known HIV-1 restriction factor in macrophages, SAMHD1, they interconnect the SNAT7 depletion with a reduction in phosphorylated, i.e. catalytical inactive SAMHD1 arguing that SNAT7 regulates the phosphorylation and thereby antiviral activity of SAMHD1. Since SNAT7 is a glutamine transporter that provides this AA from lysosomes, they lastly supplement glutamine and this somehow rescues the reduction of HIV-1 production in SNAT7 KD cells.

Major comments:

The strength of this manuscript is the clear focus on primary human macrophages that are HIV-1 infected and the interconnection of HIV-1 replication to the SNAT7 siRNA KD experiments in combination with SAMHD1 depletion and lastly glutamine supplementation. This establishes a stringent and coherent story line. The effects reported are modest; high variability is not a problem since using primary hMDM this is expected and can be addressed by testing several donors and applying stringent statistics.

1. Having said so, I realize that while they give information on the statistical test used, i.e. one-way ANOVA they miss to explain the post-test used to assess significance (i.e. Bonferroni, Fishers LSD, whatsoever). Please add this information.

We thank the reviewer for this comment. The figure legends have been updated to include more details of all the statistical tests used.

1. Another issue that might underestimate the effects of HIV-1 infection on SNAT7 levels and vice versa of SNAT7 KD on HIV-1 replication is the non-single cell approach employed, i.e. WBlots. I assume that HIV-1 infection rates in macrophages are not super high, usually not exceeding 20-30%. So indeed the effects the authors observe could be much higher, when checking at the single cell level. I do not know about the SNAT7 ab, but all the other reagents should work via flow cytometry and could hence improve the readout a lot.

We agree with the reviewer and indeed, in previous studies on HIV-1 infection of human macrophages performed in the lab, we observed via immunofluorescence that the proportion of infected cells ranged from 20 to 40 %. At the time of submission, we did not have the possibility to label the native SNAT7 protein by immunofluorescence, as the commercial antibody used only works for western blotting.

In the meantime, we have been validating a new antibody (Proteintech) targeting SNAT7 for immunofluorescence. If this is confirmed, we will be able to detect and quantify HIV-1 p24 by immunofluorescence in SNAT7-depleted human macrophages and control cells, thus confirming our results in single-cell analysis.

Flow cytometry analyses are difficult to perform on primary human macrophages because these cells are highly adherent and must be detached first. The process induces significant cell death and damage. This is why we would prefer to carry out these analyses using immunofluorescence and microscopy on adhered cells. This option will be undoubtedly pursued.

1. Furthermore the authors never commented about a dose-response effect in terms of HIV-1 infection levels. There is a MOI dependency described for Suppl.Fig.1 C-F, unfortunately the data is missing in the manuscript.

We apologize for this omission. The figures showing the increase in SNAT7 protein expression following HIV-1 infection at MOIs ranging from 0.05 to 0.5 were added to the new version of the manuscript (Supp. Fig. 1 C-F).

1. Figure1: specify circulating T lymphocytes. I would expect to see levels of SNAT7 in PHA or CD3/CD28 activated lymphocytes versus resting T cells and a time course of SNAT7 levels upon activation. I think even though SNAT7 levels in T cells might be low, they could also be increased by HIV-1 infection and it is essential that the authors test for this. If not, the result is a valid negative control. For this they should employ HIV-1 primary strains with a tropism for T cells, or at least lab-adapted HIV-1 NL4-3

We thank the reviewer for this comment. Circulating T lymphocytes isolated from the blood of healthy donors are now referred to resting lymphocytes in the new version of the manuscript, as opposed to activated T lymphocytes stimulated with IL2 and PHA-P for several days (Fig. 1 A-C).

The expression levels of SNAT7, both at the gene and protein levels, are lower in resting or IL2/PHA-P-activated T cells than in macrophages from the same donors. As suggested, we will perform a kinetic of T-cell activation upon HIV-1 infection to investigate how SNAT7 expression varies in these conditions.

1. Figure 2 again single cell measurements could reveal much more pronounced effects; it is a bit counterintuitive that siRNA #2 is more efficient in SNAT7 KD but has higher levels of HIV-1 replication in terms of Gag levels. I assume when looking at the stats it is always a comparison to the Ctl treated cells (C-G), but this is not entirely clear. Unify labeling as compared to the stats in Fig.2 I (this also applies for all the other figs).

We thank the reviewer for this comment. Fig. 2B indeed shows one of the different donors analyzed. However, protein quantification across six different donors shows that SNAT7 is more depleted with siRNA #2 (Fig. 2C), and that Gag Pr55 protein levels are consequently more reduced, than with siRNA #1 (Fig. 2D).

We use GraphPad Prism software to perform statistical analysis. Depending on the test used, the software automatically plots the comparison bar and displays the p-value above it. We changed the representation of statistics as suggested.

Figure 3: It is a bit odd that they finally conclude on RT as essential step that is reduced in the absence of SNAT7 and then they fail to provide statistical significance for this (Fig.3 panels F and G). One would expect that RT is much more affected given the huge effects on HIV-1 capsid and particle production shown in Fig.2 F, G and I.

The reviewer is right in pointing that we observed a stronger effect during the later stages of the viral cycle, from transcription of viral RNAs (Fig. 2I and Supp. Fig. 2G) to the production of viral particles in the supernatant (Fig. 2D-G), than during the earlier stage of reverse transcription (Fig. 3F, G). Also, it is also possible that we might have missed the peak in ERT/LRT production, which is transient.

It should be noted that SAMHD1 exhibits both dNTPase (Goldstone et al., 2011) and nuclease (Beloglazova et al., 2013) activities. The ability of SAMHD1 to restrict the virus, through dephosphorylation at T592, is mediated by its RNase activity (Ryoo et al., 2014), and not by the dNTPase activity (Welbourn et al., 2013; White et al., 2013).This could explain why SNAT7 exhibit a stronger impact on viral transcription than on reverse transcription.

Figure 4; again single cell flow measurements of SAMHD1, pSAMHD1 and p24 /SNAT7 might help to more clearly discriminate effects that are specifically induced upon infection or happen in virally infected cells. Maybe alternatively IF?

We thank the reviewer for this suggestion. As mentioned under comment #2, flow cytometry analyses are difficult to perform on strongly adherent primary human macrophages.

With regard to immunofluorescence, there is a technical limitation based on the species in which the antibodies are produced. The antibody that targets the native SNAT7 protein, which is currently being validated in our laboratory, is produced in rabbits. An anti-CAp24 antibody produced in goats can be used. It will then be necessary to co-label the cells with anti SAMHD1 and phospho-SAMHD1produced in mouse. We will try to find options to co-label the cells.

The wblot shown in panel D does not really reflect the point the authors want to make by the quantification in panels G-I. Primary data (D) suggests that SNAT7 KD reduces HIV-1 production even in the absence of SAMHD1. The quantification rather indicates that SNAT7 KD does not affect HIV-1 production in the absence of SAMHD1. This needs clarification/corroboration by orthogonal approaches.

We respectfully disagree with the reviewer.

Figure 4D shows a representative blot of the six donors analysed. As mentioned, the depletion of SNAT7 in the absence of SAMHD1 reduces the production of the viral proteins GagPr55 and CAp24 (see Fig. 4D). This is illustrated by the quantifications (Fig. 4G–I). Following treatment with Vpx, GagPr55 protein expression in SNAT7 KD macrophages is reduced by a factor of 2.6 for siRNA #1 (mean = 1.48, light grey bar) and by a factor of 1.83 for siRNA #2 (mean = 2.13, orange bar), compared to the control (mean = 3.9, pink bar) (Fig. 4G). Similarly, CAp24 protein expression was reduced by a factor of 2.2 for siRNA #1 (mean = 2.05, light grey bar) and by a factor of 1.36 for siRNA #2 (mean = 3.34, orange bar), compared to the control (mean = 4.52, pink bar) (Fig. 4H).

These differences are therefore consistent between the Western blot and the quantifications. However, they are not significantly different to those observed in cells treated with Vpx and depleted with control siRNA, suggesting that the viral restriction observed in SNAT7 KD cells is primarily due to SAMHD1.

Figure 5: show SAMHD1 and pSAMHD1 levels upon glutamine supplementation.

We thank the reviewer for this comment, we will perform the suggested experiment.

1. I think the discussion is very thin, mainly summarizing the results; but fails to give broader context or critically discuss the limitations and further directions.

We thank the reviewer for this comment. The discussion will be modified further accordingly.

Looking at the data as a whole, I think the results support a modest functional importance of SNAT7 for HIV-1 production in macrophages. I acknowledge that the experiments in primary macrophages are prone to high variability in different donors and the authors transparently depicted their data. However clearly, I would advice the authors to tune down the extend in which they claim SNAT7-dependency given this huge variability and the sometimes-borderline statistics. We respectfully disagree with the reviewer.

The cells used here imply greater variability than a cell line, but are also more relevant.

Indeed, the effects observed in the late stages of HIV-1 production are:

• ~80 % decrease in viral transcription compared to the control (Fig. 2I),

• ~85 % decrease in CAp24 protein expression compared to the control, as quantified by western blot (Fig. 2E), or ~90 % by ELISA measurement (Fig. 2F),

• a reduction of more than 90 % in the release of infectious particles (Fig. 2G).

These results were all significant across donors, while SNAT7 depletion was always partial (Fig. 2C, between 31 to 62 % of depletion compared to the control in infected cells).

Therefore, the data were obtained from a mixture of depleted and non-depleted macrophages. This means that the results may be underestimated.

Together, our results show that SNAT7 is necessary for HIV-1 production.

However, reading the comments, we realized that our conclusions regarding reverse transcription were too strong. SNAT7 depletion does not affect viral fusion and reverse transcription. The manuscript was modified accordingly.

On top, there are a lot of optional experiments I am sure the authors are aware of that should be done at least in the future.

For instance, how does HIV-1 upregulate SNAT7, is a viral accessory protein involved? What is the mechanism of SNAT7 dependent SAMHD1 phosphorylation? Does SNAT7 (or glutamine) regulate the activity of the SAMHD1 associated kinase / phosphatase) If so, does this impact on other targets of these enzymes? We thank the reviewer for these questions.

To address the role of accessory viral proteins, we have already performed one experiment infecting hMDM with HIV-1 strains deleted for genes such as Nef, Vpr, Vpu and Vif, and have found no clear effect on SNAT7 protein expression compared to WT strains. As an alternative experiment, we could overexpress individual viral genes, such as Nef or Vpr, in HeLa cells and analyze their impact on SNAT7 expression by Western blot.

It is also possible that SNAT7 expression and recycling of lysosomal glutamine are modulated by the macrophage intrinsic immunity in response to HIV-1 infection.

The Thr592 motif of the SAMHD1 protein is phosphorylated by Cyclin A2/CDK1 and type 1 IFN in non-cycling cells, such as MDMs (Cribier et al., 2013). For now, the relationship between SNAT7 and SAMHD1 remains unclear. However, (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This has been added to the discussion to explain the relationship between the 3 partners.

**Referees cross-commenting** I think the comments from the other referees are reasonable and consistent with my assessment

Reviewer #1 (Significance (Required)):

Strength and limitations see above;

Significance: I think this work is of high interest for virologists working in the field of HIV-1 and infection of myeloid cells. In case SNAT7 (and hence glutamine) indeed regulates the phosphorylation of SAMHD1, there could potentially be broad relevance of this work. However unfortunately, this aspect remains underdeveloped and is also not discussed

Field of expertise: HIV-1, immunology, cell biology

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

In this report, Herit and colleagues describe the role of a HIV-1 dependency factor that promotes virus replication in macrophages. The authors suggest that the lysosomal membrane-associated SNAT7 glutamine transporter is a HIV dependency factor, that promotes virus replication by enhancing reverse transcription and Gag synthesis. The authors use transient knock-down approaches in primary macrophages to identify that SNAT7 depletion does not impact viral entry but inhibits early reverse transcription which was reversed by exogenous glutamine addition. While reverse transcription enhancement was likely due to selective increase in phosho-SAMHD1 expression, mechanisms by which SNAT7 enhanced viral gene expression were not clearly defined. These are well-controlled studies that pinpoint the role of SNAT7 in the early steps of viral life cycle and highlight the intricate interplay between macrophage metabolism and HIV-1 replication. While the question that is addressed is important, and the hypothesis overall sound, the data presented needs to be strengthened to support the conclusions. There are numerous weaknesses in data interpretation as well.

1. Figure 1: SNAT7 expression was selectively enhanced upon differentiation of monocytes into macrophages but absent in CD4+ T cells. Though there is a claim of enhancement of SNAT7 expression upon HIV-1 infection of macrophages, RT-qPCR analysis shows the opposite trend (Fig 1E) and SNAT7 protein expression changes are modest. Statistical analysis in Fig. 1H needs to be revisited. The number of replicates vary for the lysates harvested at different day post infection, which might have an impact on the statistical test. To determine if SNAT7 expression enhancement is dependent on establishment of virus infection, as the authors imply, control lysates of virus infections in presence of replication inhibitors should be included.

We thank the reviewer for this comment. Indeed, there is a modest, but statistically significant increase in SNAT7 protein expression upon HIV-1 infection over time (Fig. 1G, H), without any modulation of SNAT7 gene expression (Fig. 1E). This indicates that the regulation of SNAT7 expression in this context is only at the translation level (i.e. increase of translation or stabilization of the SNAT7 protein).

As mentioned, Fig. 1H aggregates between 3 to 7 independent experiments on different donors depending on the infection time point. SNAT7 protein expression is increased already at 1 day post-infection and until 8 days. The statistical test used here, i.e. 2 way-ANOVA, compared Mock-infected and HIV-1-infected condition for each time point with the same number of donors. In this figure, the comparison is statistically different only at day 6 of the time course (7 donors). We agree that increasing the number of donors of the other time points could help to improve the statistical difference between control and infection condition.

We thank the reviewer for the suggestion mentioning the use of replication inhibitors in this experiment. We plan to use inhibitors of reverse transcription (Nevirapin) and integration (Dolutegravir).

The authors rely exclusively on western blot analysis for HIV-1 Gag expression in cell lysates as a measure of effects of SNAT7 on virus replication. Single cell analysis such as intracellular p24gag analysis by FACS should be included; this will provide a better measure of effects of SNAT7 onHIV-1 infection establishment.

We respectfully disagree with the reviewer for this question. Indeed, to evaluate the effects of SNAT7 on HIV-1 replication, we measured Gag Pr55 and Cap24 using a Western blot approach (Fig. 2B, D and E), but also assessed the quantity of Cap24 in the supernatants and lysates using an ELISA measurement, the quantity of infectious particles using TZM reporter cells, and total viral transcription or more specifically Gag Pr55 transcription using qPCR (Fig. 2F, G and I and Supp. Fig. 2G).

Regarding the quantification of CAp24 at the cell single level, please refer to comment #2 under Reviewer #1.

Knockdown of SNAT7 in MDMs was partial at best; only 30-50% decrease in expression (Fig 2C), but the effects on viral gene expression (Fig. 2I), p24 release and infectious particle production is dramatic (Fig. 2F and G). This discrepancy is not addressed. Does SNAT7 knock-down negatively impact virus particle release? Please note that the representative WB in Fig 2B does not correlate with the quantification in Fig. 2D. There are no p55gag or p24gag bands in SNAT7#1 siRNA condition (Fig. 2B)? Data could also be rearranged to follow the logical sequence of virus replication cycle (viral RNa expression followed by Gag expression, and then release).

We thank the reviewer for this comment. Our samples are indeed a mixture of SNAT7-depleted and non-depleted macrophages and RNA interference in these cells often leads to a decrease of 50 % of the protein expression.

To determine whether SNAT7 is involved in the release of particles, we quantified Cap24 in cell lysates and in the cell culture medium separately, and normalized the results to the total protein content. The absence of SNAT7 reduced the amount of Cap24 measured by ELISA in both samples to the same extent, showing that there is no storage of Cap24-positive viral particles inside the infected macrophages. These data were initially pooled in one graph (Fig. 2F), but separate graphs are now provided in new Supp. Fig. 2 E, F.

Regarding the western blot shown in Fig. 2B, please refer to comment #5 under Reviewer #1.

In the new version of the manuscript, we arranged the figures and placed the later stages of the viral cycle in Fig. 2 and the earlier stages, such as fusion, reverse transcription and transcription, in Fig. 3.

Data interpretation would be greatly improved by including infection controls (RT or integrase inhibitors) to confirm that measurements of viral RNA and Gag are indeed modulated by SNAT7 expression.

We thank the reviewer for this suggestion to include inhibitors of viral replication as controls. In our experiments, cells were Mock-infected in parallel as a negative control of viral detection. We provide the results in the new version of the manuscript to show that (i) there is no detection of viral or Gag RNA in the absence of the virus, (ii) the expression of viral genes measured in HIV-1-infected SNAT7-depleted cells is not different from Mock-infected cells, indicating almost complete inhibition of viral transcription (Fig. 3H and Supp. Fig. 3B), also confirmed at the protein level (Fig. 2B, D-F).

Figure 3: Decrease in SNAT7 expression in macrophages resulted in lower levels of early reverse transcripts. But surprisingly, LRT levels were not as affected by decreases in SNAT7 expression. The authors go on to suggest that decreases in early RT are due to loss of phospho-SAMHD1 and increases in catalytically active form of SAMHD1. Mechanistically this does not make sense: LRT should be similarly affected by increase in catalytically active SAMHD1. dNTP concentrations should be measured to determine if the rescue of RT is dependent on SAMHD1 dNTPase activity.

We thank the reviewer for this comment. LRT concentrations are very low in human macrophages and more challenging to detect than ERT concentrations. This might explain why the differences observed between the SNAT7-depleted and control conditions appear less pronounced for LRT than for ERT.

Furthermore, we cannot rule out the possibility that SNAT7 has a cumulative effect throughout the viral cycle. While reverse transcription remains statistically unaltered, and despite the reduced levels of ERT and LRT in SNAT7-depleted macrophages (Fig. 3 F, G), there is a significant impact on the transcription of viral RNAs (Fig. 2I) and Gag (Supp. Fig. 2G). This step may also be altered by the ribonuclease activity of SAMHD1 (Beloglazova et al., 2013; Ryoo et al., 2014).

Finally, with the help of Dr Baek Kim in Atlanta, we attempted to quantify dNTP concentrations in our human macrophages. Unfortunately, it was not possible to draw any conclusions, as the concentrations of dNTPs extracted from our cells were far too low.

Furthermore, it should be noted that SAMHD1 viral restriction through its phosphorylation at T592 is not correlated with its dNTPase activity (Welbourn et al., 2013; White et al., 2013), but with its ribonuclease activity (Beloglazova et al., 2013; Ryoo et al., 2014). This is supporting why SNAT7, by modulating the ribonuclease activity of SAMHD1, could have a greater effect on viral transcription than on reverse transcription.

There is lack of consistency in the data: p24 release upon SNAT7 depletion is highly variable. While there is a dramatic >90-95% decrease in p24 release (Fig. 2G), the effects are much more moderate in Fig. 4H (50-60% attenuation), even though siRNA-mediated depletion was similar across the data sets. The authors should comment on the variability in their findings.

We thank the reviewer for this comment, but believe that Figure 2E rather than Figure 2G is to be mentioned regarding the quantification of CAp24 by Western blot and to be compared with Figure 4H.

In Fig. 2E, we observed an average reduction of 85 % in CAp24 expression normalized to Clathrin HC expression across different donors for both siRNAs targeting SNAT7. For Fig. 4H, there was a 73 % reduction in CAp24 levels for siRNA #1 and a 56 % reduction for siRNA #2. In addition, it should be noted that the reduction in Gag levels is greater in Fig. 4G (between 77 % and 83 %) than in Fig. 2D (between 55 % and 72 %).

Therefore, there is some variation in the results obtained with the different donors, which could be explained by variations in Gag cleavage among donors, but this does not impact the conclusions for both figures.

SNAT7 is postulated to affect 2 steps in the virus life cycle: reverse transcription and viral transcription. But Vpx-mediated SAMHD1 degradation reversed both. Its not clear to me as to how SAMHD1 degradation impacts the role of SNAT7 in viral transcription. No explanation is provided.

We thank the reviewer for this comment. As suggested, we will perform experiments to assess the impact of Vpx-mediated SAMHD1 degradation on viral transcription.

Exogenous addition of glutamine only partially restored Gag synthesis and p24 release, which could be attributed to increased cytoplasmic levels and viral protein synthesis. What about effects on reverse transcription and viral gene expression?

We thank the reviewer for this comment. We will perform the suggested experiments to assess the impact of glutamine supplementation on viral transcription.

Reviewer #2 (Significance (Required)):

This is a novel finding, as there are limited number of studies on amino acid transporters and HIV-1 replication enhancement in macrophages. Most of the previous work has focused on CD4 T cells. These studies on SNAT7 and HIV-1 infection establishment in macrophages might better inform the influences of macrophage metabolism on HIV-1 persistence and inflammatory responses.

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

This study investigates the role of the lysosomal glutamine transporter SLC38A7/SNAT7 in HIV‑1 replication in primary human macrophages. The authors demonstrate that SNAT7 is highly expressed in macrophages and upregulated upon HIV‑1 infection. They show that SNAT7 depletion inhibits HIV‑1 production at the reverse transcription step without affecting viral fusion or global cellular translation/transcription. Mechanistically, SNAT7 knockdown reduces the inhibitory phosphorylation of SAMHD1 at T592, and degradation of SAMHD1 by Vpx fully rescues viral replication. Extracellular glutamine supplementation partially restores HIV‑1 production in SNAT7‑deficient cells. Overall, the authors report interesting observations; however, the mechanistic investigation remains preliminary, raising concerns about whether the data fully support all the conclusions drawn. Major Concerns： 1. The mechanistic depth is insufficient. The authors do not elucidate how glutamine regulates SAMHD1 T592 phosphorylation, whether through metabolite‑mediated control of kinases/phosphatases or via indirect effects.

We thank the reviewer for this comment. It is worth noting that (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity using drugs decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This is now further discussed in the discussion section of the manuscript.

The authors do not measure intracellular dNTP levels upon SNAT7 knockdown, which is the key functional substrate of SAMHD1. They also do not directly demonstrate that glutamine supplementation restores dNTP pools.

We thank the reviewer for this comment. Please, refer to comment #5 under Reviewer #2.

Extracellular glutamine only partially rescues viral production, implying the existence of transport‑independent functions of SNAT7 or additional pathways. This important observation is not discussed.

We thank the reviewer for this comment. The discussion has been modified accordingly.

It is suggested that the key findings be validated in immortalized THP‑1 cells differentiated into macrophage‑like cells by PMA.

We thank the reviewer for this suggestion but don’t really understand why this would strengthen our conclusions. Indeed, despite the known variability between donors and technical limitations to transduce cells, we chose human blood monocyte-derived macrophages as a relevant non-transformed model for HIV-1 infection of macrophages. They also represent to some extent the human diversity.

The Discussion section should be expanded to include the potential translational implications and limitations of the present study.

We thank the reviewer for this comment. The discussion points to some elements of potential translation and limitations of the study.

Reviewer #3 (Significance (Required)):

General assessment: This study identifies the lysosomal glutamine transporter SLC38A7/SNAT7 as a novel host dependency factor for HIV‑1 replication in primary human macrophages. The major strengths include the use of physiologically relevant primary macrophage models, a well-organized experimental pipeline from expression profiling to functional validation, and the establishment of a link between SNAT7, glutamine metabolism, and the HIV restriction factor SAMHD1.

Advance: It extends current understanding of HIV‑1 host dependency factors and immunometabolism by revealing a compartment‑specific metabolic pathway that supports viral reverse transcription.

Audience:This work will primarily interest specialized researchers in HIV‑1 biology, host-virus interactions, restriction factors, and antiviral innate immunity.

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

This study from the Niedergang lab establishes SNAT7 as a host-dependency factor in human macrophages that supports HIV-1 replication. They show a modest increase in SNAT7 levels HIV-1 infected macrophages and suggest that SNAT7 levels are transiently increased. Employing siRNA against SNAT7 they show reduction in HIV-1 protein levels and viral RNAs and claim that there is a block of reverse transcription in SNAT7 KD cells. Focusing on a known HIV-1 restriction factor in macrophages, SAMHD1, they interconnect the SNAT7 depletion with a reduction in phosphorylated, i.e. catalytical inactive SAMHD1 arguing that SNAT7 regulates the phosphorylation and thereby antiviral activity of SAMHD1. Since SNAT7 is a glutamine transporter that provides this AA from lysosomes, they lastly supplement glutamine and this somehow rescues the reduction of HIV-1 production in SNAT7 KD cells.

Major comments:

The strength of this manuscript is the clear focus on primary human macrophages that are HIV-1 infected and the interconnection of HIV-1 replication to the SNAT7 siRNA KD experiments in combination with SAMHD1 depletion and lastly glutamine supplementation. This establishes a stringent and coherent story line. The effects reported are modest; high variability is not a problem since using primary hMDM this is expected and can be addressed by testing several donors and applying stringent statistics.

1. Having said so, I realize that while they give information on the statistical test used, i.e. one-way ANOVA they miss to explain the post-test used to assess significance (i.e. Bonferroni, Fishers LSD, whatsoever). Please add this information.

We thank the reviewer for this comment. The figure legends have been updated to include more details of all the statistical tests used.

1. Another issue that might underestimate the effects of HIV-1 infection on SNAT7 levels and vice versa of SNAT7 KD on HIV-1 replication is the non-single cell approach employed, i.e. WBlots. I assume that HIV-1 infection rates in macrophages are not super high, usually not exceeding 20-30%. So indeed the effects the authors observe could be much higher, when checking at the single cell level. I do not know about the SNAT7 ab, but all the other reagents should work via flow cytometry and could hence improve the readout a lot.

We agree with the reviewer and indeed, in previous studies on HIV-1 infection of human macrophages performed in the lab, we observed via immunofluorescence that the proportion of infected cells ranged from 20 to 40 %. At the time of submission, we did not have the possibility to label the native SNAT7 protein by immunofluorescence, as the commercial antibody used only works for western blotting.

In the meantime, we have been validating a new antibody (Proteintech) targeting SNAT7 for immunofluorescence. If this is confirmed, we will be able to detect and quantify HIV-1 p24 by immunofluorescence in SNAT7-depleted human macrophages and control cells, thus confirming our results in single-cell analysis.

Flow cytometry analyses are difficult to perform on primary human macrophages because these cells are highly adherent and must be detached first. The process induces significant cell death and damage. This is why we would prefer to carry out these analyses using immunofluorescence and microscopy on adhered cells. This option will be undoubtedly pursued.

1. Furthermore the authors never commented about a dose-response effect in terms of HIV-1 infection levels. There is a MOI dependency described for Suppl.Fig.1 C-F, unfortunately the data is missing in the manuscript.

We apologize for this omission. The figures showing the increase in SNAT7 protein expression following HIV-1 infection at MOIs ranging from 0.05 to 0.5 were added to the new version of the manuscript (Supp. Fig. 1 C-F).

1. Figure1: specify circulating T lymphocytes. I would expect to see levels of SNAT7 in PHA or CD3/CD28 activated lymphocytes versus resting T cells and a time course of SNAT7 levels upon activation. I think even though SNAT7 levels in T cells might be low, they could also be increased by HIV-1 infection and it is essential that the authors test for this. If not, the result is a valid negative control. For this they should employ HIV-1 primary strains with a tropism for T cells, or at least lab-adapted HIV-1 NL4-3

We thank the reviewer for this comment. Circulating T lymphocytes isolated from the blood of healthy donors are now referred to resting lymphocytes in the new version of the manuscript, as opposed to activated T lymphocytes stimulated with IL2 and PHA-P for several days (Fig. 1 A-C).

The expression levels of SNAT7, both at the gene and protein levels, are lower in resting or IL2/PHA-P-activated T cells than in macrophages from the same donors. As suggested, we will perform a kinetic of T-cell activation upon HIV-1 infection to investigate how SNAT7 expression varies in these conditions.

1. Figure 2 again single cell measurements could reveal much more pronounced effects; it is a bit counterintuitive that siRNA #2 is more efficient in SNAT7 KD but has higher levels of HIV-1 replication in terms of Gag levels. I assume when looking at the stats it is always a comparison to the Ctl treated cells (C-G), but this is not entirely clear. Unify labeling as compared to the stats in Fig.2 I (this also applies for all the other figs).

We thank the reviewer for this comment. Fig. 2B indeed shows one of the different donors analyzed. However, protein quantification across six different donors shows that SNAT7 is more depleted with siRNA #2 (Fig. 2C), and that Gag Pr55 protein levels are consequently more reduced, than with siRNA #1 (Fig. 2D).

We use GraphPad Prism software to perform statistical analysis. Depending on the test used, the software automatically plots the comparison bar and displays the p-value above it. We changed the representation of statistics as suggested.

Figure 3: It is a bit odd that they finally conclude on RT as essential step that is reduced in the absence of SNAT7 and then they fail to provide statistical significance for this (Fig.3 panels F and G). One would expect that RT is much more affected given the huge effects on HIV-1 capsid and particle production shown in Fig.2 F, G and I.

The reviewer is right in pointing that we observed a stronger effect during the later stages of the viral cycle, from transcription of viral RNAs (Fig. 2I and Supp. Fig. 2G) to the production of viral particles in the supernatant (Fig. 2D-G), than during the earlier stage of reverse transcription (Fig. 3F, G). Also, it is also possible that we might have missed the peak in ERT/LRT production, which is transient.

It should be noted that SAMHD1 exhibits both dNTPase (Goldstone et al., 2011) and nuclease (Beloglazova et al., 2013) activities. The ability of SAMHD1 to restrict the virus, through dephosphorylation at T592, is mediated by its RNase activity (Ryoo et al., 2014), and not by the dNTPase activity (Welbourn et al., 2013; White et al., 2013).This could explain why SNAT7 exhibit a stronger impact on viral transcription than on reverse transcription.

Figure 4; again single cell flow measurements of SAMHD1, pSAMHD1 and p24 /SNAT7 might help to more clearly discriminate effects that are specifically induced upon infection or happen in virally infected cells. Maybe alternatively IF?

We thank the reviewer for this suggestion. As mentioned under comment #2, flow cytometry analyses are difficult to perform on strongly adherent primary human macrophages.

With regard to immunofluorescence, there is a technical limitation based on the species in which the antibodies are produced. The antibody that targets the native SNAT7 protein, which is currently being validated in our laboratory, is produced in rabbits. An anti-CAp24 antibody produced in goats can be used. It will then be necessary to co-label the cells with anti SAMHD1 and phospho-SAMHD1produced in mouse. We will try to find options to co-label the cells.

The wblot shown in panel D does not really reflect the point the authors want to make by the quantification in panels G-I. Primary data (D) suggests that SNAT7 KD reduces HIV-1 production even in the absence of SAMHD1. The quantification rather indicates that SNAT7 KD does not affect HIV-1 production in the absence of SAMHD1. This needs clarification/corroboration by orthogonal approaches.

We respectfully disagree with the reviewer.

Figure 4D shows a representative blot of the six donors analysed. As mentioned, the depletion of SNAT7 in the absence of SAMHD1 reduces the production of the viral proteins GagPr55 and CAp24 (see Fig. 4D). This is illustrated by the quantifications (Fig. 4G–I). Following treatment with Vpx, GagPr55 protein expression in SNAT7 KD macrophages is reduced by a factor of 2.6 for siRNA #1 (mean = 1.48, light grey bar) and by a factor of 1.83 for siRNA #2 (mean = 2.13, orange bar), compared to the control (mean = 3.9, pink bar) (Fig. 4G). Similarly, CAp24 protein expression was reduced by a factor of 2.2 for siRNA #1 (mean = 2.05, light grey bar) and by a factor of 1.36 for siRNA #2 (mean = 3.34, orange bar), compared to the control (mean = 4.52, pink bar) (Fig. 4H).

These differences are therefore consistent between the Western blot and the quantifications. However, they are not significantly different to those observed in cells treated with Vpx and depleted with control siRNA, suggesting that the viral restriction observed in SNAT7 KD cells is primarily due to SAMHD1.

1. Figure 5: show SAMHD1 and pSAMHD1 levels upon glutamine supplementation.

We thank the reviewer for this comment, we will perform the suggested experiment.

1. I think the discussion is very thin, mainly summarizing the results; but fails to give broader context or critically discuss the limitations and further directions.

We thank the reviewer for this comment. The discussion will be modified further accordingly.

Looking at the data as a whole, I think the results support a modest functional importance of SNAT7 for HIV-1 production in macrophages. I acknowledge that the experiments in primary macrophages are prone to high variability in different donors and the authors transparently depicted their data. However clearly, I would advice the authors to tune down the extend in which they claim SNAT7-dependency given this huge variability and the sometimes-borderline statistics. We respectfully disagree with the reviewer.

The cells used here imply greater variability than a cell line, but are also more relevant.

Indeed, the effects observed in the late stages of HIV-1 production are:

• ~80 % decrease in viral transcription compared to the control (Fig. 2I),

• ~85 % decrease in CAp24 protein expression compared to the control, as quantified by western blot (Fig. 2E), or ~90 % by ELISA measurement (Fig. 2F),

• a reduction of more than 90 % in the release of infectious particles (Fig. 2G).

These results were all significant across donors, while SNAT7 depletion was always partial (Fig. 2C, between 31 to 62 % of depletion compared to the control in infected cells).

Therefore, the data were obtained from a mixture of depleted and non-depleted macrophages. This means that the results may be underestimated.

Together, our results show that SNAT7 is necessary for HIV-1 production.

However, reading the comments, we realized that our conclusions regarding reverse transcription were too strong. SNAT7 depletion does not affect viral fusion and reverse transcription. The manuscript was modified accordingly.

On top, there are a lot of optional experiments I am sure the authors are aware of that should be done at least in the future.

For instance, how does HIV-1 upregulate SNAT7, is a viral accessory protein involved? What is the mechanism of SNAT7 dependent SAMHD1 phosphorylation? Does SNAT7 (or glutamine) regulate the activity of the SAMHD1 associated kinase / phosphatase) If so, does this impact on other targets of these enzymes? We thank the reviewer for these questions.

To address the role of accessory viral proteins, we have already performed one experiment infecting hMDM with HIV-1 strains deleted for genes such as Nef, Vpr, Vpu and Vif, and have found no clear effect on SNAT7 protein expression compared to WT strains. As an alternative experiment, we could overexpress individual viral genes, such as Nef or Vpr, in HeLa cells and analyze their impact on SNAT7 expression by Western blot.

It is also possible that SNAT7 expression and recycling of lysosomal glutamine are modulated by the macrophage intrinsic immunity in response to HIV-1 infection.

The Thr592 motif of the SAMHD1 protein is phosphorylated by Cyclin A2/CDK1 and type 1 IFN in non-cycling cells, such as MDMs (Cribier et al., 2013). For now, the relationship between SNAT7 and SAMHD1 remains unclear. However, (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This has been added to the discussion to explain the relationship between the 3 partners.

**Referees cross-commenting** I think the comments from the other referees are reasonable and consistent with my assessment

Reviewer #1 (Significance (Required)):

Strength and limitations see above;

Significance: I think this work is of high interest for virologists working in the field of HIV-1 and infection of myeloid cells. In case SNAT7 (and hence glutamine) indeed regulates the phosphorylation of SAMHD1, there could potentially be broad relevance of this work. However unfortunately, this aspect remains underdeveloped and is also not discussed

Field of expertise: HIV-1, immunology, cell biology

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

In this report, Herit and colleagues describe the role of a HIV-1 dependency factor that promotes virus replication in macrophages. The authors suggest that the lysosomal membrane-associated SNAT7 glutamine transporter is a HIV dependency factor, that promotes virus replication by enhancing reverse transcription and Gag synthesis. The authors use transient knock-down approaches in primary macrophages to identify that SNAT7 depletion does not impact viral entry but inhibits early reverse transcription which was reversed by exogenous glutamine addition. While reverse transcription enhancement was likely due to selective increase in phosho-SAMHD1 expression, mechanisms by which SNAT7 enhanced viral gene expression were not clearly defined. These are well-controlled studies that pinpoint the role of SNAT7 in the early steps of viral life cycle and highlight the intricate interplay between macrophage metabolism and HIV-1 replication. While the question that is addressed is important, and the hypothesis overall sound, the data presented needs to be strengthened to support the conclusions. There are numerous weaknesses in data interpretation as well.

1. Figure 1: SNAT7 expression was selectively enhanced upon differentiation of monocytes into macrophages but absent in CD4+ T cells. Though there is a claim of enhancement of SNAT7 expression upon HIV-1 infection of macrophages, RT-qPCR analysis shows the opposite trend (Fig 1E) and SNAT7 protein expression changes are modest. Statistical analysis in Fig. 1H needs to be revisited. The number of replicates vary for the lysates harvested at different day post infection, which might have an impact on the statistical test. To determine if SNAT7 expression enhancement is dependent on establishment of virus infection, as the authors imply, control lysates of virus infections in presence of replication inhibitors should be included.

We thank the reviewer for this comment. Indeed, there is a modest, but statistically significant increase in SNAT7 protein expression upon HIV-1 infection over time (Fig. 1G, H), without any modulation of SNAT7 gene expression (Fig. 1E). This indicates that the regulation of SNAT7 expression in this context is only at the translation level (i.e. increase of translation or stabilization of the SNAT7 protein).

As mentioned, Fig. 1H aggregates between 3 to 7 independent experiments on different donors depending on the infection time point. SNAT7 protein expression is increased already at 1 day post-infection and until 8 days. The statistical test used here, i.e. 2 way-ANOVA, compared Mock-infected and HIV-1-infected condition for each time point with the same number of donors. In this figure, the comparison is statistically different only at day 6 of the time course (7 donors). We agree that increasing the number of donors of the other time points could help to improve the statistical difference between control and infection condition.

We thank the reviewer for the suggestion mentioning the use of replication inhibitors in this experiment. We plan to use inhibitors of reverse transcription (Nevirapin) and integration (Dolutegravir).

The authors rely exclusively on western blot analysis for HIV-1 Gag expression in cell lysates as a measure of effects of SNAT7 on virus replication. Single cell analysis such as intracellular p24gag analysis by FACS should be included; this will provide a better measure of effects of SNAT7 onHIV-1 infection establishment.

We respectfully disagree with the reviewer for this question. Indeed, to evaluate the effects of SNAT7 on HIV-1 replication, we measured Gag Pr55 and Cap24 using a Western blot approach (Fig. 2B, D and E), but also assessed the quantity of Cap24 in the supernatants and lysates using an ELISA measurement, the quantity of infectious particles using TZM reporter cells, and total viral transcription or more specifically Gag Pr55 transcription using qPCR (Fig. 2F, G and I and Supp. Fig. 2G).

Regarding the quantification of CAp24 at the cell single level, please refer to comment #2 under Reviewer #1.

Knockdown of SNAT7 in MDMs was partial at best; only 30-50% decrease in expression (Fig 2C), but the effects on viral gene expression (Fig. 2I), p24 release and infectious particle production is dramatic (Fig. 2F and G). This discrepancy is not addressed. Does SNAT7 knock-down negatively impact virus particle release? Please note that the representative WB in Fig 2B does not correlate with the quantification in Fig. 2D. There are no p55gag or p24gag bands in SNAT7#1 siRNA condition (Fig. 2B)? Data could also be rearranged to follow the logical sequence of virus replication cycle (viral RNa expression followed by Gag expression, and then release).

We thank the reviewer for this comment. Our samples are indeed a mixture of SNAT7-depleted and non-depleted macrophages and RNA interference in these cells often leads to a decrease of 50 % of the protein expression.

To determine whether SNAT7 is involved in the release of particles, we quantified Cap24 in cell lysates and in the cell culture medium separately, and normalized the results to the total protein content. The absence of SNAT7 reduced the amount of Cap24 measured by ELISA in both samples to the same extent, showing that there is no storage of Cap24-positive viral particles inside the infected macrophages. These data were initially pooled in one graph (Fig. 2F), but separate graphs are now provided in new Supp. Fig. 2 E, F.

Regarding the western blot shown in Fig. 2B, please refer to comment #5 under Reviewer #1.

In the new version of the manuscript, we arranged the figures and placed the later stages of the viral cycle in Fig. 2 and the earlier stages, such as fusion, reverse transcription and transcription, in Fig. 3.

Data interpretation would be greatly improved by including infection controls (RT or integrase inhibitors) to confirm that measurements of viral RNA and Gag are indeed modulated by SNAT7 expression.

We thank the reviewer for this suggestion to include inhibitors of viral replication as controls. In our experiments, cells were Mock-infected in parallel as a negative control of viral detection. We provide the results in the new version of the manuscript to show that (i) there is no detection of viral or Gag RNA in the absence of the virus, (ii) the expression of viral genes measured in HIV-1-infected SNAT7-depleted cells is not different from Mock-infected cells, indicating almost complete inhibition of viral transcription (Fig. 3H and Supp. Fig. 3B), also confirmed at the protein level (Fig. 2B, D-F).

Figure 3: Decrease in SNAT7 expression in macrophages resulted in lower levels of early reverse transcripts. But surprisingly, LRT levels were not as affected by decreases in SNAT7 expression. The authors go on to suggest that decreases in early RT are due to loss of phospho-SAMHD1 and increases in catalytically active form of SAMHD1. Mechanistically this does not make sense: LRT should be similarly affected by increase in catalytically active SAMHD1. dNTP concentrations should be measured to determine if the rescue of RT is dependent on SAMHD1 dNTPase activity.

We thank the reviewer for this comment. LRT concentrations are very low in human macrophages and more challenging to detect than ERT concentrations. This might explain why the differences observed between the SNAT7-depleted and control conditions appear less pronounced for LRT than for ERT.

Furthermore, we cannot rule out the possibility that SNAT7 has a cumulative effect throughout the viral cycle. While reverse transcription remains statistically unaltered, and despite the reduced levels of ERT and LRT in SNAT7-depleted macrophages (Fig. 3 F, G), there is a significant impact on the transcription of viral RNAs (Fig. 2I) and Gag (Supp. Fig. 2G). This step may also be altered by the ribonuclease activity of SAMHD1 (Beloglazova et al., 2013; Ryoo et al., 2014).

Finally, with the help of Dr Baek Kim in Atlanta, we attempted to quantify dNTP concentrations in our human macrophages. Unfortunately, it was not possible to draw any conclusions, as the concentrations of dNTPs extracted from our cells were far too low.

Furthermore, it should be noted that SAMHD1 viral restriction through its phosphorylation at T592 is not correlated with its dNTPase activity (Welbourn et al., 2013; White et al., 2013), but with its ribonuclease activity (Beloglazova et al., 2013; Ryoo et al., 2014). This is supporting why SNAT7, by modulating the ribonuclease activity of SAMHD1, could have a greater effect on viral transcription than on reverse transcription.

There is lack of consistency in the data: p24 release upon SNAT7 depletion is highly variable. While there is a dramatic >90-95% decrease in p24 release (Fig. 2G), the effects are much more moderate in Fig. 4H (50-60% attenuation), even though siRNA-mediated depletion was similar across the data sets. The authors should comment on the variability in their findings.

We thank the reviewer for this comment, but believe that Figure 2E rather than Figure 2G is to be mentioned regarding the quantification of CAp24 by Western blot and to be compared with Figure 4H.

In Fig. 2E, we observed an average reduction of 85 % in CAp24 expression normalized to Clathrin HC expression across different donors for both siRNAs targeting SNAT7. For Fig. 4H, there was a 73 % reduction in CAp24 levels for siRNA #1 and a 56 % reduction for siRNA #2. In addition, it should be noted that the reduction in Gag levels is greater in Fig. 4G (between 77 % and 83 %) than in Fig. 2D (between 55 % and 72 %).

Therefore, there is some variation in the results obtained with the different donors, which could be explained by variations in Gag cleavage among donors, but this does not impact the conclusions for both figures.

SNAT7 is postulated to affect 2 steps in the virus life cycle: reverse transcription and viral transcription. But Vpx-mediated SAMHD1 degradation reversed both. Its not clear to me as to how SAMHD1 degradation impacts the role of SNAT7 in viral transcription. No explanation is provided.

We thank the reviewer for this comment. As suggested, we will perform experiments to assess the impact of Vpx-mediated SAMHD1 degradation on viral transcription.

Exogenous addition of glutamine only partially restored Gag synthesis and p24 release, which could be attributed to increased cytoplasmic levels and viral protein synthesis. What about effects on reverse transcription and viral gene expression?

We thank the reviewer for this comment. We will perform the suggested experiments to assess the impact of glutamine supplementation on viral transcription.

Reviewer #2 (Significance (Required)):

This is a novel finding, as there are limited number of studies on amino acid transporters and HIV-1 replication enhancement in macrophages. Most of the previous work has focused on CD4 T cells. These studies on SNAT7 and HIV-1 infection establishment in macrophages might better inform the influences of macrophage metabolism on HIV-1 persistence and inflammatory responses.

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

This study investigates the role of the lysosomal glutamine transporter SLC38A7/SNAT7 in HIV‑1 replication in primary human macrophages. The authors demonstrate that SNAT7 is highly expressed in macrophages and upregulated upon HIV‑1 infection. They show that SNAT7 depletion inhibits HIV‑1 production at the reverse transcription step without affecting viral fusion or global cellular translation/transcription. Mechanistically, SNAT7 knockdown reduces the inhibitory phosphorylation of SAMHD1 at T592, and degradation of SAMHD1 by Vpx fully rescues viral replication. Extracellular glutamine supplementation partially restores HIV‑1 production in SNAT7‑deficient cells. Overall, the authors report interesting observations; however, the mechanistic investigation remains preliminary, raising concerns about whether the data fully support all the conclusions drawn. Major Concerns： 1. The mechanistic depth is insufficient. The authors do not elucidate how glutamine regulates SAMHD1 T592 phosphorylation, whether through metabolite‑mediated control of kinases/phosphatases or via indirect effects.

We thank the reviewer for this comment. It is worth noting that (Meng et al., 2022) demonstrated that SNAT7 positively regulates mTORC1 activity at the lysosomal membrane through release of lysosomal glutamine, and (Dias et al., 2024) showed that inhibiting mTORC1 activity using drugs decreases SAMHD1 Thr592 phosphorylation in hMDM. Therefore, we could speculate that the absence of SNAT7 down-regulates mTORC1 activity, which then leads to decreased SAMHD1 phosphorylation. This is now further discussed in the discussion section of the manuscript.

The authors do not measure intracellular dNTP levels upon SNAT7 knockdown, which is the key functional substrate of SAMHD1. They also do not directly demonstrate that glutamine supplementation restores dNTP pools.

We thank the reviewer for this comment. Please, refer to comment #5 under Reviewer #2.

Extracellular glutamine only partially rescues viral production, implying the existence of transport‑independent functions of SNAT7 or additional pathways. This important observation is not discussed.

We thank the reviewer for this comment. The discussion has been modified accordingly.

It is suggested that the key findings be validated in immortalized THP‑1 cells differentiated into macrophage‑like cells by PMA.

We thank the reviewer for this suggestion but don’t really understand why this would strengthen our conclusions. Indeed, despite the known variability between donors and technical limitations to transduce cells, we chose human blood monocyte-derived macrophages as a relevant non-transformed model for HIV-1 infection of macrophages. They also represent to some extent the human diversity.

The Discussion section should be expanded to include the potential translational implications and limitations of the present study.

We thank the reviewer for this comment. The discussion points to some elements of potential translation and limitations of the study.

Reviewer #3 (Significance (Required)):

General assessment: This study identifies the lysosomal glutamine transporter SLC38A7/SNAT7 as a novel host dependency factor for HIV‑1 replication in primary human macrophages. The major strengths include the use of physiologically relevant primary macrophage models, a well-organized experimental pipeline from expression profiling to functional validation, and the establishment of a link between SNAT7, glutamine metabolism, and the HIV restriction factor SAMHD1.

Advance: It extends current understanding of HIV‑1 host dependency factors and immunometabolism by revealing a compartment‑specific metabolic pathway that supports viral reverse transcription.

Audience:This work will primarily interest specialized researchers in HIV‑1 biology, host-virus interactions, restriction factors, and antiviral innate immunity.

2.15.1.0

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Referee #3

Evidence, reproducibility and clarity

This study investigates the role of the lysosomal glutamine transporter SLC38A7/SNAT7 in HIV‑1 replication in primary human macrophages. The authors demonstrate that SNAT7 is highly expressed in macrophages and upregulated upon HIV‑1 infection. They show that SNAT7 depletion inhibits HIV‑1 production at the reverse transcription step without affecting viral fusion or global cellular translation/transcription. Mechanistically, SNAT7 knockdown reduces the inhibitory phosphorylation of SAMHD1 at T592, and degradation of SAMHD1 by Vpx fully rescues viral replication. Extracellular glutamine supplementation partially restores HIV‑1 production in SNAT7‑deficient cells. Overall, the authors report interesting observations; however, the mechanistic investigation remains preliminary, raising concerns about whether the data fully support all the conclusions drawn.

Major Concerns

1. The mechanistic depth is insufficient. The authors do not elucidate how glutamine regulates SAMHD1 T592 phosphorylation, whether through metabolite‑mediated control of kinases/phosphatases or via indirect effects.
2. The authors do not measure intracellular dNTP levels upon SNAT7 knockdown, which is the key functional substrate of SAMHD1. They also do not directly demonstrate that glutamine supplementation restores dNTP pools.
3. Extracellular glutamine only partially rescues viral production, implying the existence of transport‑independent functions of SNAT7 or additional pathways. This important observation is not discussed.
4. It is suggested that the key findings be validated in immortalized THP‑1 cells differentiated into macrophage‑like cells by PMA.
5. The Discussion section should be expanded to include the potential translational implications and limitations of the present study.

Significance

General assessment: This study identifies the lysosomal glutamine transporter SLC38A7/SNAT7 as a novel host dependency factor for HIV‑1 replication in primary human macrophages. The major strengths include the use of physiologically relevant primary macrophage models, a well-organized experimental pipeline from expression profiling to functional validation, and the establishment of a link between SNAT7, glutamine metabolism, and the HIV restriction factor SAMHD1.

Advance: It extends current understanding of HIV‑1 host dependency factors and immunometabolism by revealing a compartment‑specific metabolic pathway that supports viral reverse transcription.

Audience: This work will primarily interest specialized researchers in HIV‑1 biology, host-virus interactions, restriction factors, and antiviral innate immunity.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

In this report, Herit and colleagues describe the role of a HIV-1 dependency factor that promotes virus replication in macrophages. The authors suggest that the lysosomal membrane-associated SNAT7 glutamine transporter is a HIV dependency factor, that promotes virus replication by enhancing reverse transcription and Gag synthesis. The authors use transient knock-down approaches in primary macrophages to identify that SNAT7 depletion does not impact viral entry but inhibits early reverse transcription which was reversed by exogenous glutamine addition. While reverse transcription enhancement was likely due to selective increase in phosho-SAMHD1 expression, mechanisms by which SNAT7 enhanced viral gene expression were not clearly defined. These are well-controlled studies that pinpoint the role of SNAT7 in the early steps of viral life cycle and highlight the intricate interplay between macrophage metabolism and HIV-1 replication. While the question that is addressed is important, and the hypothesis overall sound, the data presented needs to be strengthened to support the conclusions. There are numerous weaknesses in data interpretation as well.

1. Figure 1: SNAT7 expression was selectively enhanced upon differentiation of monocytes into macrophages but absent in CD4+ T cells. Though there is a claim of enhancement of SNAT7 expression upon HIV-1 infection of macrophages, RT-qPCR analysis shows the opposite trend (Fig 1E) and SNAT7 protein expression changes are modest. Statistical analysis in Fig. 1H needs to be revisited. The number of replicates vary for the lysates harvested at different day post infection, which might have an impact on the statistical test. To determine if SNAT7 expression enhancement is dependent on establishment of virus infection, as the authors imply, control lysates of virus infections in presence of replication inhibitors should be included.
2. The authors rely exclusively on western blot analysis for HIV-1 Gag expression in cell lysates as a measure of effects of SNAT7 on virus replication. Single cell analysis such as intracellular p24gag analysis by FACS should be included; this will provide a better measure of effects of SNAT7 onHIV-1 infection establishment.
3. Knockdown of SNAT7 in MDMs was partial at best; only 30-50% decrease in expression (Fig 2C), but the effects on viral gene expression (Fig. 2I), p24 release and infectious particle production is dramatic (Fig. 2F and G). This discrepancy is not addressed. Does SNAT7 knock-down negatively impact virus particle release? Please note that the representative WB in Fig 2B does not correlate with the quantification in Fig. 2D. There are no p55gag or p24gag bands in SNAT7#1 siRNA condition (Fig. 2B)? Data could also be rearranged to follow the logical sequence of virus replication cycle (viral RNa expression followed by Gag expression, and then release).
4. Data interpretation would be greatly improved by including infection controls (RT or integrase inhibitors) to confirm that measurements of viral RNA and Gag are indeed modulated by SNAT7 expression.
5. Figure 3: Decrease in SNAT7 expression in macrophages resulted in lower levels of early reverse transcripts. But surprisingly, LRT levels were not as affected by decreases in SNAT7 expression. The authors go on to suggest that decreases in early RT are due to loss of phospho-SAMHD1 and increases in catalytically active form of SAMHD1. Mechanistically this does not make sense: LRT should be similarly affected by increase in catalytically active SAMHD1. dNTP concentrations should be measured to determine if the rescue of RT is dependent on SAMHD1 dNTPase activity.
6. There is lack of consistency in the data: p24 release upon SNAT7 depletion is highly variable. While there is a dramatic >90-95% decrease in p24 release (Fig. 2G), the effects are much more moderate in Fig. 4H (50-60% attenuation), even though siRNA-mediated depletion was similar across the data sets. The authors should comment on the variability in their findings.
7. SNAT7 is postulated to affect 2 steps in the virus life cycle: reverse transcription and viral transcription. But Vpx-mediated SAMHD1 degradation reversed both. Its not clear to me as to how SAMHD1 degradation impacts the role of SNAT7 in viral transcription. No explanation is provided.
8. Exogenous addition of glutamine only partially restored Gag synthesis and p24 release, which could be attributed to increased cytoplasmic levels and viral protein synthesis. What about effects on reverse transcription and viral gene expression?

Significance

This is a novel finding, as there are limited number of studies on amino acid transporters and HIV-1 replication enhancement in macrophages. Most of the previous work has focused on CD4 T cells. These studies on SNAT7 and HIV-1 infection establishment in macrophages might better inform the influences of macrophage metabolism on HIV-1 persistence and inflammatory responses.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #1

Evidence, reproducibility and clarity

This study from the Niedergang lab establishes SNAT7 as a host-dependency factor in human macrophages that supports HIV-1 replication. They show a modest increase in SNAT7 levels HIV-1 infected macrophages and suggest that SNAT7 levels are transiently increased. Employing siRNA against SNAT7 they show reduction in HIV-1 protein levels and viral RNAs and claim that there is a block of reverse transcription in SNAT7 KD cells. Focusing on a known HIV-1 restriction factor in macrophages, SAMHD1, they interconnect the SNAT7 depletion with a reduction in phosphorylated, i.e. catalytical inactive SAMHD1 arguing that SNAT7 regulates the phosphorylation and thereby antiviral activity of SAMHD1. Since SNAT7 is a glutamine transporter that provides this AA from lysosomes, they lastly supplement glutamine and this somehow rescues the reduction of HIV-1 production in SNAT7 KD cells.

Major comments:

The strength of this manuscript is the clear focus on primary human macrophages that are HIV-1 infected and the interconnection of HIV-1 replication to the SNAT7 siRNA KD experiments in combination with SAMHD1 depletion and lastly glutamine supplementation. This establishes a stringent and coherent story line. The effects reported are modest; high variability is not a problem since using primary hMDM this is expected and can be addressed by testing several donors and applying stringent statistics.

1. Having said so, I realize that while they give information on the statistical test used, i.e. one-way ANOVA they miss to explain the post-test used to assess significance (i.e. Bonferroni, Fishers LSD, whatsoever). Please add this information.
2. Another issue that might underestimate the effects of HIV-1 infection on SNAT7 levels and vice versa of SNAT7 KD on HIV-1 replication is the non-single cell approach employed, i.e. WBlots. I assume that HIV-1 infection rates in macrophages are not super high, usually not exceeding 20-30%. So indeed the effects the authors observe could be much higher, when checking at the single cell level. I do not know about the SNAT7 ab, but all the other reagents should work via flow cytometry and could hence improve the readout a lot.
3. Furthermore the authors never commented about a dose-response effect in terms of HIV-1 infection levels. There is a MOI dependency described for Suppl.Fig.1 C-F, unfortunately the data is missing in the manuscript.
4. Figure1: specify circulating T lymphocytes. I would expect to see levels of SNAT7 in PHA or CD3/CD28 activated lymphocytes versus resting T cells and a time course of SNAT7 levels upon activation. I think even though SNAT7 levels in T cells might be low, they could also be increased by HIV-1 infection and it is essential that the authors test for this. If not, the result is a valid negative control. For this they should employ HIV-1 primary strains with a tropism for T cells, or at least lab-adapted HIV-1 NL4-3
5. Figure 2 again single cell measurements could reveal much more pronounced effects; it is a bit counterintuitive that siRNA #2 is more efficient in SNAT7 KD but has higher levels of HIV-1 replication in terms of Gag levels. I assume when looking at the stats it is always a comparison to the Ctl treated cells (C-G), but this is not entirely clear. Unify labeling as compared to the stats in Fig.2 I (this also applies for all the other figs).
6. Figure 3: It is a bit odd that they finally conclude on RT as essential step that is reduced in the absence of SNAT7 and then they fail to provide statistical significance for this (Fig.3 panels F and G). One would expect that RT is much more affected given the huge effects on HIV-1 capsid and particle production shown in Fig.2 F, G and I.
7. Figure 4; again single cell flow measurements of SAMHD1, pSAMHD1 and p24 /SNAT7 might help to more clearly discriminate effects that are specifically induced upon infection or happen in virally infected cells. Maybe alternatively IF? The wblot shown in panel D does not really reflect the point the authors want to make by the quantification in panels G-I. Primary data (D) suggests that SNAT7 KD reduces HIV-1 production even in the absence of SAMHD1. The quantification rather indicates that SNAT7 KD does not affect HIV-1 production in the absence of SAMHD1. This needs clarification/corroboration by orthogonal approaches.
8. Figure 5: show SAMHD1 and pSAMHD1 levels upon glutamine supplementation.
9. I think the discussion is very thin, mainly summarizing the results; but fails to give broader context or critically discuss the limitations and further directions

Looking at the data as a whole, I think the results support a modest functional importance of SNAT7 for HIV-1 production in macrophages. I acknowledge that the experiments in primary macrophages are prone to high variability in different donors and the authors transparently depicted their data. However clearly, I would advice the authors to tune down the extend in which they claim SNAT7-dependency given this huge variability and the sometimes-borderline statistics.

On top, there are a lot of optional experiments I am sure the authors are aware of that should be done at least in the future. For instance, how does HIV-1 upregulate SNAT7, is a viral accessory protein involved? What is the mechanism of SNAT7 dependent SAMHD1 phosphorylation? Does SNAT7 (or glutamine) regulate the activity of the SAMHD1 associated kinase / phosphatase) If so, does this impact on other targets of these enzymes?

Referees cross-commenting

I think the comments from the other referees are reasonable and consistent with my assessment

Significance

Strength and limitations see above

Significance: I think this work is of high interest for virologists working in the field of HIV-1 and infection of myeloid cells. In case SNAT7 (and hence glutamine) indeed regulates the phosphorylation of SAMHD1, there could potentially be broad relevance of this work. However unfortunately, this aspect remains underdeveloped and is also not discussed

Field of expertise: HIV-1, immunology, cell biology

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

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Reply to the reviewers

1. General Statements We thank all Reviewers for their helpful input that allowed us to significantly improve our study. We acknowledge that the Reviewer's interpretation on the advance of our study was mixed. In our own view, the main advance of this study (relevant to a broader community of scientists interested in epithelial cell biology) is the identification of actin turnover as a spatial regulator of non-centrosomal microtubule organization in epithelial cells in vivo. This conclusion is based on the evidence that microtubules are specifically displaced from the apical cortex upon disruption of CAP-dependent actin turnover, associated with the mislocalization of the actin-microtubule coupling spectraplakin Shot, and partially restored by acute treatment with actin polymerization inhibitor Latrunculin A. While reviewers differed in their assessment of the conceptual advance, the reviews helped us strengthen both the experimental support and interpretation of the findings. In response, we have added new experiments, expanded quantification, and revised several conclusions to provide a more rigorous and balanced account of how CAP-dependent actin turnover contributes to epithelial cytoskeletal organization. Particularly important was the addition of acute Latrunculin A experiments demonstrating rapid and coordinated recovery of apical microtubules and Shot localization following partial disruption of the actin accumulation.

In addition, our study includes advances relevant to a more specific group of scientists working on the regulation of the actin cytoskeleton. These include evidence for the role of CAP in local regulation of apical actin turnover in epithelial cells in vivo, which extends beyond the earlier reported findings of Baum and Perrimon (2001) (PMID: 11584269). Moreover, our study establishes the essential role of the CARP domain of CAP in epithelial actin turnover in animals in vivo, which complements the earlier studies conducted in vitro and in yeast (PMID: 29760438, PMID: 36912152). For more detailed arguments and description, please see below.

1. Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity (Required)): In the manuscript by Babu et al, "Apical actin filament turnover mediated by cyclase-1 associated protein is required for organization of non-centrosomal microtubules in epithelium," the authors investigate how Cyclase-associated protein (CAP) regulates apical actin organization and how this impacts microtubule architecture and apical trafficking in the Drosophila follicular epithelium. CAP depletion leads to accumulation of a dense, Latrunculin-resistant apical F-actin network, accompanied by loss of apical microtubules, mislocalization of vesicular markers (e.g., Rab11, Cad99C, Dynein), defects in microvilli formation, and altered nuclear positioning. Domain-rescue experiments suggest that CAP's nucleotide exchange activity is required for proper actin organization. The study presents a rich set of phenotypic observations and highlights an important interplay between actin turnover, microtubule organization, and epithelial polarity. However, several key mechanistic conclusions are currently not fully supported by the data, and an important conceptual question regarding the spatial specificity of CAP function remains insufficiently addressed.

Response: We thank the reviewer for this thoughtful assessment. We agree that the original version did not sufficiently support the mechanistic conclusions or address the spatial specificity of CAP function. In the revised manuscript, we strengthened quantification and refined our interpretation to distinguish between structural effects of actin accumulation and defects in actin-microtubule coupling, supported by new data regarding Shot redistribution and its dynamic recovery upon Latrunculin A treatment. We also addressed spatial specificity by comparing CAP depletion to Cofilin and Aip1 silencing, which cause global actin accumulation, whereas CAP loss produces a spatially restricted imbalance with apical accumulation and reduced basal actin. These revisions provide a more balanced and experimentally grounded interpretation of both the mechanism and spatial nature of CAP function.

Major Comments 1. Is the CAP function truly apically specific? A central conclusion of the manuscript is that CAP regulates the apical actin cytoskeleton. However, the data do not yet clearly distinguish whether CAP acts in a spatially polarized manner or instead regulates global actin turnover, with apical accumulation emerging as a secondary consequence of epithelial geometry. As CAP appears largely cytoplasmic, it is plausible that its depletion affects actin dynamics throughout the cell. In this scenario, actin accumulation may become most apparent at the apical domain because this region is less occupied by organelles compared to the laterobasal cytoplasm. Thus, the observed phenotype could reflect global dysregulation of actin turnover, rather than a specifically apical mechanism. Importantly, this does not contradict the authors' model but represents an alternative that should be addressed. To clarify this point, the authors should consider: • Quantifying actin distribution across the full apico-basal axis • Testing whether forced relocalization of CAP (e.g., to the basal cortex) alters where actin accumulates • Assessing whether non-apical actin structures are also altered but less apparent Without addressing this, the claim of apical-specific regulation remains insufficiently supported and should be framed more cautiously.

Response: Reviewer raised important conceptual question regarding whether the CAP phenotype reflects spatially specific regulation or a global defect in actin turnover. To directly address this, we performed comparative analyses with depletion of two well-established actin disassembly factors, Cofilin and Aip1. While depletion of either factor resulted in actin accumulation throughout the apico-basal axis (Fig. 1D-I), CAP depletion caused a strikingly confined accumulation at the apical cortex (Fig. 1J-O). To further quantify this distinction, we have now • quantified actin intensity along the apico-basal axis using line-scan analysis (Fig. 1F, I, L, O) • quantified basal actin levels independently (Fig. 1E', H', K', N') These analyses show that, unlike global turnover defects caused by Cofilin and Aip1 depletion, CAP depletion does not result in uniform actin accumulation, but instead produces a spatially restricted imbalance, with accumulation at the apical cortex and reduction elsewhere. These findings argue against a purely global turnover model influenced by epithelial geometry and instead support a model in which CAP loss generates a spatial imbalance in filament turnover, leading to preferential stabilization of apical actin. We agree that forced relocalization of CAP would provide an important additional test of spatial specificity. However, such experiments are technically challenging in this system and were not feasible within the current revision timeline.

1. What is the primary molecular function of cap in this context? While the phenotypic consequences of CAP depletion are well described, the manuscript does not clearly resolve which step of actin turnover is affected. CAP is known to function in actin monomer recycling and cooperate with cofilin, but it remains unclear in this system whether the primary defect reflects: (i) Impaired actin depolymerization, (ii) Reduced monomer recycling or altered filament dynamics or nucleation balance Clarifying this point is important, as it would strengthen the mechanistic link between CAP activity and the observed cellular phenotypes. Even if not directly tested experimentally, this aspect should be more explicitly discussed and, where possible, supported by quantitative analysis of actin dynamics.

Response: Reviewer requested for a clearer mechanistic interpretation of CAP function in this system. While directly isolating individual biochemical steps in vivo is not feasible, several independent lines of evidence consistently point toward a defect in actin filament turnover at the level of disassembly and recycling, rather than increased actin assembly: • The accumulated apical F-actin persists upon Latrunculin A treatment, consistent with reduced turnover (Fig. 6A, B) • The accumulated actin is enriched for Aip1 (Suppl. Fig. 1B), which is known to preferentially associate with Cofilin-decorated actin filaments • Basal actin levels are reduced (Fig. 1N'), consistent with depletion of polymerization-competent ATP-actin monomers Together, these observations support a model (PMID: 29760438, PMID: 36912152) in which actin accumulates because it fails to be efficiently disassembled and recycled, rather than because of increased polymerization. We acknowledge that direct quantitative measurements of actin dynamics (e.g., FRAP) would further strengthen this conclusion. Such experiments were beyond the scope of the current study. Our interpretation is instead based on the increased resistance of apical F-actin to Latrunculin A and the enrichment of Aip1 within the accumulated actin network, both of which are consistent with reduced actin turnover. We agree that interpretation of the CARP domain results requires careful consideration. Because this issue was raised by multiple reviewers, we address it in detail in response to Reviewer #3 (Comment 1). Briefly, we interpret the CARP mutant phenotype as reflecting the failure of the coordinated actin recycling cycle, rather than disruption of a single activity. We have substantially expanded the Discussion to clarify this mechanistic model.

1. Insufficient quantification of actin stability. The conclusion that apical actin is stabilized in CAP mutants is based primarily on qualitative observations of Latrunculin A resistance. While convincing visually, this requires quantitative validation. Measurement of actin intensity under {plus minus} LatA conditions, across multiple samples with proper normalization and statistical analysis, is necessary to substantiate increased actin stability.

Response: We have now performed quantitative analysis of actin intensity in control and Latrunculin A-treated samples across multiple egg chambers (Fig. 6B). These experiments confirm that actin structures in CAP mutant cells are significantly more resistant to depolymerization, supporting the conclusion that they are stabilized.

1. Domain-rescue experiments lack quantification (Fig.2,S2). The conclusion that the CARP domain is required for rescue is based on qualitative comparisons. Given the importance of this experiment for mechanistic interpretation, quantitative analysis of rescue efficiency (e.g., actin intensity, percentage of rescued clones) is essential.

Response: We agree that quantification is essential for interpreting these experiments. We have now quantified apical F-actin intensity across all rescue conditions, including CAP mutant clones, wild-type CAP rescue, and domain-specific mutants (HFD, PP, WH2, CARP) (Fig. 2F-I; Supl.Fig. 2B-E). These data confirm that disruption of the CARP domain specifically prevents rescue, strengthening our conclusion that this activity is critical for maintaining normal actin organization in vivo.

1. Microtubule exclusion model is not directly demonstrated The authors propose that dense apical actin physically excludes microtubules. While the presented data are consistent with this model, they remain correlative. Alternative explanations include: (i) Altered microtubule stability, (ii) Defective nucleation or anchoring or (iii) changes in epithelial polarity affecting microtubule organization. To distinguish between these possibilities, the authors should: • Perform live imaging of microtubule plus ends (e.g., EB1) to assess whether microtubules fail to enter or instead destabilize at the apical region. • Examine whether microtubule polarity or nucleator localization is altered • Increase sample size and quantification for line-scan analyses (Fig. S3) The current interpretation should therefore be presented more cautiously as one of several possible mechanisms.

Response: Reviewer pointed out that the current data do not directly demonstrate steric exclusion and that alternative mechanisms should be considered. In response, we have revised both the Results and Discussion to present a more balanced interpretation. Our data, with new quantitations show that: • Microtubules are reduced at the apical domain, now quantitated (Fig. 5A-C) • Microtubules reappear rapidly following partial actin disruption (Fig. 6A-C) • Microtubule minus-end anchoring is preserved (Patronin, Fig. 5D-F) • Microtubule polarity is maintained (Dynein, Fig. 7J-L) These findings indicate that microtubules are not globally lost, but instead are redistributed and fail to properly occupy the apical domain. In the revised manuscript, we no longer present microtubule exclusion as a single or dominant mechanism, but provide two non-exclusive mechanisms: structural effects, in which dense actin may limit microtubule access, and coupling defects, in which redistribution of Shot alters actin-microtubule interactions. We agree that direct analysis of microtubule growth dynamics would provide important complementary evidence, but such experiments were not feasible within the revision and are now stated as a limitation.

1. Shot redistribution suggests an alternative mechanism (Fig.6). The redistribution of Shot beneath the actin accumulation is a key observation that is currently underexplored. Given that Shot mediates actin-microtubule crosslinking, this finding suggests that disrupted cytoskeletal coupling could underlie microtubule defects. This provides an alternative to the steric exclusion model and should be more fully integrated into the manuscript. The authors should: • Quantify Shot redistribution relative to the apical domain • test whether restoring Shot at the apical cortex rescues microtubule organization • compare effects of Shot versus Patronin manipulation to distinguish crosslinking versus anchoring roles

Response: We agree that the redistribution of Shot is a key observation that was underdeveloped in the original submission. In particular, we agree with the reviewer that this finding raises an important alternative (or complementary) explanation to a purely steric exclusion model. In response, we have substantially expanded this part of the manuscript, both experimentally and conceptually, to directly address this concern. Experimentally, we have strengthened the analysis of Shot localization as follows: • We quantified Shot distribution relative to the apical domain (Fig. 5H), demonstrating a significant reduction at the cortex • We performed line-scan analyses (Fig. 5I), showing that Shot is consistently redistributed beneath the accumulated actin • We expanded the Discussion to compare Shot and Patronin phenotypes described in the literature with the CAP mutant phenotype Importantly, we also addressed whether Shot mislocalization is a consequence of altered actin organization. To this end, we performed Latrunculin A treatment, where partial disruption of the apical actin accumulation leads to re-entry of microtubules into the apical domain (Fig. 6A-C). Our new data shows that under the same conditions, Shot partially redistributes back toward the apical cortex (Fig. 6E-F) The rapid timescale of this response (30 min LatA treatment) indicates that Shot localization is dynamically dependent on the actin network and is not a secondary, long-term effect. Conceptually, we have revised our interpretation in direct response to the reviewer's suggestion. In the revised manuscript, we no longer present microtubule exclusion as a single or dominant mechanism. Instead, we explicitly distinguish between two non-exclusive mechanisms: • Structural effects - dense actin may limit microtubule access • Coupling defects - redistribution of Shot alters actin-microtubule interactions Under this model, microtubules are not simply blocked from entering the apical cortex, but may also fail to be properly captured, stabilized, or guided, due to loss of cortical coupling. We believe this revised interpretation directly addresses the reviewer's concern and integrates the Shot phenotype as a central mechanistic component, rather than a secondary observation. We agree that further experiments-such as targeted manipulation of Shot localization-would provide a more direct test of this model. However, these approaches require new genetic tools and therefore need to be performed in forthcoming studies.

1. Nuclear positioning phenotype is not fully resolved (Fig.7). The explanation that the lack of rescue reflects late expression of the CAP construct is plausible but not experimentally demonstrated. This interpretation should be toned down or explicitly presented as speculative.

Response: We agree that the original manuscript did not sufficiently explain why nuclear positioning is not rescued by CAP re-expression. To address this, we performed additional quantifications of CAP rescue construct expression and cytoskeletal organization during the developmental stages when nuclear positioning is established. We now show that: • CAP rescue constructs exhibit minimal expression during stages 6-7, when nuclear positioning is established (Fig. 4J-K). • During this same developmental window, CAP mutant cells and CAP rescue cells both display apical actin accumulation and altered microtubule organization (Fig. 4D-I). • By stage 10, when CAP expression increases, both the actin and microtubule phenotypes are efficiently rescued. Together, these data provide a plausible explanation for the lack of rescue of the nuclear positioning phenotype. Specifically, CAP activity appears to be required during early oogenesis, when nuclear positioning is established, whereas expression of the rescue construct occurs predominantly at later stages. Consistent with previous work showing that nuclear positioning depends on apically organized microtubules during stages 6-9 (PMID: 23077179), our findings suggest that early defects in actin and microtubule organization are sufficient to disrupt nuclear positioning even if cytoskeletal organization is restored later. We have revised the manuscript accordingly and now present the nuclear positioning phenotype as a consequence of early cytoskeletal defects, while noting that the precise mechanism linking CAP function to nuclear positioning remains to be determined.

Minor comments: 1. Quantification and sample size Many claims rely on representative images and n and N are not reported in such cases. Include quantification and clearly report n and N for all analyses.

Response: We have added quantitative analysis and clearly report n and N throughout all relevant figures.

1. Vesicle exclusion and secretion defects remain indirect (Fig.3) Evidence for vesicle exclusion is based on loss of ER/Golgi markers and altered TEM structures. However, TEM identification of mutant (clones) cells is phenotype-based. The current data are consistent with altered apical trafficking but do not directly demonstrate vesicle exclusion from the actin-rich domain. More direct evidence would require visualization of vesicle dynamics to determine whether they fail to enter, stall at or are redirected from the apical actin accumulation. The current wording should be softened accordingly.

Response: We have modified the wording accordingly. While direct visualization of vesicle dynamics is not provided, our data show consistent marked reduction of multiple markers: mCD8GFP (Fig. 3A-C), ER (Fig. 3E-G), Golgi (Gig.3H-J), Rab11 (Fig. 7G-I), and Dynein (Fig. 7J-L), from the actin-rich domain, supporting the interpretation indirectly.

Reviewer #1 (Significance (Required)): The work provides a strong phenotypic characterization linking CAP depletion to accumulation of a dense, Latrunculin-resistant apical F-actin network, accompanied by defects in microtubule organization, vesicle localization, and epithelial morphology. A key strength is the integration of multiple readouts to connect actin turnover with broader aspects of epithelial organization. The study therefore offers potentially important insight into how actin dynamics can influence cytoskeletal crosstalk and tissue architecture. However, several central conclusions rely on largely qualitative or correlative evidence, and quantitative support is limited in key experiments. In addition, an important conceptual question remains unresolved: whether CAP regulates actin turnover in a spatially polarized (apical-specific) manner or more globally, with apical phenotypes emerging as a consequence of cellular organization. Addressing this distinction, along with strengthening quantification and moderating interpretation of the steric exclusion model, would substantially improve the manuscript. The main advance of the study is functional and conceptual, linking CAP-dependent actin turnover to microtubule organization and apical trafficking in a polarized epithelial context. While CAP is known to regulate actin dynamics, its role in coordinating cytoskeletal organization at the tissue level is less well defined, and this work extends current knowledge in that direction. At present, however, the mechanistic insight remains limited, particularly regarding the specific step in actin turnover affected and the causal relationship between actin, microtubules, and trafficking defects. The study will be of primary interest to a specialized audience in cytoskeleton, epithelial, and developmental biology, with broader relevance to researchers studying actin-microtubule crosstalk and cell polarity.

Response: We thank the reviewer for this thoughtful assessment and recognizing the strengths of the manuscript. In the revised manuscript, we addressed the concerns regarding quantification by incorporating systematic analyses across key experiments and moderating interpretations where appropriate. We also directly addressed the question of spatial specificity by showing that the CAP phenotype differs from global actin turnover defects, supporting a model of spatially biased disruption rather than uniform regulation. Together, these revisions clarify the conceptual advance and provide a more balanced and experimentally supported interpretation of CAP function. We agree that resolving the individual biochemical steps of actin turnover is very challenging in our in vivo model. However, in the revised manuscript we clarify this by framing CAP function at the level of the actin turnover cycle and presenting the CARP phenotype as a defect in coordinated actin recycling, supported by Latrunculin A resistance, enrichment of disassembly-associated factors, and reduced basal actin levels. In addition, we have refined our interpretation of the relationship between actin, microtubules, and trafficking, explicitly considering both direct structural effects of altered actin organization and indirect consequences for cellular organization. Together, these revisions clarify the conceptual advance and provide a more balanced and experimentally supported interpretation of epithelial CAP function. Specifically, our study demonstrates that defects in actin turnover generate spatially restricted cytoskeletal changes that reorganize microtubule positioning and engagement in vivo.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): Babu and colleagues report that clonal loss of Cyclase associated protein (CAP) function results in dramatic accumulation of F-actin in a large cytoplasmic domain below the apical surface of Drosophila egg chamber follicle cells. Rescue experiments confirm the overall role of CAP and show that its function in converting actin-GDP to actin-GTP is critical for preventing the F-actin accumulation. Numerous components of the cell are probed in the mutant clones and are shown to have altered distributions. Microtubules and intracellular membranes are generally excluded from the abnormal F-actin domains, and Latrunculin A treatment partially reversed the microtubule exclusion. Abnormalities in apical microvilli, apicolateral nuclear positioning, and actin binding protein distributions are also reported. In general, the microscopy is quite striking, and the manuscript is clearly written, but the overall advance seems fairly limited and several revisions are needed.

Response: We thank the reviewer for their positive assessment of the microscopy and clarity of the manuscript. We acknowledge that the overall advance should be more clearly articulated. While apical actin accumulation in CAP mutants has been previously described (PMID: 11584269), our study shows that defects in actin turnover can generate spatially restricted cytoskeletal phenotypes, impair microtubule engagement with the apical cortex, and reorganize non-centrosomal microtubules in vivo. Importantly, we show that defects in actin turnover can both limit microtubule access to the apical cortex and alter actin-microtubule coupling through redistribution of the crosslinker Shot, providing a conceptual framework linking local actin dynamics to microtubule organization and epithelial function. Moreover, we show that CARP-domain-dependent actin recycling is required for spatial turnover of actin in an epithelium. We have revised the manuscript to better emphasize these advances and to distinguish our findings from prior work.

Major comments: 1. The authors conclude that the abnormal F-actin accumulations of CAP mutant cells coincide with microtubule cytoskeleton alterations and say that this "suggests that spatially regulated actin filament turnover is important for microtubule organization". Although the conclusion and suggestion are formally true, they don't consider the directness of the relationship. In my view, two possibilities of indirect effects should be included: (1) the general disruption of subcellular organization by the large F-actin accumulation suggests that many indirect effects are possible, and (2) the very high level of F-actin accumulation, and of actin binding protein co-accumulations, without apparent losses from other parts of the cell suggest that the mutant cells have undergone major gene expression changes which could have a range of effects.

Response: The Reviewer raises a concern regarding the extent to which the observed microtubule defects reflect direct consequences of altered actin organization versus indirect effects arising from broader disruption of cellular organization or changes in gene expression. Our study is based on genetic in vivo experiments and due the duration of these experiments, distinguishing between immediate and long-term cellular changes is challenging, as the Reviewer correctly points out. However, we would like to emphasize that our phenotypes show that microtubules are not globally disrupted but instead redistributed locally relative to the actin-rich domain (Fig. 5A-C), while polarity and anchoring remain intact (Fig. 5D-F; Fig. 7J-L). This distinguishes the observed phenotype from general cellular collapse and supports a conclusion of specific reorganization of microtubule-cortex interactions. To further address the Reviewer's concern, we have performed acute (~30 min) Latrunculin A (LatA) treatment experiments to test, how microtubule organization and the localization of actin-microtubule crosslinker Shot corresponds to LatA-mediated changes in actin cytoskeleton. We observed that LatA partially mitigated the accumulation of apical actin in CAP mutant cells (Fig. 6A, B). Concomitantly, microtubules reappeared to the apical domain (Fig. 6A, C) as well as the apical localization of Shot was increased (Fig. 6E, F). Considering the timescale of this experiment, we conclude that it is unlikely to reflect indirect effects, such as reprogramming of gene expression (typically occurring in the scale of hours). In our view, the most parsimonious conclusion is that these acute phenotypic changes reflect a direct structural effect of actin organization on local microtubule formation. Despite these arguments, we cannot fully rule out that long-term cellular adaptations, such as altered organelle distribution or changes in gene expression, are reflected to some of the CAP mutant phenotypes. We have now explicitly acknowledged both possibilities in the revised manuscript.

1. The authors state that the CARP domain of CAP is known to bind ADP-actin monomers and promote ADP-ATP exchange, "thereby recharging actin monomers for polymerization". Of many mutations expected to affect individual domains of CAP, only mutations disrupting the nucleotide exchange activity of the CARP domain failed to rescue the abnormal F-actin accumulations of CAP mutant cells. It was unclear how extreme actin polymerization occurs in cells in which the CAP protein expressed only lacks the ability to recharge actin monomers for polymerization. Minimally, the results of the domain analyses should be addressed in the Discussion section. More analyses/constructs may be needed to confirm whether the mutations listed in Table 1 had their intended effects on CAP domain activities (especially on the activity of the HFD domain implicated in actin depolymerization).

Response: The reviewer raises a concern regarding the apparent contradiction between impaired nucleotide exchange and the observed accumulation of F-actin. We agree that this observation is counterintuitive and requires better clarification. Firstly, we would like to emphasize that our interpretation is not that CAP loss increases actin polymerization. Instead, our interpretation of the experimental finding is that the phenotype likely arises from a defect in actin filament turnover, leading to progressive accumulation of aged, stabilized filaments. This interpretation is based on the following observations: • Accumulated apical actin shows increased resistance to Latrunculin A, indicating reduced filament dynamics (Fig. 6B) • The actin-rich structures are enriched in Aip1 that associate with cofilin-decorated filaments (Supl. Fig. 1B) • Basal actin levels are reduced (Fig. 1N'), consistent with depletion of polymerization-competent ATP-actin Together, these findings argue against excess polymerization and instead support a model in which filaments accumulate because they fail to be efficiently disassembled and recycled. This conclusion supported by existing studies in yeast (PMID: 29760438) and in vitro (PMID: 36912152). Based on the findings reported in Kotila et al., 2019 (PMID: 29760438) the CARP domain mutation used in this study is expected to disrupt both ADP-actin binding and nucleotide exchange. These functions are part of a coordinated and sequential actin turnover cycle. Disruption of this cycle is expected to 1) impair Cofilin release, 2) prevent efficient processing of disassembly products, and 3) block regeneration of ATP-actin. As a consequence, actin becomes trapped in a non-productive ADP-bound state, leading to accumulation of aged filaments and overall impairment of the turnover cycle. We acknowledge that direct biochemical validation of each mutant construct would have further strengthened the conclusions on the mutants lacking a clear phenotype. While these analyses were beyond the scope of the current study, we now discuss this caveat in the manuscript and clarify the mechanistic interpretation of the domain-rescue results in the Discussion.

Minor comments: 1. It is stated that "In follicular epithelial cells, Lat A treatment resulted in the disappearance of apical and basal actin, whereas cortical actin remained largely unaffected in both stage 8 and 10 egg chambers (Fig. 1B)". However, the disappearance of basal actin was not clear because it is at low levels in the control making the comparison with the treatment difficult to interpret. Also, "lateral" would be a better term than "cortical".

Response: We agree that the originally presented images did not adequately illustrate the effect of Latrunculin A treatment on basal actin, particularly given its relatively low baseline intensity. To address this, we have: • Added images of lateral and basal cross-sections (Fig. 1B) • Included quantitative measurements of basal actin intensity under control (DMSO) and Latrunculin A conditions (Fig. 1C) These additions allow for a more direct and reliable comparison and clarify that basal actin is indeed sensitive to Latrunculin A treatment. We have also replaced the term "cortical" with "lateral" throughout the manuscript, as suggested, to improve precision and clarity.

1. The authors state "Interestingly, the width of the perivitelline space, apically to CAP mutant cells was decreased compared to the neighboring cells (Figure 3 E)." However, it was unclear where to look in the figure panel to see this effect. A degree of quantification is also warranted.

Response: To improve the clarity in the original figure presentation we have now clearly marked the perivitelline space in the TEM images. We agree that direct quantification would strengthen this observation. However, because the width of the perivitelline space is closely related to the length of apical microvilli, we refer the reader to our quantitative measurements of microvillar length (Fig. 7B-C), which provides a biologically relevant quantitative measure associated with this phenotype. We now explicitly state this relationship in main text to ensure clarity.

1. In Figure 4, I recommend expanding the explanations of the X axes of the graphs, and adding explanations of why data from the same experiment are graphed in multiple ways (or simplifying the presentation if it still allows the same conclusions).

Response: We have revised the figure presentation (Fig. 5C', I' and 7F', I',L') to improve clarity in several ways: • Axis definition: We now provide a detailed explanation of the X-axis in the figure legends. In control cells, the zero point corresponds to the apical cortex. In CAP mutant cells, the position of the actin accumulation varies between cells. Therefore, we normalized the X-axis such that the zero point corresponds to the boundary between the actin-rich domain and the basal cytoplasm. • Rationale for normalization: We explicitly explain that this normalization allows for more meaningful averaging across cells and better reflects the spatial relationship between markers and the actin accumulation. • Simplification of presentation: To reduce complexity and improve readability, we have removed individual cell line scans and now present averaged profiles of the apical intensity from multiple cells, which better represent the overall trend. These revisions substantially improve the interpretability of the data while preserving the conclusions.

1. Typo on page 6, line 244: "(Fig. 4C, E-F)"?

Response: The figure reference has been corrected in the revised manuscript.

1. More detail is needed to clarify this interpretation: "Furthermore, the localization of membrane-bound mCD8-GFP was partially restored in the apical region of CAP mutant cells after Latrunculin A treatment (Fig. 5E, F)." With respect to the local mCD8 protein levels, the DMSO control and LatA treatment seem similar.

Response: Following this comment, we repeated the experiment and performed quantitative analysis of mCD8-GFP localization. Our results show no significant difference between DMSO and Latrunculin A-treated conditions (Fig. 6D). Therefore, we agree that the original interpretation was not sufficiently supported. We have now removed the corresponding statement from the manuscript and revised the text. We thank the reviewer for prompting this clarification.

1. Grammar issue on page 2, line 50: "comprising of contractile actin"

Response: We have corrected the grammatical error ("comprising of contractile actin") in the revised manuscript.

1. Unclear sentence on page 3, line 100: "Our study demonstrates that actin disassembly protein, Cyclase associated protein-mediated apical actin turnover is required for..."

Response: We have rewritten the sentence for clarity.

1. On page 4, after describing an increased expression of profilin localized mainly away from the site of F-actin accumulation, the authors conclude that "This indicates that an excess of actin filament assembly is unlikely to occur at the apical side of CAP mutant cells." I suggest toning down this conclusion.

Response: We have revised the text and removed this interpretation.

Reviewer #2 (Significance (Required)): The advance made by the paper seems somewhat limited. In part, this is due to the two major comments above. Addressing these concerns experimentally could increase the significance of the paper. Additionally, the authors reference Baum and Perrimon (2001), a paper which showed excessive, apical F-actin accumulations in follicle cells mutant for CAP in Drosophila egg chambers. Other studies referenced in the manuscript provide evidence of local F-actin accumulations affecting the distributions of other components of a cell. Thus, the main conclusions of the manuscript seem similar to those made by previously published papers. Nonetheless, a strength of the paper is its reporting of altered distributions of a wide range of cell components in relation to an excessive accumulation of apical F-actin in an epithelial cell lacking CAP.

Response: We realize that in the original manuscript, we did not fully succeed in communicating the advance made by this study. The Reviewer correctly points out, that the apical actin accumulation has been reported previously by Baum and Perrimon (2001) (PMID: 11584269). In our view, the main advance of our study relevant for broader audience interested in epithelial cell biology is that the disturbance of apical actin turnover in epithelial cells in vivo locally disturbs non-centrosomal microtubule organization. We show that while microtubule polarity is preserved (dynein localization) and apical Patronin localization is retained, the microtubules are markedly reduced from the apical site of actin accumulation. In the revised manuscript we further show that this phenotype can be partially reversed by a 30 min latrunculin A treatment, which also partially reduces the actin accumulation. We also show that the apical actin accumulation leads to mislocalization of the actin-microtubule crosslinker Shot. Notably, this mislocalization is also partially rescued by the 30 min LatA treatment, further supporting that these changes reflect direct impact on actin-microtubule coupling. In addition, more specific advance relevant to scientists studying regulation of actin cytoskeleton are following 1. Evidence for the role of CAP in local regulation of apical actin turnover in epithelial cells in vivo. We show that while the apical actin pool is rapidly (5 min) lost in LatA-treated control cells, reflecting high turnover, it becomes significantly more resistant to LatA in CAP mutant cells, supporting the conclusion that CAP controls apical actin turnover. This conclusion is further supported by the findings of Aip1 enrichment in the sites of CAP-dependent actin accumulation. Aip1 associates with cofilin-decorated filaments undergoing disassembly. 2. Establishing the essential role of the CARP domain of CAP in epithelial actin turnover in animals in vivo. Through domain-specific rescue experiments, we demonstrate that CARP-domain function is uniquely required to prevent apical actin accumulation, whereas mutations affecting other described CAP activities retain substantial rescue capacity. These data identify actin monomer recycling as a critical determinant of epithelial actin turnover and provide the first in vivo functional dissection of CAP domain requirements in a polarized epithelial tissue.

Reviewer #3 (Evidence, reproducibility and clarity (Required)): Summary: Cyclase-Associated Protein (CAP) is a multifunctional regulator of actin turnover that stabilises pointed end of actin filaments and facilitates ADP-ATP exchange on G-actin. In the manuscript by Babu et al. re-visit a previously described phenotype of CAP mutants in Drosophila follicle epithelial cells. Depletion of CAP in the follicular epithelium leads to an accumulation of dense actin aggregates in the apical region of the cells. This ectopic apical actin structure disrupts the organization of the non-centrosomal microtubule (MT) network, Dynein-based apical cargo trafficking, the formation of apical microvilli and nuclear positioning.

1) The most interesting part of the manuscript in my opinion is the rescue of the CAP mutant phenotype by various CAP transgenes. The authors show that the formation of the actin aggregates can be rescued by the overexpression of CAP defective in pointed end depolymerisation activity, but not by a transgene with the for CARP domain, which is involved in actin monomer ADP-ATP exchange. This leads to the conclusion that the formation of actin aggregates is not caused by the stabilisation of the pointed ends of actin filaments, but rather by deficient G-actin ADP-ATP exchange. However, the overexpression of profilin does not rescue the CAP phenotype. It seems counterintuitive that depletion of G-actin-ATP induces the formation of an ectopic actin structure, suggesting an excess of actin polymerisation. Thus, the molecular basis for the phenotype remains unexplained.

Response: We thank the reviewer for carefully considering the mechanistic implications of our domain-rescue experiments and for highlighting the apparent contradiction between impaired G-actin nucleotide exchange and accumulation of filamentous actin. We agree that this observation is initially counterintuitive. Our interpretation, however, is that CAP mutant cells do not exhibit increased actin assembly but instead accumulate actin filaments due to a failure of the turnover and recycling cycle. Several lines of evidence support this interpretation: • The accumulated apical actin is resistant to Latrunculin A (Fig. 6B), compared to apical actin in control cells (Fig. 1B, C), indicating that CAP reduced turnover rather than active assembly • The actin structures are enriched in Aip1 which associate with cofilin-decorated filaments undergoing disassembly (Suppl. Fig. 1B) • Basal actin levels are reduced (Fig. 1N'), consistent with depletion of ATP-actin monomers Together, these observations indicate that actin filaments accumulate because they become trapped in a non-productive state, rather than because polymerization is increased. In this context, the CARP domain plays a central role in coordinating ADP-actin processing, cofilin release, and nucleotide exchange. Disruption of this domain is expected to stall multiple steps of the recycling cycle simultaneously. This results in accumulation of ADP-bound actin and failure to sustain dynamic turnover. Thus, the phenotype likely reflects an impairment of the actin recycling system as described in previous studies (PMID: 29760438, PMID: 36912152), rather than a shift in polymerization dynamics. We have expanded the Discussion to explicitly address this point and clarify the interpretation of the underlying mechanism.

2) I suggest that the authors go further to pinpoint the in vivo function of CAP in epithelia. According to Kotila et al., 2018, the CARP mutant that the authors used for their rescue experiments disrupts both G-actin-ADP binding and ADP-ATP exchange. The authors could test less severe CARP mutants for their ability to rescue the phenotype, such as the ∆4C mutant, which disrupts nucleotide exchange but still binds ADP-G actin, and K347A Y351A Y353A (yeast numbering), which disrupts ADP G-actin binding, but keeps ADP-ATP nucleotide exchange activity intact.

Response: We agree that analysis of additional CARP mutants would provide valuable mechanistic insight. However, we were not able to perform these experiments within the scope of the current study: • The specific mutants separating ADP-actin binding and nucleotide exchange functions have not yet been generated in our system • We attempted to generate transgenic lines expressing the Δ4C mutant; however, these lines were unstable, poorly expressed, or non-viable These observations suggest that disruption of CAP function at this level may have strong dominant-negative or toxic effects in vivo. This is consistent with previous findings in yeast, where Δ4C behaves similarly to a CAP loss-of-function mutant by sequestering ADP-actin and stalling the turnover cycle (Kotila et al., 2019, PMID: 29760438). Such a dominant-negative effect could explain the poor viability and instability of transgenic lines. While we regret that we cannot provide these additional data, we believe that our current results already support a model in which CAP function cannot be reduced to a single biochemical activity but instead reflects coordinated regulation of multiple steps in actin turnover. We now state this limitation explicitly in the manuscript.

3)The authors claim that noncentrosomal microtubules are disorganised in CAP mutant cells. However, the density of MTs below the apical actin barrier is normal and Patronin, a well-characterised marker of MT minus ends, still localises apically. This suggests that even though MT cannot penetrate the ectopic actin structure, they efficiently go round it. Since the authors have concluded that MT apical-basal polarity is preserved in CAP mutant cells, they should explain and demonstrate more clearly what is specifically wrong with the MT organisation and how this links to nuclear mispositioning.

Response: The reviewer points out that our original description of the microtubule phenotype as "disorganized" was imprecise. We have revised this interpretation to more accurately reflect our observations. Specifically, we find that: • Microtubules are detectable beneath the actin accumulation (Fig. 5A-C) • Minus-end anchoring at the apical cortex is preserved (Patronin, Fig. 5D-F) • Microtubule polarity remains intact (Dynein, Fig. 7J-L) Thus, the microtubule array is not globally disrupted but is instead spatially redistributed relative to the apical cortex. We agree with the reviewer that microtubules may "go around" the actin-rich region, and this observation may be related to Shot mislocalization and changes in actin-microtubule coupling. However, such redistribution is itself likely to have functional consequences, particularly for processes that depend on proper microtubule positioning and engagement at the apical cortex. Importantly, we now incorporate Shot mislocalization into this interpretation (Fig. 5G-I). Because Shot mediates actin-microtubule coupling, its displacement suggests that microtubules may fail to be properly captured or guided at the cortex, in addition to being displaced. Consistent with the known role of apically organized microtubules in follicle cell nuclear positioning (PMID: 23077179), we propose that disruption of actin-microtubule coupling together with reduced microtubule access from the apical cortex may impair the spatial organization of microtubule-generated pushing forces required for nuclear positioning. We have revised the manuscript to emphasize spatial redistribution and impaired functional engagement, rather than disorganization.

4)It would be very helpful if the authors could provide a clearer explanation why the expression of CAP rescue constructs enhances the nuclear mispositioning phenotype. I do not understand how the "better survival" (line 346) of cells connects with nuclear positioning. It is also not clear why the nuclear mispositioning phenotype cannot be rescued by expressing CAP transgenes at stages 8 to 10.

Response: The reviewer highlights the need for a clearer and more consistent interpretation of the nuclear positioning phenotype. We agree that the original manuscript did not adequately explain the relationship between rescue construct expression and nuclear positioning, and we have removed unsupported statements regarding "better survival." Our revised analysis now provides a plausible explanation for why nuclear positioning is not restored by CAP re-expression. Specifically, we show that: • Nuclear mispositioning is present in CAP mutant cells (Fig. 4A-C). • CAP rescue constructs exhibit minimal expression during stages 6-7, when nuclear positioning is established (Fig. 4J-K). • During this same developmental window, actin accumulation and microtubule defects persist in CAP rescue cells (Fig. 4D-I). • At later stages, when CAP expression increases, both the actin and microtubule phenotypes are efficiently rescued. Together, these findings indicate that expression of the rescue construct occurs largely after the developmental period during which nuclear positioning is established. Thus, the inability of the transgene to rescue nuclear positioning is consistent with the temporal requirements of this process rather than a failure to rescue CAP function per se. Based on these observations, we propose that the nuclear positioning phenotype arises as a consequence of early cytoskeletal defects. Given that nuclear positioning in follicle cells depends on coordinated actin and microtubule organization during stages 6-9 (PMID: 23077179), persistent cytoskeletal defects during this period provide a plausible explanation for the observed phenotype. We have revised the manuscript accordingly and now clearly state that, while the data support a temporal explanation, the precise mechanism linking CAP function to nuclear positioning remains to be determined.

Minor points: 1) Line 523 "For rescue experiments clones were generated up to 9 days prior to dissections, in order to ensure the disappearance of endogenous CAP." It takes less than 2 days for an egg chamber to mature from stage 1 to stage 10. Thus, waiting longer after clone induction should have no effect on the perdurance of CAP.

Response: We agree that the timing of egg chamber development suggests that prolonged clone induction is unlikely to significantly affect the perdurance of endogenous CAP. We have revised this statement in the Methods section to avoid implying that extended induction time ensures CAP depletion. Instead, we now describe the experimental timing more accurately and avoid overinterpreting its effect.

2)I could not find what media was used for incubating egg chambers with Latrunculin A.

Response: We have now added a detailed description of the incubation conditions used for Latrunculin A treatment, including the culture medium and treatment parameters, to the Methods section to ensure reproducibility.

Reviewer #3 (Significance (Required)): Although the data are sound, this report does not explain why CAP mutants cause an apical accumulation of F-actin in epithelial cells. Instead, their data seem to rule out the most likely explanation, namely that a loss of CAP leads to a failure to disassemble actin filaments, because mutation of the HDF domain, which enhances filament disassembly has no effect on the rescue by CAP transgenes. Since the CARP domain, which binds to G-actin to catalyse ADP to ATP exchange, is required for rescue, we are left with the counterintuitive conclusion that reducing the levels of assembly-competent ATP G-actin increases F-actin polymerisation. The main part of the manuscript describes the CAP mutant phenotype in detail. This reveals that the large apical blob of actin excludes other cellular structures. However, this does not advance our understanding of actin/ microtubule crosstalk as the authors claim, not does it explain why the nucleus is mispositioned even in rescued CAP mutant clones

Response: As discussed above, we agree that the accumulation of F-actin upon disruption of a recycling function appears initially counterintuitive. However, our evidence that the apical actin pool is rapidly (5 min) lost in LatA-treated control cells but becomes significantly more resistant to LatA in CAP mutant cells, supports the conclusion that CAP indeed promotes apical actin turnover. This conclusion is further supported by the findings of Aip1 enrichment in the sites of CAP-dependent actin accumulation. Aip1 preferentially associate with aged, Cofilin-decorated filaments undergoing disassembly. As explained above, the failure of rescue of the mutant phenotype by the CARP domain mutant may reflect failure in the actin recycling, a conclusion supported by recent studies (PMID: 29760438, PMID: 36912152). Therefore, the conclusions of the role of CAP in epithelial actin turnover (disassembly vs. polymerization), cannot in our view be solely based on the single line of evidence from the CARP domain mutant rescue.

While we appreciate the Reviewer's perspective, we believe our findings advance understanding of actin-microtubule crosstalk by identifying a role for local actin turnover in regulating the positioning and cortical engagement of non-centrosomal microtubules in vivo. Our data shows that while microtubule polarity is preserved (dynein localization) and apical Patronin localization is retained, the microtubules are markedly reduced from the apical site of actin accumulation. In the revised manuscript we further show that this phenotype can be partially reversed by a 30 min latrunculin A treatment, which also partially reduces the actin accumulation. We also show that the apical actin accumulation leads to mislocalization of the actin-microtubule crosslinker Shot. Notably, this mislocalization is also partially rescued by the 30 min LatA treatment. Collectively, these data support the conclusion that CAP-mediated apical actin turnover directly impacts actin-microtubule coupling in epithelial cells in vivo. In conclusion, our own interpretation of the advance aligns with that of Reviewer 1 that "the main advance of the study is functional and conceptual, linking CAP-dependent actin turnover to microtubule organization and apical trafficking in a polarized epithelial context."

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Referee #3

Evidence, reproducibility and clarity

Summary: Cyclase-Associated Protein (CAP) is a multifunctional regulator of actin turnover that stabilises pointed end of actin filaments and also facilitates ADP-ATP exchange on G-actin. In the manuscript by Babu et al. re-visit a previously described phenotype of CAP mutants in Drosophila follicle epithelial cells. Depletion of CAP in the follicular epithelium leads to an accumulation of dense actin aggregates in the apical region of the cells. This ectopic apical actin structure disrupts the organization of the non-centrosomal microtubule (MT) network, Dynein-based apical cargo trafficking, the formation of apical microvilli and nuclear positioning.

1) The most interesting part of the manuscript in my opinion is the rescue of the CAP mutant phenotype by various CAP transgenes. The authors show that the formation of the actin aggregates can be rescued by the overexpression of CAP defective in pointed end depolymerisation activity, but not by a transgene with the for CARP domain, which is involved in actin monomer ADP-ATP exchange. This leads to the conclusion that the formation of actin aggregates is not caused by the stabilisation of the pointed ends of actin filaments, but rather by deficient G-actin ADP-ATP exchange. However, the overexpression of profilin does not rescue the CAP phenotype. It seems counterintuitive that depletion of G-actin-ATP induces the formation of an ectopic actin structure, suggesting an excess of actin polymerisation. Thus, the molecular basis for the phenotype remains unexplained.

2) I suggest that the authors go further to pinpoint the in vivo function of CAP in epithelia. According to Kotila et al., 2018, the CARP mutant that the authors used for their rescue experiments disrupts both G-actin-ADP binding and ADP-ATP exchange. The authors could test less severe CARP mutants for their ability to rescue the phenotype, such as the ∆4C mutant, which disrupts nucleotide exchange but still binds ADP-G actin, and K347A Y351A Y353A (yeast numbering), which disrupts ADP G-actin binding, but keeps ADP-ATP nucleotide exchange activity intact.

3)The authors claim that noncentrosomal microtubules are disorganised in CAP mutant cells. However, the density of MTs below the apical actin barrier is normal and Patronin, a well-characterised marker of MT minus ends, still localises apically. This suggests that even though MT cannot penetrate the ectopic actin structure, they efficiently go round it. Since the authors have concluded that MT apical-basal polarity is preserved in CAP mutant cells, they should explain and demonstrate more clearly what is specifically wrong with the MT organisation and how this links to nuclear mispositioning.

4)It would be very helpful if the authors could provide a clearer explanation why the expression of CAP rescue constructs enhances the nuclear mispositioning phenotype. I do not understand how the "better survival" (line 346) of cells connects with nuclear positioning. It is also not clear why the nuclear mispositioning phenotype cannot be rescued by expressing CAP transgenes at stages 8 to 10.

Minor points:

1) Line 523 "For rescue experiments clones were generated up to 9 days prior to dissections, in order to ensure the disappearance of endogenous CAP." It takes less than 2 days for an egg chamber to mature from stage 1 to stage 10. Thus, waiting longer after clone induction should have no effect on the perdurance of CAP.

2)I could not find what media was used for incubating egg chambers with Latrunculin A.

Significance

Although the data are sound, this report does not explain why CAP mutants cause an apical accumulation of F-actin in epithelial cells. Instead, their data seem to rule out the most likely explanation, namely that a loss of CAP leads to a failure to disassemble actin filaments, because mutation of the HDF domain, which enhances filament disassembly has no effect on the rescue by CAP transgenes. Since the CARP domain, which binds to G-actin to catalyse ADP to ATP exchange, is required for rescue, we are left with the counterintuitive conclusion that reducing the levels of assembly-competent ATP G-actin increases F-actin polymerisation.

The main part of the manuscript describes the CAP mutant phenotype in detail. This reveals that the large apical blob of actin excludes other cellular structures. However, this does not advance our understanding of actin/ microtubule crosstalk as the authors claim, not does it explain why the nucleus is mispositioned even in rescued CAP mutant clones

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Referee #2

Evidence, reproducibility and clarity

Babu and colleagues report that clonal loss of Cyclase associated protein (CAP) function results in dramatic accumulation of F-actin in a large cytoplasmic domain below the apical surface of Drosophila egg chamber follicle cells. Rescue experiments confirm the overall role of CAP and show that its function in converting actin-GDP to actin-GTP is critical for preventing the F-actin accumulation. Numerous components of the cell are probed in the mutant clones, and are shown to have altered distributions. Microtubules and intracellular membranes are generally excluded from the abnormal F-actin domains, and Latrunculin A treatment partially reversed the microtubule exclusion. Abnormalities in apical microvilli, apicolateral nuclear positioning, and actin binding protein distributions are also reported. In general, the microscopy is quite striking and the manuscript is clearly written, but the overall advance seems fairly limited and several revisions are needed.

Major comments:

1. The authors conclude that the abnormal F-actin accumulations of CAP mutant cells coincide with microtubule cytoskeleton alterations, and say that this "suggests that spatially regulated actin filament turnover is important for microtubule organization". Although the conclusion and suggestion are formally true, they don't consider the directness of the relationship. In my view, two possibilities of indirect effects should be included: (1) the general disruption of subcellular organization by the large F-actin accumulation suggests that many indirect effects are possible, and (2) the very high level of F-actin accumulation, and of actin binding protein co-accumulations, without apparent losses from other parts of the cell suggest that the mutant cells have undergone major gene expression changes which could have a range of effects.
2. The authors state that the CARP domain of CAP is known to bind ADP-actin monomers and promote ADP-ATP exchange, "thereby recharging actin monomers for polymerization". Of many mutations expected to affect individual domains of CAP, only mutations disrupting the nucleotide exchange activity of the CARP domain failed to rescue the abnormal F-actin accumulations of CAP mutant cells. It was unclear how extreme actin polymerization occurs in cells in which the CAP protein expressed only lacks the ability to recharge actin monomers for polymerization. Minimally, the results of the domain analyses should be addressed in the Discussion section. More analyses/constructs may be needed to confirm whether the mutations listed in Table 1 had their intended effects on CAP domain activities (especially on the activity of the HFD domain implicated in actin depolymerization).

Minor comments:

1. It is stated that "In follicular epithelial cells, Lat A treatment resulted in the disappearance of apical and basal actin, whereas cortical actin remained largely unaffected in both stage 8 and 10 egg chambers (Figure 1B)". However, the disappearance of basal actin was not clear because it is at low levels in the control making the comparison with the treatment difficult to interpret. Also, "lateral" would be a better term than "cortical".
2. The authors state "Interestingly, the width of the perivitelline space, apically to CAP mutant cells was decreased compared to the neighboring cells (Figure 3 E)." However, it was unclear where to look in the figure panel to see this effect. A degree of quantification is also warranted.
3. In Figure 4, I recommend expanding the explanations of the X axes of the graphs, and adding explanations of why data from the same experiment are graphed in multiple ways (or simplifying the presentation if it still allows the same conclusions).
4. Typo on page 6, line 244: "(Figure 4 C, E-F)"?
5. More detail is needed to clarify this interpretation: "Furthermore, the localization of membrane-bound mCD8-GFP was partially restored in the apical region of CAP mutant cells after Latrunculin A treatment (Figure 5 E, F)." With respect to the local mCD8 protein levels, the DMSO control and LatA treatment seem similar.
6. Grammar issue on page 2, line 50: "comprising of contractile actin"
7. Unclear sentence on page 3, line 100: "Our study demonstrates that actin disassembly protein, Cyclase associated protein-mediated apical actin turnover is required for..."
8. On page 4, after describing an increased expression of profilin localized mainly away from the site of F-actin accumulation, the authors conclude that "This indicates that an excess of actin filament assembly is unlikely to occur at the apical side of CAP mutant cells." I suggest toning down this conclusion.

Significance

The advance made by the paper seems somewhat limited. In part, this is due to the two major comments above. Addressing these concerns experimentally could increase the significance of the paper. Additionally, the authors reference Baum and Perrimon (2001), a paper which showed excessive, apical F-actin accumulations in follicle cells mutant for CAP in Drosophila egg chambers. Other studies referenced in the manuscript provide evidence of local F-actin accumulations affecting the distributions of other components of a cell. Thus, the main conclusions of the manuscript seem similar to those made by previously published papers. Nonetheless, a strength of the paper is its reporting of altered distributions of a wide range of cell components in relation to an excessive accumulation of apical F-actin in an epithelial cell lacking CAP.

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Referee #1

Evidence, reproducibility and clarity

In the manuscript by Babu et al, "Apical actin filament turnover mediated by cyclase-1 associated protein is required for organization of non-centrosomal microtubules in epithelium," the authors investigate how Cyclase-associated protein (CAP) regulates apical actin organization and how this impacts microtubule architecture and apical trafficking in the Drosophila follicular epithelium. CAP depletion leads to accumulation of a dense, Latrunculin-resistant apical F-actin network, accompanied by loss of apical microtubules, mislocalization of vesicular markers (e.g., Rab11, Cad99C, Dynein), defects in microvilli formation, and altered nuclear positioning. Domain-rescue experiments suggest that CAP's nucleotide exchange activity is required for proper actin organization.

The study presents a rich set of phenotypic observations and highlights an important interplay between actin turnover, microtubule organization, and epithelial polarity. However, several key mechanistic conclusions are currently not fully supported by the data, and an important conceptual question regarding the spatial specificity of CAP function remains insufficiently addressed.

Major Comments

1. Is the CAP function truly apically specific? A central conclusion of the manuscript is that CAP regulates the apical actin cytoskeleton. However, the data do not yet clearly distinguish whether CAP acts in a spatially polarized manner or instead regulates global actin turnover, with apical accumulation emerging as a secondary consequence of epithelial geometry. As CAP appears largely cytoplasmic, it is plausible that its depletion affects actin dynamics throughout the cell. In this scenario, actin accumulation may become most apparent at the apical domain because this region is less occupied by organelles compared to the laterobasal cytoplasm. Thus, the observed phenotype could reflect global dysregulation of actin turnover, rather than a specifically apical mechanism. Importantly, this does not contradict the authors' model but represents an alternative that should be addressed. To clarify this point, the authors should consider:
   • Quantifying actin distribution across the full apico-basal axis
   • Testing whether forced relocalization of CAP (e.g., to the basal cortex) alters where actin accumulates
   • Assessing whether non-apical actin structures are also altered but less apparent Without addressing this, the claim of apical-specific regulation remains insufficiently supported and should be framed more cautiously.
2. what is the primary molecular function of cap in this context? While the phenotypic consequences of CAP depletion are well described, the manuscript does not clearly resolve which step of actin turnover is affected. CAP is known to function in actin monomer recycling and cooperate with cofilin, but it remains unclear in this system whether the primary defect reflects: (i) Impaired actin depolymerization, (ii) Reduced monomer recycling or altered filament dynamics or nucleation balance Clarifying this point is important, as it would strengthen the mechanistic link between CAP activity and the observed cellular phenotypes. Even if not directly tested experimentally, this aspect should be more explicitly discussed and, where possible, supported by quantitative analysis of actin dynamics.
3. insufficient quantification of actin stability. The conclusion that apical actin is stabilized in CAP mutants is based primarily on qualitative observations of Latrunculin A resistance. While convincing visually, this requires quantitative validation. Measurement of actin intensity under {plus minus}LatA conditions, across multiple samples with proper normalization and statistical analysis, is necessary to substantiate increased actin stability.
4. Domain-rescue experiments lack quantification (Fig.2,S2). The conclusion that the CARP domain is required for rescue is based on qualitative comparisons. Given the importance of this experiment for mechanistic interpretation, quantitative analysis of rescue efficiency (e.g., actin intensity, percentage of rescued clones) is essential.
5. Microtubule exclusion model is not directly demonstrated The authors propose that dense apical actin physically excludes microtubules. While the presented data are consistent with this model, they remain correlative. Alternative explanations include: (i) Altered microtubule stability, (ii) Defective nucleation or anchoring or (iii) changes in epithelial polarity affecting microtubule organization. To distinguish between these possibilities, the authors should:
   • Perform live imaging of microtubule plus ends (e.g., EB1) to assess whether microtubules fail to enter or instead destabilize at the apical region
   • Examine whether microtubule polarity or nucleator localization is altered
   • Increase sample size and quantification for line-scan analyses (Fig. S3) The current interpretation should therefore be presented more cautiously as one of several possible mechanisms.
6. Shot redistribution suggests an alternative mechanism (Fig.6). The redistribution of Shot beneath the actin accumulation is a key observation that is currently underexplored. Given that Shot mediates actin-microtubule crosslinking, this finding suggests that disrupted cytoskeletal coupling could underlie microtubule defects. This provides an alternative to the steric exclusion model and should be more fully integrated into the manuscript. The authors should:
   • Quantify Shot redistribution relative to the apical domain
   • test whether restoring Shot at the apical cortex rescues microtubule organization
   • compare effects of Shot versus Patronin manipulation to distinguish crosslinking versus anchoring roles
7. Nuclear positioning phenotype is not fully resolved (Fig.7). The explanation that the lack of rescue reflects late expression of the CAP construct is plausible but not experimentally demonstrated. This interpretation should be toned down or explicitly presented as speculative.

Minor comments:

1. Quantification and sample size Many claims rely on representative images and n and N are not reported in such cases. Include quantification and clearly report n and N for all analyses.
2. Vesicle exclusion and secretion defects remain indirect (Fig.3) Evidence for vesicle exclusion is based on loss of ER/Golgi markers and altered TEM structures. However, TEM identification of mutant (clones) cells is phenotype-based. The current data are consistent with altered apical trafficking but do not directly demonstrate vesicle exclusion from the actin-rich domain. More direct evidence would require visualization of vesicle dynamics to determine whether they fail to enter, stall at or are redirected from the apical actin accumulation. The current wording should be softened accordingly.

Significance

The work provides a strong phenotypic characterization linking CAP depletion to accumulation of a dense, Latrunculin-resistant apical F-actin network, accompanied by defects in microtubule organization, vesicle localization, and epithelial morphology. A key strength is the integration of multiple readouts to connect actin turnover with broader aspects of epithelial organization. The study therefore offers potentially important insight into how actin dynamics can influence cytoskeletal crosstalk and tissue architecture. However, several central conclusions rely on largely qualitative or correlative evidence, and quantitative support is limited in key experiments. In addition, an important conceptual question remains unresolved: whether CAP regulates actin turnover in a spatially polarized (apical-specific) manner or more globally, with apical phenotypes emerging as a consequence of cellular organization. Addressing this distinction, along with strengthening quantification and moderating interpretation of the steric exclusion model, would substantially improve the manuscript.

The main advance of the study is functional and conceptual, linking CAP-dependent actin turnover to microtubule organization and apical trafficking in a polarized epithelial context. While CAP is known to regulate actin dynamics, its role in coordinating cytoskeletal organization at the tissue level is less well defined, and this work extends current knowledge in that direction. At present, however, the mechanistic insight remains limited, particularly regarding the specific step in actin turnover affected and the causal relationship between actin, microtubules, and trafficking defects. The study will be of primary interest to a specialized audience in cytoskeleton, epithelial, and developmental biology, with broader relevance to researchers studying actin-microtubule crosstalk and cell polarity.

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Referee #3

Evidence, reproducibility and clarity

Cancer is associated with profound changes in metabolism and a deprivation of nutrients, including an overall reduction in amino acids. This research group has previously demonstrated that amino acid deprivation leads to ECM uptake that drives breast cancer cell migration and growth, but the mechanisms that drive this ECM scavenging are unknown. Here, the demonstrate that the collagen receptor integrin a2 is upregulated in cells following AA starvation in cells cultured in 2D and 3D. This upregulation is promoted by Ras/MEK signalling and was required for collagen uptake by cells. Furthermore, amino acid starvation was shown to promote cell adhesion to collagen-I and cell migration, highlighting the functional importance of this pathway.

The data presented and approaches used are clear and well executed with appropriate conclusions made from the data. I have a few questions and suggestions that would help clarify the findings of the study and potentially increase the impact of the study:

1. A clear change in a2 expression levels are shown following amino acid starvation, but does this correspond to changes in surface levels of this integrin?
2. In the attachment assays, you mention that integrin a5 levels are not altered and suggest fibronectin as a possible ECM where no change in adhesion would be observed. Have you done the experiment with fibronectin?
3. The conclusions are written appropriately for the data presented, but it would be interesting to determine whether the a2 internalisation and collagen-I uptake are required for the changes in proliferation observed following starvation rather than signalling downstream of a2 engagement with ligand.
4. Similarly, the conclusion that amino acid starvation promotes attachment and migration on collagen is appropriate, but is this dependent on a2? You could use you inhibitor or knockdown to assess this.
5. Does a2 localise to adhesion complexes in your assays? This is particularly relevant to your proliferation and migration assays where you use complete media over a longer period of time, ECM protein in the serum and generated by cells over this time may alter the integrins being utilised by the cells.

I think addressing all of these points is optional as they will help strengthen the study but will not alter the conclusions drastically.

The text and figures are very clear and work in the field is cited appropriately.

Significance

The findings from this study are significant to a variety of cancer types where changes in metabolism and nutrient availability are prevalent. The findings suggest that targeting a2 integrin may be a valid treatment option in pancreatic and breast tumours, particularly in relation to those with KRAS mutations which increases the significance of this study significantly and paves the way for future research that will presumably use patient-derived cells to assess some of the pathways identified.

This study will be of interest to people working in basic research, cancer research and potentially translational research.

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Referee #2

Evidence, reproducibility and clarity

This well-prepared manuscript describes the results of a study interrogating the mechanisms regulating amino acid-starvation-driven ECM uptake via alpha-2-integrin. The experiments are carefully carried out and analysed, and my comments mainly concern some analyses that are in my view lacking to fully enable the conclusions drawn.

Specific comments

Fig. 1. Maybe I am just missing something, but I do not understand the collagen-I labeling procedure: pH-rodo is pH sensitive, with increasing fluorescence at acidic pH values. It can therefore be used to assess endo-lysosomal pH values - but how do you distinguish in your collagen-I uptake index between more collagen taken up, vs localization in more acidic compartments? It seems this could introduce confounding effects. Please comment, and consider validating with a non-pH sensitive fluorophore.

Fig. 2. There is a very dramatic difference between the increase in ITGA2 mRNA levels (up to 200-fold) and protein levels (max 2-fold) in starvation conditions. Would protein levels increase more substantially upon longer treatments? This deserves at least commenting, ideally testing.

Fig. 3. It is very nice that the authors emply a matrigel 3D culture, but this is still a very artificial scenario, and matrigel does not really mimic the tumor ECM. To what extent is the same mechanism required for cancer cell survival in a more realistic tumor environment - i.e. with more complex ECM and/or additional (stromal) cell types present - which would alter the nutrient landscape? It would be very valuable to conduct experiments addressing this, but at least it should be discussed in more detail.

Fig. 4. The authors convincingly show that the GCN2 pathway is not responsible for the ITGA2 regulation. This is a very nice opportunity to gain insight into the relative importance of ITGA2 for cancer cell survival under nutrient starvation - how much is growth affected by the GCN2 inhibition relative to by interfering with ITGA2?

Perhaps I missed it, but can you comment on the possible relation and/or relative importance of the mTOR-inhibition-driven and RAS-driven pathways of ITGA2 regulation? If RAS signaling is important for the starvation-driven increase in ITGA2, does that imply that starvation further activates RAS signaling in cells which already harbor an oncogenic RAS mutation and thus presumably have constitutively increased RAS/MEK/MAPK signaling? Should ITGA2 not be consitutively upregulated in these cells if it was driven by RAS? Or is RAS just necessary, not the driver? Can the effect of starvation on ITGA2 be mimicked by introducing a constitutively active RAS in cells not harboring such mutations?

Fig. 6. It would be very helpful to show whether this increased migration and spreading is dependent on the RAS-dependent increase in ITGA2 (use a RAS inhibitor) and/or can be mimicked by overexpression of ITGA2? And a suggestion: the quantified difference in F is very small (about 0.4 vs 0.45), whereas the image indicates that the gap is essentially closed in the AA condition. I would replace this with a more representative example.

Fig. 7. Similar to my concern above, can you distinguish between effects of the MEKi on endo-lysosomal pH vs on collagen uptake?

Minor

P 1, a5b1 intergin -> integrin

Significance

Maybe not a huge advance but a carefully performed and clearly relevant study which contributes new information and is clearly deserving of publication.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study, Yanes et al. used several cell lines from pancreatic and breast cancer to show that amino-acid starvation induces ECM uptake via RAS-MEK signaling pathway-dependent increase of integrin α2 expression at the RNA and the protein level, using RAS and MEK inhibitors. They also showed that this pathway enhances cell adhesion and that AA starvation promotes migration on collagen. Patient data analysis indicated a correlation between high integrin α2 expression and poor prognosis in pancreatic cancer.

Major comments:

While the key conclusions are mostly convincing, some require additional experiments to be fully supported, and some additional discussion would help to clarify some points, as explained in the comments bellow. The data are clearly presented and properly analyzed and replicated with the adequate statistical analysis. The methods are clear enough to ensure reproducibility.

1) When observing collagen uptake, it would be useful to have a staining of endosomal markers to show that collagen is internalized in endosomes. Otherwise, the observed structures can only be named "vesicles" and not "endosomes".

2) In figure 1D, the proliferation is tested only by counting cells after 4 days. We cannot exclude that the difference in cell numbers is due to a difference in cell viability or to a difference of the number of cells which initially attached (as it is shown in figure 6C). Testing proliferation with a proliferation assay such as Brdu incorporation assay or at least testing the cell viability would ensure that AA starvation improves proliferation on collagen.

3) Only one siRNA has been used to knockdown integrin α2. A second siRNA should be used to ensure that the observed effects of the knockdown are not due to off-target effects.

4) In figure 2B-F, it seems that the integrin α2 levels differ between the cell lines, both at the baseline level and after starvation. Do these differences correlate with different capacities of each cell line to internalize collagen in response to AA starvation? This should be discussed.

5) In conclusion of figure 2, it is said that "a3, a5, and a6 integrin were not affected" by AA deprivation, and this is written again in the discussion. However, Figure S1K shows that integrin α5 expression also increases in this condition in SW1990 cells, as written in the text when describing this figure. The conclusion should be changed to include this result, and it would be nice to discuss it. Would fibronectin internalization in response to starvation also happen in this cell line?

5) In figure 3 it seems from the images that integrin α2 is increased only in cell-cell adhesions but not on the edge of the spheroids in contact with the matrix. Is this something consistent and could this be quantified? If the increase is only happening inside the spheroids, it seems unlikely that it would have a role in matrix uptake in 3D. Moreover, as figure 6D does not show any difference of cell adhesion to Matrigel in complete media vs under AA starvation, doing the 3D experiments in collagen rather than Matrigel would give a better insight in the significance of the uptake mechanism in 3D. Even if the observation of integrin α2 expression changes in 3D is suggesting a similar mechanism in 3D than in 2D, observing collagen uptake in 3D would ensure that the role of this pathway is the same than in 2D. This could be done either by staining for collagen in Matrigel or by embedding the cells inside fluorescent collagen. Finally concerning the 3D data, in Figure 3 the size of the spheroids is quantified but no conclusion is drawn from the observed difference. Quantifying the number of cells would give a better readout of the differences in proliferation.

6) Figure S3 shows that the MRTX1133 KRASG12D inhibitor decreases expression of integrin α2 in SW1990 cells but not in PANC1 cells, and it is speculated that this difference is due to the heterozygous status of PANC1 cells for KRAS. Using a pan-RAS inhibitor would be useful in PANC1 cells to confirm this hypothesis.

7) The finding in Figure 6D that AA starvation does not impact adhesion on Matrigel is surprising, as we would expect Matrigel to contain collagen. This should be further discussed. As SW1990 also express higher levels of integrin α5 in response to starvation, looking at adhesion on fibronectin should be done to interrogate if this mechanism is specific to collagen binding only.

8) The functional experiments of Figure 6 show nicely that AA starvation improves cell adhesion on collagen and migration under a collagen overlay. However, this does not show if the uptake of collagen itself is involved there. Blocking endocytosis would show if collagen uptake is necessary for the observed phenotype, or if it is only due to the higher expression of integrin α2 which by itself enhances cell adhesion and migration. Using in the migration experiment RAS and MEK inhibitors is also necessary to show that the same pathway is involved in migration to exclude that AA starvation would impact these via a different pathway, as it has been done for adhesion in Figure 7A. As the migration is emphasized in the title, I would also expect to see this experiment on other cell lines.

9) While most experiments are performed on SW1990 cells, the collagen uptake experiment under MEK inhibition of Figure 7B was done only on MCF10A cells. This should be done on the SW1990 cells as well for consistency.

10) If possible, showing correlation between KRAS mutation status and integrin α2 expression in patient data would reinforce the conclusions on the clinical significance of the mechanism. As the study includes breast cancer cell lines, showing the correlation between integrin α2 expression and survival in breast cancer patients would also provide better insights on the relevance of the mechanism in different cancer types.

Minor comments:

1) A reference is missing to cite the origin of the BTT-3033 inhibitor. I would suggest to cite Nissinen et al. Journal of Biochemistry 2012 (DOI: 10.1074/jbc.M111.309450).

2) In figure 2L-M the 37kDa mark is not placed at the same height for all the GAPDH bands. I suppose it is an issue of the figure design rather than an issue on the blot itself and this should be corrected. Without the uncropped blots showing the ladder it is however not possible to assess if the bands are really at the indicated size, these should be provided.

3) In Figure 6F, the graph should indicate individual values.

Significance

This study follows previous findings by the same group and others who showed that ECM uptake promotes tumors cells survival and proliferation in a low-nutrient availability context, and that the integrin α2β1 allows collagen uptake. The new findings here link these two observations as AA starvation is shown to upregulate integrin α2, leading to pro-oncogenic phenotypes. The study provides a mechanism for this, as they show the involvement of the RAS-MAPK pathway. The point made in the discussion that depending on the ERK inhibitor used or the duration of the inhibition might lead to different effects on integrin α2 levels, added to the discrepancies between cell lines, suggests that the described mechanism might not be universal or is relevant only in specific conditions.

This is still an interesting and important conceptual and mechanistic advance, which will be of interest for researchers in the fields of cancer (here pancreas and breast cancer), cell adhesion and signaling, mostly for basic research but potential clinical implications might be of interest for a broader audiance.<br /> My expertise relevant to this study is in cancer cell biology, cell adhesion, migration and signaling.

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Reply to the reviewers

General Statements

We thank the reviewers for thoroughly reading our manuscript and their constructive feedback. We have considered each comment carefully and came up with a revision plan that can be found below.

1. Description of the planned revisions

Response to Reviewer #1, #2 and #3 concerning alternative assays to measure the effects of ER stress on ribosome translation:

Reviewer 1: 4. The modest reduction in the translation upon ER stress induction could be supported by alternative biochemical assays such as polysome profiling and amino acid incorporation.

Reviewer 2: Is there a difference in the number polysomes in the non-stressed vs stressed yeast cells? A functional assay, such as polysome profiling combined with nascent-chain labeling might help to support the observation that an increased level of hibernating ribosomes exist in DTT or Tm-treated cells. Has this been considered? Perhaps there is evidence available in the literature?

Reviewer 3: 5. The study mainly provides structural snapshots and population distributions of ribosomal states, without direct functional measurements of translation activity. Could the authors provide orthogonal biochemical or functional evidence supporting reduced translation under these exact stress conditions?

We thank the reviewers for this suggestion. Other studies have shown a decrease in protein synthesis rate (Geronimo RAC et al., 2025 (PMID: 40959222), Pincus et al., 2014 (PMID: 25275008)) under similar conditions which matches our findings. However, we agree that confirming a reduction in translation for our specific conditions will strengthen our findings.

In our lab we have previously performed polysome profiling for mammalian cells, we will adopt this protocol to yeast cells and use this to measure changes in monosome abundance and changes in the polysome to monosome ratio. We will perform this experiment for our main strain (Ire1cGFP) upon 0 hr, 45 min. and 4 hr. DTT treatment. Given the increase in hibernating ribosomes upon prolonged ER stress, we hypothesize that polysome profiles will reveal an increase in monosome subunits, assuming that the technique is sensitive enough to pick up moderate changes in translational activity. In case polysome profiling is not sensitive enough to pick up the moderate change in hibernation, we also aim to quantify the decrease in protein synthesis using C-35 labeling as we have done earlier in collaboration (Fedry et al, Mol. Cell 2024 (PMID: 38340715)).

Reviewer #1 continued:

1. For identification of hibernating ribosomes, the authors rely mainly on the presence of empty ribosomes along with eEF2, eEF5A, and eEF3. Whether these particles indeed possess known dormancy factors or they are different subclass of empty ribosomes is unclear. Similar analysis in the absence of dormancy factors would strengthen the authors claims.

While empty 80S ribosomes (lacking tRNAs, elongation or hibernation factors) have been described in purified ribosome samples, those seem to be an in vitro re-association artifact as they are never observed in cells (bacteria: Xue et al. Nature 2022 (PMID: 36171285), yeast: Cheng et al. 2025 (PMID: 39789210), mammals: Xing et al. 2023 (PMID: 37410833), Fedry et al. 2024 (PMID: 38340715), etc.).

Instead, in cells ribosomes are found in three possible states:

1. individual subunits (40S and 60S in eukaryotes),
2. translating 80S ribosomes; featuring a tRNA in the P-site
3. hibernating 80S ribosomes; lacking a tRNA in the P-site and hence non translating. Those ribosomes are typically bound by eEF2 interacting with the dormancy factor bound in the mRNA channel, as well as possible additional factors (eIF5A, Dap1, SNOR, etc.). Our Hib class is seen in cells without tRNA in the P-site and bound by eEF2; we can therefore unambiguously assign this class as hibernating ribosomes.

While doing a similar analysis on the translation landscape under ER stress in the absence of hibernating factors may yield some interesting insights, it would also alter the overall stress response and therefore may not help with the interpretation of our current structures. It would require us to repeat our complete workflow with new yeast strains (with Stm1 and/or Lso2 knocked out) and in our opinion the amount of time that these experiments would require do not justify the additional confidence that would be gained from the results. We have therefore decided that these experiments will be beyond the scope of this study. We will add a supplementary figure showing the presence of a density in the mRNA channel further supporting the presence of a dormancy factor interacting with eEF2.

1. The authors suggest that ER induces modest level of increase in hibernating ribosomes. Adding controls such as glucose deprivation and nitrogen starvation would have provided more strength in relative comparison of these ribosomal sub populations.

To our knowledge, no cryo-ET study has been done to study the effect of glucose deprivation and nitrogen starvation on the abundance of different translational states, making it an interesting and relevant experiment to do. However, it is unknown what change(s) in translational state abundance(s) these low-nutrient conditions might cause, so we are unsure if they could serve as control conditions. Collecting data on yeast under different stresses would require extensive resources, and would not directly address the translational response to ER stress. Therefore, we consider these suggested experiments beyond the scope of this work. We think this is an interesting future research direction and will comment on this in our discussion.

We will include the suggested conditions in our polysome profiling experiments (proposed above in the first part of our revision plan) and analyse their monosome to polysome ratios. These can serve as positive controls for strong translation shutdown. We are grateful for the reviewers suggestion.

1. The authors show the retention of dormant ribosomes on the ER surface. As usual notion of ribosome association with ER membrane to be dependent on nascent translation, retention of dormant ribosomes on ER membrane is interesting and puzzling. Analysis using strains deleted for dormancy factors may provide more insights on this mechanism.

We agree with the reviewer that the presence of hibernating ribosomes on the ER surface is an interesting observation, but we do not consider it surprising. For yeast and mammals, idle ribosomes bound to Sec61 are well established in vitro (e.g., Becker et al (PMID: 19933108)), indicating that the interaction between these two components is not dependent on active translation. Furthermore, an average of an ER-bound hibernating ribosomes have been found on microsomes derived from human cells, and they become the prevalent form upon DDT-treatment, which strongly suggests that hibernating ribosomes can stay bound to the ER (Gemmer et al., 2023 (PMID: 36697828)). To clarify this point we will refer to these previous findings in our revised manuscript. As our observation is consistent with current knowledge in the field, we do not believe that additional analysis is necessary on this point.

Reviewer #2 continued:

The new Dec3 state might be clarified a bit further by zooming in to the corresponding areas in the Dec1 and Dec2 structures. This is a point of novelty in the paper and should be emphasized for future reference. Does an additional classification algorithm, such as cryo-DRGN-ET, verify the various states, especially the new Dec3 state? The structures should of course be uploaded to EMDB or another suitable server.

We will provide an additional supplemental figure, zooming in on the eIF5a area in Dec1/2/3. Dec3 was found in 3 separate classification runs and we will therefore not perform classification with an alternative algorithm. We will upload the novel structures (Dec3, Hib and the ER-bound ribosome) to EMDB, which will be released upon publication of this manuscript

There is generally a lack of supporting quantification, which will bother a number of readers. For example, a "high confidence rigid body fit" shows additional density in the hibernating state, but what is the confidence? Even the resolution measures of 7-8 Angstrom are simply stated. Presumably they come from a WARP report. There should be some specification for the evaluation. How many lamellae were used, and how many tomograms? Were they taken from different biological experiments, or all collected from the same grid, for each condition?

We agree with the reviewer that this additional information is required to properly judge our conclusions. We will provide a confidence score for the eEF3 fit. We will provide FSC curves as supplemental data, specifying where the FSC curve was obtained from. Local resolution estimates are derived from Relion. Table 4 indicates the number of tomograms collected per sample and we will add the number of lamella/grids used.

Reviewer #3 continued:

Major comments:

1. For the analysis of ER-bound ribosomes, the authors applied an ellipsoidal mask during subtomogram averaging. However, this masking strategy may not be sufficient because the relative orientation of ribosomes with respect to the ER membrane can be variable, and membrane density may influence particle alignment. The authors may consider including an additional masking step to exclude membrane density and minimize potential alignment bias.

We thank the reviewer for pointing out this confusing point in our manuscript. The ellipsoid mask was only used in the image classification step aiming at separating ER-bound ribosomes from soluble ribosomes. The ER-bound ribosomes were subsequently aligned with a mask comprising the large ribosomal subunit and the membrane. This was crucial for the alignment not to go astray. We will clarify this in the text:

“Alignment and averaging of these particles using a mask comprising the ribosomal large subunit and the membrane region yielded a ribosome with a clear membrane bilayer and an additional density at the exit tunnel”

The signal coming from the ribosomal RNA is very strong (unlike single particles studies of smaller membrane proteins) and typically much stronger than the signal coming from the ER membrane. This strategy is well established in the field (Pfeffer et al. 2014 (PMID: 24407213), 2015 (PMID: 26411746), Braunger et al. 2018 (PMID: 29519914), Gemmer et al. 2023 (PMID: 36697828)).

1. Supplementary Figures 1B and 1C appear to suggest that the Ire1i-GFP and Ire1i-NG strains exhibit stronger HAC1 splicing upon DTT treatment. Given this apparent increase in UPR activation, it would be interesting to analyze these strains as well to determine whether they display more pronounced changes in translational states.

We thank the reviewer for raising this interesting point. All strains display ~25% of hibernating ribosomes under ER stress. The corresponding analysis can be found in Sup Figures 4 and 5. We will clarify this point by adding a sentence about this and the reference to the corresponding Sup figures: “First, we observed an increase in the relative abundance of hibernating ribosomes (from 3 to 25%) at the expense of some of the major elongating states, like Dec2 and Pre (from 22% to 16% and from 38% to 17%, (Fig. 3E-F, Supp. Fig. 4D-e). A similar effect was observed in the Ire1i-GFP and Ire1i-NG (Sup. Fig. 4, 5). This increase in inactive 80S complexes is indicative of a reduced translation activity in the cell, that is typically caused by the inhibition of translation initiation.”

There is a difference in the magnitude of HAC1 splicing, but all have sufficiently high HAC1 splicing levels to robustly activate ER stress. This can explain why they all show a similar abundance in hibernating ribosomes.

Minor comments:

1. "FOV" should be defined as "Field of View" upon first use

We will correct the corresponding sentence to: “Cells were then imaged with cryo-ET at an intermediate magnification (6.32-7.09 Å/pix, Field of View (FOV): ~9 µm2), allowing us to laterally capture near-complete cellular ultrastructure in each tomogram (Figure 1B-D)“

1. In Supplementary Figure 7A, the image quality appears insufficient to clearly resolve structures within the autophagic bodies. As a result, it is difficult to determine whether ER-derived membranes are present within these structures. If ER-like membranes are observed, this could suggest induction of ER-phagy under ER stress conditions, consistent with previous reports (e.g., Mizuno et al., PLoS Genetics, 2020).

The tomogram in supplemental Figure 7A does not contain obvious ER-derived membranes. We have observed membranes in other tomograms but our cryo-ET approach does not allow us to identify their origin (ER or other organelles). Therefore, we refrain from making any claims about ER-phagy in our manuscript and limit our discussion to the more general autophagy.

1. In the sentence "Using this approach, we identified 7 distinct ribosome states," the authors should clearly specify which strains and treatment conditions were analyzed. Similarly, statements such as "A similar increase in Dec3 was seen for the other conditions" and "Overall, we observed a consistent, stress-independent increase of the Dec3 state at the ER for all Ire1c-GFP conditions" should explicitly define the corresponding conditions in the text.

We agree that these statements are too vague and we will specify the corresponding conditions in each of these sentences in the revised manuscript.

1. In the sentence "Finally, like for cytosolic ribosome states, we observed that upon ER stress the abundance of hibernating states at the ER increased over time at the expense of other translating states (Dec2 and Pre)," the authors should explicitly reference the corresponding figures.

Agreed, we will refer to the Figure 4D for explicit comparison.

1. In the References section, "Elife" should be corrected to "eLife" for the citation of van Anken et al.

Agreed, we will correct this citation.

1. The enrichment of eEF3 on inactive ribosomes leads the authors to propose a possible role for eEF3 in yeast ribosome hibernation improvement or keep. However, this interpretation currently appears speculative because the map resolution for the external density is relatively limited (~9-15 Å). Could the authors strengthen this claim by performing focused refinement/classification of the eEF3 density, testing eEF3 mutants or depletion strains or examining whether eEF3 occupancy changes quantitatively during stress progression?

Based on the abundance and function of eEF3 we deemed eEF3 the most likely candidate to fit this external density. However, we agree that currently the strength of the claim does not match the strength of the evidence. We will try to improve the local resolution by performing a focused refinement on the eEF3 density. Though, eEF3 is a small density for cryo-ET. In this resolution range we are uncertain whether it will improve the quality of the map in this region. We will quantify the quality of the fit.

Regarding the mutant/depletion strains, eEF3 is essential in yeast and it is also required for translation elongation. Hence depletion strains or interaction mutants will also perturb the role of eEF3 in translation. This strongly limits the possibilities to specifically investigate the functional importance of eEF3 for ribosome hibernation.

1. The current study only examines translational states during ongoing stress exposure and does not investigate whether these changes are reversible after stress resolution.

We thank the reviewer for this interesting point. We hypothesize that the modest translation decrease we observe upon ER stress is most likely reversible. We will check this by including a recovery condition in our polysome profiling experiment.

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

No revisions have been carried out yet.

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

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

1. The authors mainly focus on 80S particles in their analysis for suggesting the different states of ribosomes. However, there is a possibility of free subunits being stored under specific condition. Can the authors comment on free 40S and 60S subunits?

The reviewer is correct and several factors binding free ribosomal subunits have been proposed to play a role in translation inhibition and ribosomal subunit hibernation (Saba et al. EMBO J 2024 (PMID: 39533057)). While we appreciate this interesting perspective, we believe that it is beyond the scope of the present work and that incorporating it would distract from the central focus of the manuscript, namely the effect of ER stress on translation elongation dynamics.

However, if the polysome profiling experiments, now planned based on the suggestions of the reviewers, highlight a significant change in 40S and/or 60s subunit abundance relative to 80S we will try to re-analyze our data, focusing on 40S and 60S subunits.

1. A previous study has reported the storage of dormant ribosomes on the mitochondrial surfaces. Analysis of mitochondria associated dormant ribosomes in S. cerevisiae would shed more light on this phenomenon.

We thank the reviewer for raising this interesting point. Because of our focus on ER stress, our data collection was targeted at the ER, hence only a few of our tomograms contain mitochondria. On the few mitochondria that we did image, we do not observe lattice-like tethering of ribosomes, as described upon glucose starvation in S. Pombe (Gemin and Gluc et al. 2024 (PMID: 39379376)). This tethering is a novel observation, and its function still needs to be explored. Indeed, earlier experiments also indicated that glucose deprivation can induce ribosome binding to mitochondria in S. cerevisiae spheroplasts (Kellems et al., 1975 (PMID: 1092698)). However, initial experiments should first confirm whether this phenomenon also without conversion to spheroplasts before moving on to ER stress.

The structural analysis of mitochondria-associated ribosomes upon ER stress would require new sample preparation of lamellae of control and DTT-treated yeast cells and data collection targeted at mitochondria. It is unlikely to be very different from the modest effect we describe in the cytosol and at the ER membrane. Finally it would distract from the main message of our manuscript centered on the impact of ER stress on translation dynamics. Hence, we consider these experiment beyond the scope of our current work.

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

Were the cryo-FM lamellae maps shown in Fig. S1F-I used to target the tomogram acquisitions? A correlation between the FM and the EM could provide hints about where the Ire1p clusters are located. The puncta are curious somehow, although established in the literature. I'm wondering if they appear somewhere in the tomograms. I would not insist on new experiments to find them, but it would make sense to show if they are already present in the data. Fig S1D does not show a lamella, and it is hard to conclude that the puncta are really absent there. As a general/historical comment, is it clear that the GFP does not affect the protein condensation?

We thank the reviewer for this highly relevant and interesting question. Indeed, the cryo-FM data was used to collect tomograms targeted at Ire1p oligomers. However, none of the conditions (the 3 different cell lines, different timing and different type of stressors) showed detectable clusters in the tomograms.

The absence of clusters can be explained by at least three possible reasons. First, as pointed out by the reviewer, it is possible that the fusion of a fluorescent protein (GFP or NeonGreen) affects the assembly of Ire1p clusters. We think that this is unlikely as these clusters could be visualized by cryoCLEM using a similar fusion constructs in mammalian cells (Tran et al. Science 2021 (PMID: 34591618)). The second possible explanation is a technical limitation. To detect enough fluorescent signal, our cryo-FM data was collected on ~400 nm thick lamellae prior to polishing the lamellae down to Since it is very challenging to convincingly determine which explanation is correct, and it still remains largely speculative to us, we decided to not elaborate on this part of the research effort.*

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

1. For the description of ER volume changes under ER stress, the manuscript currently presents only tomograms from Ire1c-GFP cells treated with DTT. To strengthen this observation, it would be helpful to also include representative tomograms and corresponding segmentations from additional treatments and strains in the supplementary figures.

Indeed we have only collected these low magnification tomograms on a single strain. Similar to HAC1 splicing, ER expansion in response to ER stress is a widely accepted phenomenon (Bernales et al. 2006 (PMID: 17132049), Schuck et al. 2009 (PMID: 19948500)). There is likely only limited potential for new insights from reproducing these data, and we do not feel the resource investment required is justified.

1. While cryo-ET enables structural analysis of small cellular volumes at high resolution, volume EM approaches such as FIB-SEM can provide complementary large-scale ultrastructural information. In particular, samples prepared by high-pressure freezing and freeze substitution generally preserve membrane morphology well and closely resemble native membrane architecture. Incorporating such approaches could further support and complement the cryo-ET observations.

We think that additional volume EM experiments cannot be justified here as the enlargement of ER volume upon ER stress has already been well established through various volume EM approaches (eg; Sriburi et al. 2004 (PMID: 15466483), Bernales et al. 2006 (PMID: 17132049), Schuck et al. 2009 (PMID: 19948500), Heinz et al. 2025 (PMID: 40795978)). Here we only collected additional low magnification tomogram and quantified the ER volume on these to confirm that our experimental conditions lead to a similar ER stress response as previously described. We will add additional references related to this volume EM work to the text to clarify this.

Minor Comments

1. Figure 1: the number of biological replicates (N = 3) is relatively small, particularly considering that yeast samples are generally not difficult to prepare.

The sample size here was not limited by yeast preparation but by cryo-ET data collection time. Because ER expansion upon ER stress is well established in the literature, we only collected a few low magnification tomograms to confirm this effect in our samples, and dedicated most of our microscope time to the collection of high magnification tomograms for the analysis of translation elongation dynamics.

1. In addition to ER volume expansion, were there any detectable changes in nuclear size or nuclear envelope morphology? Since the nuclear envelope is continuous with the ER network, this could provide additional insight into the cellular response to ER stress.

Only a few of our low magnification tomograms contained parts of the nucleus. The few nuclei that we observed may show an increased distance between the nuclear membranes, but we collected too few examples to reliably quantify this effect. Hence we refrained from discussing this in our manuscript, focused on translation elongation.

1. The discussion of alternative pathways remains underdeveloped. Specifically, the authors briefly mention Gcn2p and PKA signaling as potential contributors. Yet no experiments directly test whether the observed ribosome hibernation depends on these pathways. Could the authors clarify: whether eIF2α phosphorylation was induced under their stress conditions, whether Gcn2-deficient strains alter the hibernation phenotype and how much of the observed effect is truly UPR-specific rather than a generic integrated stress response?

We touched upon alternative pathways in the discussion to explain that the observed hibernation was plausible. Since the PERK pathway does not exist in yeast, we expect that some readers might be surprised by our findings. We will adjust this paragraph to improve its readability.

The suggested experiments would show which pathways are activated, however the activation of these pathways has already been described in the literature (Pincus et al., 2014 (PMID: 25275008) ; Patil et al., 2004 (PMID: 15314660)). To really explain which factors directly trigger hibernation, various additional biochemical experiments will have to be performed. This is definitely interesting for future research, but beyond the scope of this cryo-ET focused paper.

We agree that we cannot directly attribute the observed changes to the UPR, that is why we focus on ER stress instead of the UPR. We will double check that this is done consistently throughout the paper.

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Referee #3

Evidence, reproducibility and clarity

This study combines cryo-FIB milling, cryo-electron tomography, and subtomogram averaging to investigate how ER stress affects the translational machinery in S. cerevisiae. The work provides interesting structural insights into ER morphology, autophagy, and ribosome states under stress conditions. The manuscript is generally well written, and the data are of potential interest to the field. However, several aspects of the analysis and presentation would benefit from further clarification and additional supporting data, as outlined below.

Major Comments

1. For the description of ER volume changes under ER stress, the manuscript currently presents only tomograms from Ire1c-GFP cells treated with DTT. To strengthen this observation, it would be helpful to also include representative tomograms and corresponding segmentations from additional treatments and strains in the supplementary figures.
2. While cryo-ET enables structural analysis of small cellular volumes at high resolution, volume EM approaches such as FIB-SEM can provide complementary large-scale ultrastructural information. In particular, samples prepared by high-pressure freezing and freeze substitution generally preserve membrane morphology well and closely resemble native membrane architecture. Incorporating such approaches could further support and complement the cryo-ET observations.
3. For the analysis of ER-bound ribosomes, the authors applied an ellipsoidal mask during subtomogram averaging. However, this masking strategy may not be sufficient because the relative orientation of ribosomes with respect to the ER membrane can be variable, and membrane density may influence particle alignment. The authors may consider including an additional masking step to exclude membrane density and minimize potential alignment bias.
4. Supplementary Figures 1B and 1C appear to suggest that the Ire1i-GFP and Ire1i-NG strains exhibit stronger HAC1 splicing upon DTT treatment. Given this apparent increase in UPR activation, it would be interesting to analyze these strains as well to determine whether they display more pronounced changes in translational states.
5. The study mainly provides structural snapshots and population distributions of ribosomal states, without direct functional measurements of translation activity. Could the authors provide orthogonal biochemical or functional evidence supporting reduced translation under these exact stress conditions?

Minor Comments

1. Figure 1: the number of biological replicates (N = 3) is relatively small, particularly considering that yeast samples are generally not difficult to prepare.
2. "FOV" should be defined as "Field of View" upon first use.
3. In addition to ER volume expansion, were there any detectable changes in nuclear size or nuclear envelope morphology? Since the nuclear envelope is continuous with the ER network, this could provide additional insight into the cellular response to ER stress.
4. In Supplementary Figure 7A, the image quality appears insufficient to clearly resolve structures within the autophagic bodies. As a result, it is difficult to determine whether ER-derived membranes are present within these structures. If ER-like membranes are observed, this could suggest induction of ER-phagy under ER stress conditions, consistent with previous reports (e.g., Mizuno et al., PLoS Genetics, 2020).
5. In the sentence "Using this approach, we identified 7 distinct ribosome states," the authors should clearly specify which strains and treatment conditions were analyzed. Similarly, statements such as "A similar increase in Dec3 was seen for the other conditions" and "Overall, we observed a consistent, stress-independent increase of the Dec3 state at the ER for all Ire1c-GFP conditions" should explicitly define the corresponding conditions in the text.
6. In the sentence "Finally, like for cytosolic ribosome states, we observed that upon ER stress the abundance of hibernating states at the ER increased over time at the expense of other translating states (Dec2 and Pre)," the authors should explicitly reference the corresponding figures.
7. In the References section, "Elife" should be corrected to "eLife" for the citation of van Anken et al.
8. The enrichment of eEF3 on inactive ribosomes leads the authors to propose a possible role for eEF3 in yeast ribosome hibernation improvement or keep. However, this interpretation currently appears speculative because the map resolution for the external density is relatively limited (~9-15 Å). Could the authors strengthen this claim by performing focused refinement/classification of the eEF3 density, testing eEF3 mutants or depletion strains or examining whether eEF3 occupancy changes quantitatively during stress progression?
9. The discussion of alternative pathways remains underdeveloped. Specifically, the authors briefly mention Gcn2p and PKA signaling as potential contributors. Yet no experiments directly test whether the observed ribosome hibernation depends on these pathways. Could the authors clarify: whether eIF2α phosphorylation was induced under their stress conditions, whether Gcn2-deficient strains alter the hibernation phenotype and how much of the observed effect is truly UPR-specific rather than a generic integrated stress response?
10. The current study only examines translational states during ongoing stress exposure and does not investigate whether these changes are reversible after stress resolution.

Significance

General Assessment

This study combines cryo-FIB milling, cryo-electron tomography, and subtomogram averaging to investigate how ER stress affects translational regulation in S. cerevisiae. The work provides valuable in situ structural insights into ER remodeling, autophagy, and stress-associated ribosome states. A major strength of the study is the direct visualization of inactive ribosome populations within native cellular environments. The manuscript is technically strong and generally well presented. However, several conclusions would benefit from additional validation across strains and conditions, clearer description of analyzed datasets, and further methodological clarification regarding ER-bound ribosome analysis.

Advance

The study extends current understanding of the yeast ER stress response by providing structural evidence that ER stress promotes accumulation of inactive ribosome states both in the cytosol and at the ER. Since translational attenuation in S. cerevisiae remains less well characterized compared with metazoan UPR pathways, these findings provide useful mechanistic insight into how yeast cells may reduce translational load during ER stress. The work also highlights the power of cryo-ET for studying translational states directly in situ.

Audience

This work will mainly interest researchers in structural biology, cryo-ET, ribosome biology, ER stress/UPR research, and membrane cell biology. The study is primarily relevant to the basic research community but may also be of broader interest to scientists studying cellular stress responses and proteostasis.

Field of Expertise

Cryo-electron tomography, in situ structural biology, membrane biology.

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Referee #2

Evidence, reproducibility and clarity

de Jager et al investigate the unfolded protein response (UPR) in yeast using an approach of in situ structural biology. As explained in the introduction, metazoans react to ER stress by a number of means, and in particular by reducing the protein folding load by mRNA translation inhibition. (To the non-specialist, this would seem to be simply a non-specific reduction in protein expression at the level of translation. Is that the intent?) Yeast lack key components in the identified DIDD/PERK mechanism of translational control, so the question arises how the inhibition occurs in its absence. The underlying hypothesis proposed here is that ribosome structure may provide an explanation. Indeed, the core of the study was a sub-tomogram analysis of a large number of ribosomes in both non-stressed and stressed conditions. Ribosomes were classified into 7 classes corresponding to stages in the elongation cycle, and a significant increase was found in the fraction of hibernating ribosomes. Under longer stress where autophagy was observed, the ribosomes present in vesicles showed a majority in the hibernating state as might be expected. One might have expected that ER-associated ribosomes would be more strongly inhibited than cytoplasmic ones; this was not observed. The overall fraction of translation-inhibited ribosomes was much lower than observed previously by the same group in human cells, however. It was not clear from the manuscript whether this corresponds to a less-complete shutdown of protein expression in yeast UPR, or whether there must be another mechanism yet to be discovered. This would be an important point for structural biologists less familiar with the specific system. Overall, the work is impressive and should definitely be published.

Major points:

Were the cryo-FM lamellae maps shown in Fig. S1F-I used to target the tomogram acquisitions? A correlation between the FM and the EM could provide hints about where the Ire1p clusters are located. The puncta are curious somehow, although established in the literature. I'm wondering if they appear somewhere in the tomograms. I would not insist on new experiments to find them, but it would make sense to show if they are already present in the data. Fig S1D does not show a lamella, and it is hard to conclude that the puncta are really absent there. As a general/historical comment, is it clear that the GFP does not affect the protein condensation?

Is there a difference in the number polysomes in the non-stressed vs stressed yeast cells? A functional assay, such as polysome profiling combined with nascent-chain labeling might help to support the observation that an increased level of hibernating ribosomes exist in DTT or Tm-treated cells. Has this been considered? Perhaps there is evidence available in the literature?

Minor points:

The new Dec3 state might be clarified a bit further by zooming in to the corresponding areas in the Dec1 and Dec2 structures. This is a point of novelty in the paper and should be emphasized for future reference. Does an additional classification algorithm, such as cryo-DRGN-ET, verify the various states, especially the new Dec3 state? The structures should of course be uploaded to EMDB or another suitable server.

There is generally a lack of supporting quantification, which will bother a number of readers. For example, a "high confidence rigid body fit" shows additional density in the hibrenating state, but what is the confidence? Even the resolution measures of 7-8 Angstrom are simply stated. Presumably they come from a WARP report. There should be some specification for the evaluation. How many lamellae were used, and how many tomograms? Were they taken from different biological experiments, or all collected from the same grid, for each condition?

Significance

The manuscript extends a previous work of the group on UFP in human cells to yeast, where the most relevant biochemical pathway is missing. It follows a very nice publication by the group on human cells. Here, the result is less striking but no less a discovery. Therefore I think it will make a very nice publication, and it is likely to inspire further work to identify further mechanisms involved in stress-dependent translation inhibition.

The approach taken is that of structural biology, where the work defines a state of the art. The conclusions have strongest implications for cell biology, to my taste. Since my own expertise is on the side of cryo-ET I would defer to cell biologists regarding the latter.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The Jager et al., investigated the effect of DTT and Tunicamycin induced ER stress on translation status. They used the cryo-FIB milling and cryo-ET to identify different states of ribosomes and found increased dormant ribosomes occupied with eEF5A, eEF2, and eEF3. The study suggests that ER stress also leads to suppression of translation by increasing the levels of dormant ribosomes in both cytosol and ER membranes.

Major Comments:

1. For identification of hibernating ribosomes, the authors rely mainly on the presence of empty ribosomes along with eEF2, eEF5A, and eEF3. Whether these particles indeed possess known dormancy factors or they are different subclass of empty ribosomes is unclear. Similar analysis in the absence of dormancy factors would strengthen the authors claims.
2. The authors suggest that ER induces modest level of increase in hibernating ribosomes. Adding controls such as glucose deprivation and nitrogen starvation would have provided more strength in relative comparison of these ribosomal sub populations.
3. The authors mainly focus on 80S particles in their analysis for suggesting the different states of ribosomes. However, there is a possibility of free subunits being stored under specific condition. Can the authors comment on free 40S and 60S subunits?
4. The modest reduction in the translation upon ER stress induction could be supported by alternative biochemical assays such as polysome profiling and amino acid incorporation.
5. The authors show the retention of dormant ribosomes on the ER surface. As usual notion of ribosome association with ER membrane to be dependent on nascent translation, retention of dormant ribosomes on ER membrane is interesting and puzzling. Analysis using strains deleted for dormancy factors may provide more insights on this mechanism.
6. A previous study has reported the storage of dormant ribosomes on the mitochondrial surfaces. Analysis of mitochondria associated dormant ribosomes in S. cerevisiae would shed more light on this phenomenon.

Significance

General assessment: The study provides further insights into the regulation of translation under ER stress in yeast in the structural perspective. It provides more insights onto the proportion of different ribosomal populations under normal and ER stress conditions.

Advance: This study provides very useful technical advancement for understanding the proportion of dormant ribosomes to the 80S monosomes which is difficult to segregate using classical biochemical approaches.

Audience: This study will be interesting for the broad readership of structural biology and regulation of protein synthesis and ribosomes.

Field of expertise: Molecular biology, regulation of protein synthesis, mTOR signaling

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Reply to the reviewers

• *

Review Commons: RC-2026-03417

We thank all three reviewers for their thoughtful and constructive evaluations of our manuscript. We are encouraged that the reviewers recognize the significance of identifying a role for the TRAPPIII-Rab1 module in Wingless (Wg) trafficking and secretion. We also appreciate the insightful comments that have helped us identify areas where our interpretations, experimental support, and presentation can be strengthened.

Below, we provide a detailed point-by-point response to all comments and concerns raised by the reviewers.

Reviewer #1

__Evidence, reproducibility and clarity __

Summary

In this manuscript, the authors investigate the role of Transport Protein Particle (TRAPP) complexes in the secretion of Wingless (Wg) in Drosophila. Two TRAPP complexes are known to exist: TRAPPII and TRAPPIII. Through the systematic analysis of individual subunits, the authors identify the requirement of the TRAPPIII subunit TRAPPC8 for Wg trafficking.

They demonstrate that the absence of TRAPPC8 disrupts the retrograde trafficking of both Wg and its carrier Evi, resulting in their intracellular accumulation within Wg- producing cells. Further analyses suggest that TRAPPC8 controls the post-apical internalisation and endosomal trafficking of Wg and Evi. Consistent with the established function of TRAPPIII as a Rab1-specific GEF, they demonstrate that inhibiting Rab1 produces similar effects as depleting TRAPPC8, while constitutively active Rab1 reverses the trafficking defects. Furthermore, depletion of either TRAPPC8 or Rab1 increases the levels of Wg-unbound Evi, suggesting that they act downstream of Evi-Wg dissociation. Taken together, these findings suggest that TRAPPIII and its effector Rab1 are essential regulators of retrograde Wg trafficking, which is necessary for efficient secretion.

Overall, the work is carefully performed and the results are presented clearly. The controls are appropriate and the study expands the functional scope of Rab1-dependent trafficking beyond early secretory pathways. The identification of a previously unrecognised function of TRAPPC8 in Wg trafficking is a valuable contribution.

Major Points

1. It is not entirely clear whether the RNAi lines used in the initial screen were validated for knockdown efficiency. Notably, some core TRAPPIII subunits (e.g., TRAPPC3 and TRAPPC5) do not show a phenotype. This could indicate that the complex retains partial function upon their depletion, or alternatively that the RNAi lines are ineffective. While this point may not critically affect the main conclusion regarding TRAPPC8, it is important for drawing conclusions about the specificity of TRAPPIII versus TRAPPII involvement. For instance, TRAPPC10 (a TRAPPII-specific subunit) was analysed using a single RNAi line, yet no evidence of knockdown efficiency was provided. Validation of these RNAi reagents would strengthen the conclusions regarding complex specificity.

Response: *We thank the reviewer for highlighting this shortcoming in the manuscript. We agree that testing the knockdown efficiency of the TRAPPII complex subunits will strengthen our conclusion on the specificity of TRAPPC8/TRAPPIII towards Wg trafficking. While testing the protein levels would be ideal for checking knockdown efficiency, specific antibodies to these subunits are not commercially available. Therefore, as an alternative approach, we will perform RT-PCR to assess the efficiency of RNAi-mediated depletion of the TRAPPII-specific subunits (TRAPPC9 and TRAPPC10). *

Furthermore, we would also like to highlight that previous studies have reported variable phenotypic outcomes upon loss of TRAPP complex subunits, ranging from no apparent defects to early lethality (Sun and Sui 2023; Riedel et al. 2018). For example, complete deletion of the C9 gene and a frameshift mutation in the C10 gene were found to be homozygously viable, whereas C8 and C11 homozygous mutants showed early larval lethality (Riedel et al., 2018).

*To better contextualize our findings, we will include a more detailed discussion comparing our results with the phenotypes reported for these published mutants, in addition to the RT-PCR analysis of RNAi efficiency. *

Minor Points

In Figure 2C, the clone appears restricted to the apical region, and I do not clearly observe GFP loss in the basolateral domain. Larger clones or additional sections would help clarify the spatial distribution and strengthen the interpretation.

Response - *We thank the reviewer for pointing this out. This issue arises from the pseudostratified nature of the wing epithelium. For smaller clones, such as those observed in the TRAPPC8 mutant, cross-sections can occasionally pass through the tissue at an oblique angle, making it difficult to capture the entire clone within a single section. *

We have repeated the experiment and now provide better images where the apical and basolateral distribution of the mutant clone is visible, and accumulation of exWg can be observed (see updated Figure 2A-C).

The authors should discuss why TRAPPC8 depletion results primarily in apical Wg enrichment, whereas Rab1 inhibition leads to Wg accumulation at both apical and basolateral membranes. This difference may provide insight into whether Rab1 has additional TRAPPIII-independent functions or whether TRAPPC8 affects a more spatially restricted trafficking step.

__ ____Response__: We agree that, while inhibition of either TRAPPC8 or Rab1 led to a strong intracellular accumulation of Wg, subtle differences were observed in the localization of the accumulated Wg. In agreement with your comment and as suggested by previous studies, C8 may direct the Rab1-GEF activity of the core TRAPP complex towards a specific location, while Rab1DN will affect all downstream functions, possibly also including TRAPPIII-independent effects (Riedel et al. 2018; Gyurkovska et al. 2026)*. We will modify the text to incorporate these points more clearly. *

__ ____Significance__

This study broadens our understanding of Rab1-dependent membrane trafficking by identifying a previously unrecognized role for the TRAPPIII complex in retrograde transport during Wingless secretion. ____While the study convincingly establishes the involvement of the TRAPPIII-Rab1 module in Wg trafficking, it does not define the specific retrograde trafficking step that is regulated by this machinery. In addition, the functional relationship between TRAPPIII-Rab1 and established retrograde regulators, such as the retromer complex, is not addressed.

____Response: We thank the reviewer for this comment. This issue was also raised by Reviewer 3. We agree that the precise retrograde trafficking step regulated by the TRAPPC8-Rab1 module remained unclear in the study. To address this, we will perform additional experiments to investigate the functional interactions between TRAPPC8-Rab1 and components of the retrograde trafficking machinery, including the retromer complex, and will incorporate these findings into the revised manuscript. These analyses should help clarify the specific trafficking step controlled by the TRAPPC8-Rab1 module.

Further molecular and mechanistic analyses will be required to position TRAPPIII within the broader retrograde trafficking network and to fully elucidate how Rab1 activity is coordinated with other pathways involved in Wnt secretion. These unresolved issues represent the main limitation of the current study.

__ ____Response__: Wg secretion in polarized epithelial cells involves multiple transport routes and regulatory mechanisms, including exosome-mediated transport, cytonemes, and association with carrier molecules. A systematic analysis of the contribution of TRAPPC8-Rab1 to each of these pathways would require substantial additional investigation and falls outside the scope of the present study.

In this work, we focused on a key, relatively underexplored aspect of Wg transport: the retrograde pathway that mediates the separation and recycling of Wg and Evi/Wls. Our findings identify TRAPPC8-Rab1 as an important component of this process and provide a basis for future studies to define its broader mechanistic integration into intracellular trafficking pathways.

Reviewer #2

__Evidence, reproducibility and clarity __

__Summary Sharma, Sabnis et al. show in this report that TRAPPC8 and Rab1 are important for Wingless (Wg) secretion in developing Drosophila wing discs. - Loss of TRAPPC8 (either knockdown or mutant clones) lead to higher levels of apical Wg in Wg-producing cells (total and extracellular staining). - The levels of the intracellular Wg transporter Evi/Wls are also increased, in particular in its 'unbound' form. - A similar phenotype is observed upon overexpression of Rab1 dominant negative. - Overexpression of constitutively active Rab1 has no effect in otherwise wild type discs but does rescue the effect of TRAPPC8 loss of function.

Major concerns 1) The author's key message is that TRAPPC8 is essential for retrograde transport of Wg and Evi. However, in apparent contradiction, TRAPPC8 loss does not appear to affect the basolateral distribution of exWg (or total Evi) (Fig2B', FigS3). Therefore, while Wg transport may be less efficient in the absence of TRAPPC8, the conclusion that TRAPPC8 is essential should be toned down. It is warranted to suggest that transport of unbound Evi is disrupted in the absence of TRAPPC8, as unbound Evi increases apically and is lost basally (Fig 4A-B).__

Response:

*Thank you for these comments, which prompted us to retest the extracellular Wg levels in these experiments. We repeated the experiments and reanalyzed the basolateral distribution of extracellular Wg in TRAPPC8-depleted cells. While we consistently observed an increase in apical extracellular Wg, the effects on basolateral Wg were more variable. In several samples, basolateral Wg appeared largely unaffected, whereas in others we observed some reduction. We speculate that this variability may arise from differences in RNAi efficiency, with stronger depletion of TRAPPC8 potentially required to reveal basolateral defects. Furthermore, these defects are completely rescued by the expression of Rab1CA, indicating Rab1-dependent effects of TRAPPC8 loss. *

*We apologize for this oversight in our analysis in the original manuscript and would like to correct our conclusions regarding the basolateral Wg. We have included both results in the partially revised manuscript, indicating the variability observed in the basolateral Wg, albeit with consistent apical accumulation of extracellular Wg. *

Furthermore, we have modified the statement (line 235, page 8) "These results suggest that TRAPPC8 functions after the dissociation of the Evi-Wg complex, likely promoting proper sorting of Evi and Wg within maturing endosomes" to "These results suggest that TRAPPC8 functions after the dissociation of the Evi-Wg complex, likely affecting proper retrograde trafficking of unbound-Evi."

Pending revision: *We will further update our discussion section to include these points after completing all additional experiments suggested by the reviewers. *

2) The relative roles of Rab1 and TRAPPC8 are not equally considered. As the authors show, unlike TRAPPC8 loss of function, Rab1 DN causes a decrease in basal exWg. Doesn't this suggest that Rab1 is more important for Wg trafficking than TRAPPC8?

Response: This issue is addressed in the previous comment.

a) Rab1 DN causes also accumulation of total basal Wg. Does this mean that Wg can be trafficked basally but fails to be secreted at the basal surface?

Response: Yes, we agree with this interpretation. In Rab1DN-expressing cells, total Wg accumulates throughout the cell, including at the basal side, while basolateral extracellular Wg is reduced. This suggests that Wg-containing vesicles can reach the basolateral region but are inefficiently secreted at the basal surface. One possibility is that Rab1 function is required for the apical-to-basolateral transcytosis and/or the final delivery of Wg-containing vesicles to sites of basolateral secretion.

b) A similar assay (total basal Wg) is lacking in condition of TRAPPC8 loss (clones or RNAi); only exWg is shown.__

Response: We will also include the basolateral sections of total Wg in TRAPPC8 depletion conditions (mutant clones and RNAi) in the revised manuscript.

c) Also needed is an assessment of total and exWg at the basal surface in the Rab1 CA experiment. Based on the cross-section image shown in Fig6B, it seems that the distribution of Wg might be more confined to the apical plane of the cells compared to other conditions (Fig6F for example), but there is little difference in this regard between the anterior and posterior compartments.__

Response: *We thank the reviewer for this important point, and we will reanalyze both total and extracellular Wg levels in Rab1CA samples, specifically the apical and basolateral distributions and provide images in the revised manuscript. *

3) A significant claim of the paper is "TRAPPC8 regulates retrograde Wg trafficking post-apical internalization". a. The increase in apical extracellular Wg (FigS3), which seems to remain associated with the membrane of Wg-producing cells (i.e. no onward spread) would suggest that apical internalization may be affected, but this is not considered by the authors.

Response: *We agree that the increased apical extracellular Wg observed in Fig. S3 (now Fig 2D-F and S3) could also suggest alterations in apical uptake dynamics. However, based on our internalization assay, we believe that the major defect is likely in the post-endocytic sorting/trafficking of Wg after apical internalization rather than a complete block in internalization itself. In these internalization assays, following the internalization pulse, the tissue was subjected to a brief acid wash to remove extracellular and surface-bound antibody. At the same time, the internalized antibody-antigen complexes remain protected. Therefore, the Wg signal detected after the acid wash represents internalized apical Wg, demonstrating that apical internalization does occur in the TRAPPC8 loss condition. *

4) From the antibody chase experiment, it is not clear if the effect of TRAPPC8 loss affects endocytosis and/or trafficking in general or whether it is specific to Wg and Evi. A fluorescent Dextran control should be included as in Witte et al., 2020 (https://doi.org/10.1242/dev.186833 ). Also, can the authors be sure that they are visualising internalised Wg and not just internalised Wg antibody? Can the author show a field of view where Wg is not expressed?

__ Response: __Thank you for this important suggestion. We would first like to clarify that the Wg internalization assay, using the highly specific monoclonal anti-Wg antibody, is an established approach that has been used in multiple previous studies to monitor Wg internalization and trafficking (Hemalatha et al. 2016; Sharma and Chaudhary 2024)*. Furthermore, as shown in Figure S4C-C′ (now moved to Fig 3D), the internalized Wg signal is detected specifically in cells close to the DV boundary, while more distal receiving cells do not show comparable staining. This spatially restricted pattern strongly supports the specificity of the assay for Wg-producing cells and a limited number of nearby receiving cells that may internalize secreted Wg, rather than nonspecific internalization of the antibody alone. We will revise the text to clarify this point in the revised manuscript. *

To address whether TRAPPC8 loss affects general endocytosis, we will perform a fluorescent Dextran uptake assay, as suggested by the reviewer and similar to the approach described by (Witte et al. 2020)*. *

5) The authors suggest that TRAPPC8 loss leads to increased Rab7 levels. This is taken as evidence for a role of acidification in driving Wg dissociation from Evi, with TRAPPC8 acting downstream to sort Wg from mature endosomes. ____Neither of these claims are supported because in Fig.S3G loss of TRAPPC8 results in an increase in Rab7 everywhere except at the DV boundary where the Wg-producing cells are. This should be acknowledged in text, and these data should appear in the main Fig4.

Response: To address this concern, we have repeated the experiment and reanalyzed the RAb7 and lysotracker levels specifically in cells at the DV boundary. The data is now moved to the updated main Figure 5E-F and 5G-H. A significant increase in both lysotracker and Rab7 can be observed, suggesting that loss of TRAPPC8 affected late endosomal maturation.

a) The increase in lysotracker also does not support the above claims as it could be due to an increase in unbound Evi that cannot be trafficked back to the ER (and hence targeted for degradation in lysosomes).

Response: We respectfully disagree with this interpretation. If TRAPPC8 loss primarily caused increased lysosomal degradation of unbound Evi, we would expect a reduction in total Evi levels, as observed upon loss of retromer function, in which Evi is diverted to lysosomes and specifically depleted in Wg-producing cells (Port et al. 2008). In contrast, we observe an accumulation of both total and unbound Evi in TRAPPC8-depleted cells (Figures 4A-D and 5A-D), arguing against enhanced lysosomal degradation as the primary defect.

b) In fig S3G, the purported Rab7 increase in the posterior compartment is not readily apparent (and not quantified), in contrast to the authors' description of the effect of TRAPPC8 depletion. This suggest that the model proposed by the authors needs to be revised (Fig6G) and the relevant paragraphs from Results and Discussion section must be significantly edited or removed.

Response: We apologize for the lack of clarity in our previous images. As noted above, we now observe a significant increase in Rab7 and Lysotracker signals in Wg-producing cells, indicating an expansion of Rab7-positive acidic late endosomal compartments upon TRAPPC8 depletion. Furthermore, our interpretation is consistent with our previous findings showing that the Evi-Wg complex dissociates within maturing endosomes.

Minor concerns 1) The way data in Fig 2, S3 and S4 is presented and referred to in text could be rearranged slightly to make it easier to follow: first talk about the work using clones (Fig2, FigS4 becomes FigS3), then mention similar results with the knockdown (FigS3 becomes FigS4). This arrangement would link naturally to the effect on Evi.

Response: Thanks for your suggestion, we have revised the supplementary figure order by changing FigS3 (now Fig S4) to FigS4 (now Fig S5) and FigS4 (now Fig S5) to FigS3 (now Fig S4), and the corresponding figure references in the main text have been updated accordingly. We have also moved some of the RNAi data from Fig S3 to main figures (Fig 2D-F and Fig 3D-F) to increase the clarity and make the results easier to follow.

2) How do the authors explain that the knockdown of some core TRAPP subunits does not have a phenotype? Some sort of rationalisation (or experimental follow up) is desirable.

*__Response: __The lack of a detectable phenotype following knockdown of some core TRAPP subunits may reflect several possibilities. Previous studies have suggested that certain core subunits, including TRAPPC2, TRAPPC2L, TRAPPC6A and TRAPPC6B, are not universally required for mammalian cell viability, indicating potential functional redundancy or their context-dependent requirements within the TRAPP core complex (Lipatova and Segev, 2019; Sun and Sui, 2023). It is also possible that residual protein levels after RNAi-mediated depletion are sufficient to support partial TRAPP function. Testing the RNAi-mediated protein depletion of these subunits is beyond the scope of the current study. *

*We would like to highlight that the focus of the study is TRAPPC8, a TRAPPIII-specific subunit, which was validated with a genomic mutation. However, to strengthen our conclusions regarding the TRAPPIII-specific effect, we will validate the known efficiency of the TRAPPII complex subunits with RT-PCR, also addressing the comment from Reviewer 1. *

3) The authors should give more detail about how they quantified normalised intensity profiles and clarify if the profiles correspond to just the representative image shown or the average of multiple discs (possible for the compartment experiments, but presumably impossible for the clone experiments as they would need to normalise by the size of the clone too).

Response: *Thank you. We have updated the figure legend to clearly indicate the representative images corresponding to each plot profile. The plot profiles were generated from representative images only and do not represent averages from multiple discs. The intensity values were normalized by dividing each value by the mean intensity across the quantified region. We have also added this information in the Materials and Methods section (line 447, page 16). *

__ ____Significance__

This report is a valuable report for the Wg secretion subfield, and useful for the Wnt community. It makes some interesting observations and brings the importance of Rab1 back into the conversation after Ching et al., 2008. However, the insight remain limited and the mechanism/trafficking defects remain unclear. There is convincing evidence that TRAPPC8 and Rab1 affect Wg and Evi, but the claims that TRAPPC8 is essential and acts downstream of acidic endosomes is inadequate.

__ ____Response:__ * Please refer to the responses for Reviewer 3. We have addressed these concerns in the next section.*

Reviewer #2 (Significance (Required)):

__This report is a valuable report for the Wg secretion subfield, and useful for the Wnt community. It makes some interesting observations and brings the importance of Rab1 back into the conversation after Ching et al., 2008. However, the insight remain limited and the mechanism/trafficking defects remain unclear. There is convincing evidence that TRAPPC8 and Rab1 affect Wg and Evi, but the claims that TRAPPC8 is essential and acts downstream of acidic endosomes) is inadequate. ____ __

__Reviewer #3 __

This manuscript uncovers a direct or indirect role of RAB1/TRAPPIII in regulating the intracellular fate of Wng in the columnar epithelial cells of the wing imaginal disc of the fruit fly. This observation is interesting, although it should come as no surprise that, given the fact that Wnts are secreted morphogens and considering the involvement of TRAPPIII in the early stages of the secretory pathway, the key TRAPPIII subunit, TRS85/TRAPPC8, is crucial for their normal trafficking. The main finding of this work is that cells deficient in TRAPPIII/RAB1 accumulate the morphogen and its receptor in the apical region of morphogen-producing cells, which is interpreted as a block in the retrograde trafficking of the morphogen.

---

1) While it is unclear to me what the authors consider as retrograde trafficking of Wng (see below), the arguments fall short of being convincing, in part because the intracellular trafficking of Wng is rather intricate, but also because the physiological role of TRAPPIII is insufficiently understood. It is well established that Wng transits through endosomes to reach multivesicular bodies, where it is incorporated into the inwardly budding vesicles that are secreted as exosomes (Gross et al, cited). Do the authors consider this a retrograde pathway? The authors do not delineate further the location at which Wng accumulates, for example using co-localization studies.

Response: *We would like to clarify that, in our manuscript, we use the term "retrograde trafficking" specifically to describe the trafficking route followed by apically internalized Wg/Evi complexes through the endosomal system before their re-secretion from Wg-producing cells. *

*Wg trafficking after internalization is highly complex and can involve multiple intracellular routes. Importantly, besides trafficking of internalized Wg to multivesicular bodies (MVBs) for exosomal secretion, other pathways downstream of apical internalization have also been reported, including Rab4-dependent apical recycling, apical-to-basolateral transcytosis involving HSPGs, and secretion of Wg on lipoprotein particles. Testing the effect of TRAPPC8 in multiple trafficking routes is currently beyond the scope of this study. *

*Our current study does not attempt to distinguish between these individual downstream secretory routes. Rather, our data support a requirement for TRAPPC8/Rab1 in trafficking steps occurring after apical internalization of Wg/Evi and before their redistribution and/or re-secretion. The detailed characterization of the precise endosomal compartments and carrier-specific secretion mechanisms affected by TRAPPC8/Rab1 will require significant additional lines of experiments, which are beyond the scope of the current work. *

__2) They have also not provided a rationalization of their observations with current knowledge of retrograde trafficking between the endosomes and the Golgi. It would have been interesting to address the effects of Trs85 depletion in mutant backgrounds deficient in the master regulator of retrograde pathways, RAB6, its effector, the GARP complex, or RAB7 and the retromer; it would have been important to study TRAPPIII depletion under conditions in which endocytic internalization is blocked, or the biogenesis of multivesicular bodies is prevented. __

__ ____Response: __We agree that understanding the functional relationship between TRAPPIII and other retrograde trafficking regulators would provide important mechanistic insight into Wg/Evi trafficking.

*Among the known regulators of retrograde trafficking, we are particularly interested in testing the functional interaction between TRAPPC8 and the retromer complex, as retromer is one of the best-characterized regulators of Evi recycling in the Drosophila Wg pathway (Port et al., 2008; Franch-Marro et al., 2008; Belenkaya et al., 2008). Therefore, we will analyze the functional interactions between TRAPPC8 and retromer components and provide results in the revised manuscript. *

However, the roles of other retrograde trafficking regulators, such as GARP and Rab6, in retrograde Wg trafficking in Drosophila are not yet well established and would first require independent characterization before meaningful epistasis analyses with TRAPPIII can be performed.

*Regarding the suggestion to block endocytic internalization, our antibody internalization experiments indicate that early Wg internalization, including uptake of Wg in neighboring receiving (non-secreting) cells, is not detectably affected upon TRAPPC8 or Rab1 depletion. These observations suggest that TRAPPC8 and Rab1 are unlikely to play a general role in endocytic uptake. *

We therefore focused our analyses on post-internalization trafficking events affecting Wg and Evi. Furthermore, blocking endocytosis globally would likely introduce strong secondary effects on both Evi-Wg complex internalization in secreting cells and uptake of extracellular Wg in receiving cells, making it difficult to distinguish direct effects on retrograde trafficking from broader defects in Wg trafficking dynamics.

__Specific comments __

3) There are no page or line numbers, which makes very cumbersome to comment on specific sections of the manuscript.

*__Response: __We apologize for this inconvenience and have now added page and line numbers. *

__4) The introduction contains a factual mistake. TRAPPC11, 12, and 13 are not metazoan specific. They are present in fungi but have been lost in Saccharomyces cerevisiae. Pinar M, Arias-Palomo E, de Los Ríos V, Arst HN Jr, Peñalva MA. Characterization of Aspergillus nidulans TRAPPs uncovers unprecedented similarities between fungi and metazoans and reveals the modular assembly of TRAPPII. PLoS Genet. 2019 Dec 23;15(12):e1008557. doi: 10.1371/journal.pgen.1008557. This reference should have been cited. __

Response: *We thank the reviewer for pointing this out and apologize for missing this reference. We have now updated the text and added the reference (see line 83 on page 3). *

__5) Materials and methods are very incomplete, particularly in the section that deals with the antibodies, which are essential tools for understanding the experiments. __

__Is the Wnt antibody a monoclonal antibody? __

__Are there different antibodies specific for extracellular and intracellular Wnt? __

__What is the molecular basis for this differential detection? __

__The transgene expressing GFP under the engrailed driver is not described anywhere. __

__ ____Response:__ We apologize for the lack of sufficient detail in the Materials and Methods section. We have now revised this section to include the missing methodological details and clarifications requested by the reviewer.* *

For all Wg-related stainings, including total, extracellular, and internalization assays, we used the mouse monoclonal anti-Wg antibody obtained from DSHB. Antibody details and working dilutions are provided in the revised Materials and Methods section.

The differential detection of extracellular versus total Wg does not arise from the use of different antibodies, but rather from differences in the staining protocol. Total Wg staining was performed after permeabilization of wing imaginal discs using 0.2% Triton X-100 in 1X PBS, allowing detection of both intracellular and extracellular Wg pools. In contrast, extracellular Wg staining was performed without tissue permeabilization, thereby restricting antibody access to extracellular or cell surface-associated Wg. Similarly, the Wg internalization assay was performed using established protocols already described in the manuscript. We have now updated the Materials and Methods section to include additional details for the extracellular Wg staining procedure (line 409, page 14).

• *The GFP expression used in our study is driven by the Gal4-UAS system, where engrailed-Gal4 (en-Gal) drives UAS-GFP expression. We have provided the details for these two fly lines in the Drosophila stocks section in Materials and Methods. For our experiments, we generated a recombinant fly stock having both en-Gal and UAS-GFP on the second chromosome using Drosophila genetics, and this genotype, along with different combinations of genes, is listed in our Supplementary Information.

• *__6) The labeling of the figures and the figure legends themselves are excessively simple and appear to be accessible for fly experts only. __

Response: We thank the reviewer for this suggestion. We have revised the details for labeling the figure in the legends and expanded the figure legends to improve clarity and accessibility for a broader audience. In particular, we added more detailed descriptions of the specific images with reference to their corresponding quantified graphs (as also suggested by Reviewer 2). We also incorporated additional minor explanatory details (for example, GFP-negative clones mean the homozygous mutant) wherever necessary to help non-fly experts to better understand the figures.

__7) The authors have not considered the possibility that ablating TRAPPC8 of TRAPPIII can have off-target effects in TRAPPII. It would have been very interesting to address the phenotype of down-regulating TRAPPII and of down-regulating one of the core subunits of TRAPPs. __

__ ____ Response: __*If the reviewer is suggesting the off-target effects of TRAPPC8 RNAi on TRAPPII complex member, we would like point out that the observations from the RNAi were validated by the TRAPPC8 mutant. However, if the concern is whether TRAPPC8 loss functionally affected TRAPPII complex besides TRAPPIII, then it we have not directly tested this. However, several past studies have shown that TRAPPC8 is a TRAPPIII-specific subunit and not part of TRAPPII complex. Furthermore, and more importantly, we have rescued the RNAi phenotype with the expression of Rab1CA, indicating the effects TRAPPIII-specific are unlikely to be via the TRAPPII-Rab11 pathway. *

__8) Figure 1, Panel 1i: What is the basis at this point that justifies "likely by altering intra-cellular trafficking"? __

Response: Since loss of TRAPPC8 resulted in increased levels of total Wg, we wanted to determine whether this increase could be due to transcriptional upregulation of wg. To address this, we examined the established wg-LacZ reporter and found that its expression was not altered upon loss of TRAPPC8 (Fig 1i).

Therefore, the increased Wg levels are unlikely to arise from increased wg transcription. In addition, previous studies have shown that loss of Evi/Wls leads to intracellular accumulation of Wg as a consequence of trafficking defects rather than transcriptional regulation. Based on these observations, we concluded that the accumulation of Wg upon TRAPPC8 depletion is more likely due to altered intracellular trafficking.

__9) Several figures: where are the boundaries of the cells in orthogonal views? If GFP labels whole cells, why is there an area at the top of the cross-sections that hasn't got GFP staining? __

__ ____Response:__ In all orthogonal views of the GFP-negative mutant clones, we have used dotted lines to indicate the clone boundaries. The wing disc epithelium consists of two distinct epithelial layers: a squamous epithelium (the peripodial membrane) and a pseudostratified columnar epithelium. Although GFP-negative clones are generated in both layers, our analysis focuses specifically on the columnar epithelium, where Wg is expressed. Therefore, the signal observed from the peripodial membrane can vary in the orthogonal views and does not affect our interpretation of Wg localization in the columnar cells.

__10) I can follow the point that accumulation in the apical side means that retrograde trafficking is impaired. I miss the connection between the observation and the conclusion. __

Response: We apologize for the lack of clarity in explaining the retrograde trafficking defects and would like to clarify this point for Wg.

In our experiments, we performed both total Wg staining (predominantly intracellular) and extracellular Wg staining. The apical accumulation observed in total Wg staining upon TRAPPC8/Rab1 depletion, by itself, does not directly demonstrate impaired retrograde trafficking. However, the increase in extracellular Wg indicates that Wg can still reach the plasma membrane, suggesting that the anterograde delivery pathway remains functional.

Our conclusion regarding defective retrograde trafficking is primarily based on the antibody internalization assays. In these experiments, internalized Wg and Evi accumulate intracellularly upon loss of TRAPPC8/Rab1, consistent with a defect in post-endocytic trafficking and recycling. Since both Wg and Evi normally undergo endocytic recycling through retrograde pathways, the accumulation of internalized Evi and Wg supports the interpretation that retrograde trafficking is impaired in TRAPPC8/Rab1-depleted cells.

__11) VPS34 is an effector of RAB5 and therefore its down-regulation impairs the maturation of early endosomes because their membranes cannot acquire the key component phosphatidylinositol-3-phosphate, which is recognized by the ESCRT machinery to proceed with multivesicular body biogenesis. __

__ ____Response: __We agree with the reviewer that VPS34 acts as an effector of Rab5 and plays an important role in early endosome maturation. However, more recent studies have shown that VPS34 functions within two related but functionally distinct complexes, VPS34 complex I and VPS34 complex II. VPS34 complex II, which contains UVRAG, functions predominantly in the endolysosomal system and is associated with Rab5. In contrast, VPS34 complex I, which contains Atg14, functions in autophagy and has been shown to interact with Rab1. Importantly, Rab1 and Rab5 bind VPS34 in a mutually exclusive manner at overlapping interaction sites (Scott and Burke 2026; Cook et al. 2025; Špokaitė et al. 2026; Tremel et al. 2021)*. *

• *Therefore, while the reviewer's interpretation regarding Rab5-dependent VPS34 function in endosomal maturation is fully valid, these studies also support the possibility that Rab1 can regulate VPS34-dependent trafficking pathways through a distinct VPS34 complex.

__12) The Q70L mutation, widely used as a constitutive activator of RABs, is borrowed from studies in RAS and it might not lead to constitutive activation of RAB1 (Langemeyer, L., Nunes Bastos, R., Cai, Y., Itzen, A., Reinisch, K.M., and Barr, F.A. (2014). Diversity and plasticity in Rab GTPase nucleotide release mechanism has consequences for Rab activation and inactivation. eLife 3, e01623). __

Response: We thank the reviewer for raising this important point. We admit that we have not performed an independent analysis of the GTP-locked status of the Rab1Q70L mutant in flies. Our rationale for using Rab1Q70L as a GTP-locked or functionally hyperactive Rab1 variant is based on its extensive prior use in the field (Tisdale et al. 1992; Levin et al. 2016; Russo et al. 2016; van Vliet et al. 2026). Importantly, a past study in Drosophila has shown functional hyperactivity of the Rab1Q70L compared with WT Rab1 (Sechi et al. 2017)*. ** *

References (response to reviewers):

Cook, Annan S. I., Minghao Chen, Thanh N. Nguyen, et al. 2025. "Structural Pathway for PI3-Kinase Regulation by VPS15 in Autophagy." Science (New York, N.Y.) 388 (6743): eadl3787.

Gyurkovska, Valeriya, Rakhilya Murtazina, Sarah F. Zhao, Christopher B. Huppenbauer, Vadim Gaponenko, and Nava Segev. 2026. "Distinct TRAPP Complexes Activate Ypt/Rab GTPases in Secretion and Autophagy." The Journal of Cell Biology 225 (5). https://doi.org/10.1083/jcb.202507166.

Hemalatha, Anupama, Chaitra Prabhakara, and Satyajit Mayor. 2016. "Endocytosis of Wingless via a Dynamin-Independent Pathway Is Necessary for Signaling in Drosophila Wing Discs." Proceedings of the National Academy of Sciences of the United States of America 113 (45): E6993-E7002.

Levin, Rebecca S., Nicholas T. Hertz, Alma L. Burlingame, Kevan M. Shokat, and Shaeri Mukherjee. 2016. "Innate Immunity Kinase TAK1 Phosphorylates Rab1 on a Hotspot for Posttranslational Modifications by Host and Pathogen." Proceedings of the National Academy of Sciences of the United States of America 113 (33): E4776-83.

Nakajima, Yu-Ichiro. 2021. "Analysis of Epithelial Architecture and Planar Spindle Orientation in the Drosophila Wing Disc." Methods in Molecular Biology (Clifton, N.J.) (New York, NY), Methods in molecular biology (Clifton, N.J.), vol. 2346: 51-62.

Port, Fillip, Marco Kuster, Patrick Herr, et al. 2008. "Wingless Secretion Promotes and Requires Retromer-Dependent Cycling of Wntless." Nature Cell Biology 10 (2): 178-185.

Riedel, Falko, Antonio Galindo, Nadine Muschalik, and Sean Munro. 2018. "The Two TRAPP Complexes of Metazoans Have Distinct Roles and Act on Different Rab GTPases." The Journal of Cell Biology 217 (2): 601-617.

Russo, Ashley J., Alyssa J. Mathiowetz, Steven Hong, Matthew D. Welch, and Kenneth G. Campellone. 2016. "Rab1 Recruits WHAMM during Membrane Remodeling but Limits Actin Nucleation." Molecular Biology of the Cell 27 (6): 967-978.

Scott, Mackenzie K., and John E. Burke. 2026. "Two Binding Sites Are Better than One." eLife 15 (e110917). https://doi.org/10.7554/eLife.110917.

Sechi, Stefano, Anna Frappaolo, Roberta Fraschini, et al. 2017. "Rab1 Interacts with GOLPH3 and Controls Golgi Structure and Contractile Ring Constriction during Cytokinesis in Drosophila Melanogaster." Open Biology 7 (1): 160257.

Sharma, Satyam, and Varun Chaudhary. 2024. "Dissociation of Drosophila Evi-Wg Complex Occurs Post Apical Internalization in the Maturing Acidic Endosomes." Traffic (Copenhagen, Denmark) 25 (9): e12955.

Špokaitė, Saulė, Yohei Ohashi, Maxime Bourguet, Antoine N. Dessus, and Roger L. Williams. 2026. "A Novel RAB5 Binding Site in Human VPS34-CII That Is Likely the Primordial Site in Eukaryotic Evolution." In eLife. ELife, March 31. https://doi.org/10.7554/elife.110040.

Sun, Shan, and Sen-Fang Sui. 2023. "Structural Insights into Assembly of TRAPPII and Its Activation of Rab11/Ypt32." Current Opinion in Structural Biology 80 (102596): 102596.

Tisdale, E. J., J. R. Bourne, R. Khosravi-Far, C. J. Der, and W. E. Balch. 1992. "GTP-Binding Mutants of rab1 and rab2 Are Potent Inhibitors of Vesicular Transport from the Endoplasmic Reticulum to the Golgi Complex." The Journal of Cell Biology 119 (4): 749-761.

Tremel, Shirley, Yohei Ohashi, Dustin R. Morado, et al. 2021. "Structural Basis for VPS34 Kinase Activation by Rab1 and Rab5 on Membranes." Nature Communications 12 (1): 1564.

Vliet, Alexander R. van, Alison K. Gillingham, Tomos E. Morgan, et al. 2026. "A Rab1 Interactome Illuminates a Dual Role in Autophagy and Membrane Trafficking." The Journal of Cell Biology 225 (3): e202507084.

Witte, Leonie, Karen Linnemannstöns, Kevin Schmidt, et al. 2020. "The Kinesin Motor Klp98A Mediates Apical to Basal Wg Transport." Development 147 (15). https://doi.org/10.1242/dev.186833.

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Referee #3

Evidence, reproducibility and clarity

This manuscript uncovers a direct or indirect role of RAB1/TRAPPIII in regulating the intracellular fate of Wng in the columnar epithelial cells of the wing imaginal disc of the fruit fly. This observation is interesting, although it should come as no surprise that, given the fact that Wnts are secreted morphogens and considering the involvement of TRAPPIII in the early stages of the secretory pathway, the key TRAPPIII subunit, TRS85/TRAPPC8, is crucial for their normal trafficking. The main finding of this work is that cells deficient in TRAPPIII/RAB1 accumulate the morphogen and its receptor in the apical region of morphogen-producing cells, which is interpreted as a block in the retrograde trafficking of the morphogen. While it is unclear to me what the authors consider as retrograde trafficking of Wng (see below), the arguments fall short of being convincing, in part because the intracellular trafficking of Wng is rather intricate, but also because the physiological role of TRAPPIII is insufficiently understood. It is well established that Wng transits through endosomes to reach multivesicular bodies, where it is incorporated into the inwardly budding vesicles that are secreted as exosomes (Gross et al, cited). Do the authors consider this a retrograde pathway? The authors do not delineate further the location at which Wng accumulates, for example using co-localization studies. They have also not provided a rationalization of their observations with current knowledge of retrograde trafficking between the endosomes and the Golgi. It would have been interesting to address the effects of Trs85 depletion in mutant backgrounds deficient in the master regulator of retrograde pathways, RAB6, its effector, the GARP complex, or RAB7 and the retromer; it would have been important to study TRAPPIII depletion under conditions in which endocytic internalization is blocked, or the biogenesis of multivesicular bodies is prevented.

Specific comments

There are no page or line numbers, which makes very cumbersome to comment on specific sections of the manuscript.

The introduction contains a factual mistake. TRAPPC11, 12, and 13 are not metazoan specific. They are present in fungi but have been lost in Saccharomyces cerevisiae. Pinar M, Arias-Palomo E, de Los Ríos V, Arst HN Jr, Peñalva MA. Characterization of Aspergillus nidulans TRAPPs uncovers unprecedented similarities between fungi and metazoans and reveals the modular assembly of TRAPPII. PLoS Genet. 2019 Dec 23;15(12):e1008557. doi: 10.1371/journal.pgen.1008557. This reference should have been cited.

Materials and methods are very incomplete, particularly in the section that deals with the antibodies, which are essential tools for understanding the experiments. Is the Wnt antibody a monoclonal antibody? Are there different antibodies specific for extracellular and intracellular Wnt? What is the molecular basis for this differential detection? The transgene expressing GFP under the engrailed driver is not described anywhere.

The labeling of the figures and the figure legends themselves are excessively simple and appear to be accessible for fly experts only.

The authors have not considered the possibility that ablating TRAPPC8 of TRAPPIII can have off-target effects in TRAPPII. It would have been very interesting to address the phenotype of down-regulating TRAPPII and of down-regulating one of the core subunits of TRAPPs.

Figure 1, Panel 1i: What is the basis at this point that justifies "likely by altering intra-cellular trafficking"?

Several figures: where are the boundaries of the cells in orthogonal views? If GFP labels whole cells, why is there an area at the top of the cross-sections that hasn't got GFP staining?

I can follow the point that accumulation in the apical side means that retrograde trafficking is impaired. I miss the connection between the observation and the conclusion.

VPS34 is an effector of RAB5 and therefore its down-regulation impairs the maturation of early endosomes because their membranes cannot acquire the key component phosphatidylinositol-3-phosphate, which is recognized by the ESCRT machinery to proceed with multivesicular body biogenesis.

The Q70L mutation, widely used as a constitutive activator of RABs, is borrowed from studies in RAS and it might not lead to constitutive activation of RAB1 (Langemeyer, L., Nunes Bastos, R., Cai, Y., Itzen, A., Reinisch, K.M., and Barr, F.A. (2014). Diversity and plasticity in Rab GTPase nucleotide release mechanism has consequences for Rab activation and inactivation. eLife 3, e01623).

Referee cross-commenting

I also feel that six months is a more realistic estimation

Significance

In summary an interesting observation that deserves a more detailed follow-up to unveil the actual role of TRAPPIII in the Wng pathway.

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Referee #2

Evidence, reproducibility and clarity

Summary

Sharma, Sabnis et al. show in this report that TRAPPC8 and Rab1 are important for Wingless (Wg) secretion in developing Drosophila wing discs.

• Loss of TRAPPC8 (either knockdown or mutant clones) lead to higher levels of apical Wg in Wg-producing cells (total and extracellular staining).
• The levels of the intracellular Wg transporter Evi/Wls are also increased, in particular in its 'unbound' form.
• A similar phenotype is observed upon overexpression of Rab1 dominant negative.
• Overexpression of constitutively active Rab1 has no effect in otherwise wild type discs but does rescue the effect of TRAPPC8 loss of function.

Major concerns

1) The authors key message is that TRAPPC8 is essential for retrograde transport of Wg and Evi. However, in apparent contradiction, TRAPPC8 loss does not appear to affect the basolateral distribution of exWg (or total Evi) (Fig2B', FigS3). Therefore, while Wg transport may be less efficient in the absence of TRAPPC8, the conclusion that TRAPPC8 is essential should be toned down. It is warranted to suggest that transport of unbound Evi is disrupted in the absence of TRAPPC8, as unbound Evi increases apically and is lost basally (Fig4A-B).

2) The relative roles of Rab1 and TRAPPC8 are not equally considered. As the authors show, unlike TRAPPC8 loss of function, Rab1 DN causes a decrease in basal exWg. Doesn't this suggest that Rab1 is more important for Wg trafficking than TRAPPC8? a. Rab1 DN causes also accumulation of total basal Wg. Does this mean that Wg can be trafficked basally but fails to be secreted at the basal surface? b. A similar assay (total basal Wg) is lacking in condition of TRAPPC8 loss (clones or RNAi); only exWg is shown. c. Also needed is an assessment of total and exWg at the basal surface in the Rab1 CA experiment. Based on the cross-section image shown in Fig6B, it seems that the distribution of Wg might be more confined to the apical plane of the cells compared to other conditions (Fig6F for example), but there is little difference in this regard between the anterior and posterior compartments.

3) A significant claim of the paper is "TRAPPC8 regulates retrograde Wg trafficking post-apical internalization". a. The increase in apical extracellular Wg (FigS3), which seems to remain associated with the membrane of Wg-producing cells (i.e. no onward spread) would suggest that apical internalization may be affected, but this is not considered by the authors. b. From the antibody chase experiment, it is not clear if the effect of TRAPPC8 loss affects endocytosis and/or trafficking in general or whether it is specific to Wg and Evi. A fluorescent Dextran control should be included as in Witte et al., 2020 (https://doi.org/10.1242/dev.186833 ). Also, can the authors be sure that they are visualising internalised Wg and not just internalised Wg antibody? Can the author show a field of view where Wg is not expressed?

4) The authors suggest that TRAPPC8 loss leads to increased Rab7 levels. This is taken as evidence for a role of acidification in driving Wg dissociation from Evi, with TRAPPC8 acting downstream to sort Wg from mature endosomes. a. Neither of these claims are supported because in Fig.S3G loss of TRAPPC8 results in an increase in Rab7 everywhere except at the DV boundary where the Wg-producing cells are. This should be acknowledged in text, and these data should appear in the main Fig4. b. The increase in lysotracker also does not support the above claims as it could be due to an increase in unbound Evi that cannot be trafficked back to the ER (and hence targeted for degradation in lysosomes). c. In fig S3G, the purported Rab7 increase in the posterior compartment is not readily apparent (and not quantified), in contrast to the authors' description of the effect of TRAPPC8 depletion. This suggest that the model proposed by the authors needs to be revised (Fig6G) and the relevant paragraphs from Results and Discussion section must be significantly edited or removed.

Minor concerns

1) The way data in Fig 2, S3 and S4 is presented and referred to in text could be rearranged slightly to make it easier to follow: first talk about the work using clones (Fig2, FigS4 becomes FigS3), then mention similar results with the knockdown (FigS3 becomes FigS4). This arrangement would link naturally to the effect on Evi.

2) How do the authors explain that the knockdown of some core TRAPP subunits does not have a phenotype? Some sort of rationalisation (or experimental follow up) is desirable.

3) The authors should give more detail about how they quantified normalised intensity profiles and clarify if the profiles correspond to just the representative image shown or the average of multiple discs (possible for the compartment experiments, but presumably impossible for the clone experiments as they would need to normalise by the size of the clone too).

Referee cross-commenting

Reviewer 3 was thorough and makes some good points that I had not considered because of coming from a different research field (e.g. the fact that losing TRAPPC8 can have off-target effects in TRAPPII, or that the figures may not be clear to non-fly people). In my review I identified the lack of testing of other TRAPP subunits as a minor point, but having read R3's comments I would probably increase this to a major issue. Reviewer 1 and I agree on multiple points as well (e.g. the lack of testing of other TRAPP subunits, the difference between the TRAPPC8 and Rab1 phenotypes). I believe that 1 - 3 months to complete revisions is optimistic. 6 months is a more realistic, with the caveat that the results from some of the requested experiments could upend the conclusions of this study.

Significance

This report is a valuable report for the Wg secretion subfield, and useful for the Wnt community. It makes some interesting observations and brings the importance of Rab1 back into the conversation after Ching et al., 2008. However, the insight remain limited and the mechanism/trafficking defects remain unclear. There is convincing evidence that TRAPPC8 and Rab1 affect Wg and Evi, but the claims that TRAPPC8 is essential and acts downstream of acidic endosomes) is inadequate.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this manuscript, the authors investigate the role of Transport Protein Particle (TRAPP) complexes in the secretion of Wingless (Wg) in Drosophila. Two TRAPP complexes are known to exist: TRAPPII and TRAPPIII. Through the systematic analysis of individual subunits, the authors identify the requirement of the TRAPPIII subunit TRAPPC8 for Wg trafficking. They demonstrate that the absence of TRAPPC8 disrupts the retrograde trafficking of both Wg and its carrier Evi, resulting in their intracellular accumulation within Wg-producing cells. Further analyses suggest that TRAPPC8 controls the post-apical internalisation and endosomal trafficking of Wg and Evi. Consistent with the established function of TRAPPIII as a Rab1-specific GEF, they demonstrate that inhibiting Rab1 produces similar effects as depleting TRAPPC8, while constitutively active Rab1 reverses the trafficking defects. Furthermore, depletion of either TRAPPC8 or Rab1 increases the levels of Wg-unbound Evi, suggesting that they act downstream of Evi-Wg dissociation. Taken together, these findings suggest that TRAPPIII and its effector Rab1 are essential regulators of retrograde Wg trafficking, which is necessary for efficient secretion. Overall, the work is carefully performed and the results are presented clearly. The controls are appropriate and the study expands the functional scope of Rab1-dependent trafficking beyond early secretory pathways. The identification of a previously unrecognised function of TRAPPC8 in Wg trafficking is a valuable contribution.

Major Points

It is not entirely clear whether the RNAi lines used in the initial screen were validated for knockdown efficiency. Notably, some core TRAPPIII subunits (e.g., TRAPPC3 and TRAPPC5) do not show a phenotype. This could indicate that the complex retains partial function upon their depletion, or alternatively that the RNAi lines are ineffective. While this point may not critically affect the main conclusion regarding TRAPPC8, it is important for drawing conclusions about the specificity of TRAPPIII versus TRAPPII involvement. For instance, TRAPPC10 (a TRAPPII-specific subunit) was analysed using a single RNAi line, yet no evidence of knockdown efficiency was provided. Validation of these RNAi reagents would strengthen the conclusions regarding complex specificity.

Minor Points

• In Figure 2C, the clone appears restricted to the apical region, and I do not clearly observe GFP loss in the basolateral domain. Larger clones or additional sections would help clarify the spatial distribution and strengthen the interpretation.
• The authors should discuss why TRAPPC8 depletion results primarily in apical Wg enrichment, whereas Rab1 inhibition leads to Wg accumulation at both apical and basolateral membranes. This difference may provide insight into whether Rab1 has additional TRAPPIII-independent functions or whether TRAPPC8 affects a more spatially restricted trafficking step.

Significance

This study broadens our understanding of Rab1-dependent membrane trafficking by identifying a previously unrecognized role for the TRAPPIII complex in retrograde transport during Wingless secretion. While the study convincingly establishes the involvement of the TRAPPIII-Rab1 module in Wg trafficking, it does not define the specific retrograde trafficking step that is regulated by this machinery. In addition, the functional relationship between TRAPPIII-Rab1 and established retrograde regulators, such as the retromer complex, is not addressed. Further molecular and mechanistic analyses will be required to position TRAPPIII within the broader retrograde trafficking network and to fully elucidate how Rab1 activity is coordinated with other pathways involved in Wnt secretion. These unresolved issues represent the main limitation of the current study. This work will be of particular interest to researchers in the fields of cell signaling, membrane trafficking, and intercellular communication.

My expertise lies in cell communication and the regulation of cellular proliferation.

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Reply to the reviewers

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

This work focuses on zebrafish notochord morphogenesis during axial elongation. In particular it dissects the role of YAP signalling on regulating the balance between caudal cell addition with the cell enlargement occurring rostrally through vacuolation.

The article is timely to the field and includes several important experiments. The overall presentation and written style are good, citations are adequate and there is a clear effort to integrate experiments and mathematical modelling from the outset. The logic behind experiments is sound and the conclusion coherent (even if not totally unexpected given the literature): YAP affects progenitor addition which in turn changes packing, vacuolation and axis length. I just have a few points that could make the article clearer and more persuasive.

We thank the reviewer for these positive comments about our manuscript. We would like to reiterate the two main unexpected findings based on our results:

• While YAP mutants display a defective notochord (Kimelman et al., 2017; eLife) it has not been clear what specific role that YAP signalling is playing during notochord development. Therefore, the finding that Yap signalling plays a role in controlling the rate to notochord progenitor addition and represents a novel discovery.
• The observation that the notochord can buffer its elongation rate against an increased influx of progenitors is novel and counter intuitive. Our current understanding of tissue elongation depends on the central idea that the addition of progenitors directly impacts elongation rate. Here we show for the first time that this has minimal impact at the tissue level using the notochord as an example. Major points

- Last section of results is difficult and confusing. After analysing vgll4b loss-of-function line, effectively over-activating YAP, the focus is on YAP inhibition using Verteporfin.

o Concerns on Verteporfin: the molecule has been widely used to module YAP, but there are also plenty of studies suggesting it is non-specific (also degrades YAP, has 14-4-3σ dependency and induces stress). I would consider an alternative: truncated TEAD, LATS over-expression or gain-of-function phosphomimetic versions of YAP.

o Presentation: regardless of point above, Verteporfin's role on YAP should be verified in the system. As such it is crucial to include: images of 4xGTIIC, noto and YAP stains after treatment. Only then inspect the effects on vacuolation and different treatments.

As suggested by the reviewer, we have added a supplementary figure validating the verteporfin treatment, including quantification of GFP reduction across the three tissues and quantification of notochord staining. We did not include Yap1 immunostaining data because the signal quality was insufficient for reliable analysis.

A simple over-expression experiment will not allow the spatial and temporal control required to test our hypothesis. Yap has a known function in gastrulation, so we need experiments that allow us to perturb Yap activity only at posterior body elongation stages. This has been achieved with the vgl4b experiments shown in the manuscript, as this gene is specifically expressed in the tailbud at these stages. In addition to the full verification of verteporfin's impact on YAP activity, we feel this is sufficient evidence to support our conclusions.

- In Fig 3F, noto HCR staining is taken as evidence for progenitor exhaustion/ faster depletion. Other scenarios would be possible without more direct demonstration. Evidence (either experimental or literature) that YAP is not involved in self-renewal or induction of these progenitors at these stages should be discussed.

We have concluded that the smaller volume of noto expressing cells is consistent with the faster depletion of the progenitor pool based on the direct observation of increased progenitor addition rate from photo-labelling experiments (Figure 3A,B). As suggested by the reviewer, we have now quantified cell divisions within the midline progenitor population and found no significant differences between mutant and control embryos. These data have now been included in Supplementary figure 3.

- Individual datapoints in Fig 3C and 4D should be shown.

These data have now been added to the figures

Additional justification is needed as to why spinal cord is the best to benchmark displacement. Additionally looking at this with respect to mesoderm migration could capture another set of progenitors and behaviour/ displacements.

Photolabels within the pre-somitic mesoderm are difficult to interpret as the high amount of cell rearrangement in this tissue leads to a spreading out of the labelled clone in a manner that then makes it difficult to assess tissue displacement (see Figure 2D,E; Thomson et al., (2021) Cells and Development). In contrast, aprevious paper has shown that notochord-spinal cord displacements can be mapped in a reliable manner across the anterior-posterior axis which motivated our choice here (McLaren and Steventon (2021) Development).

- Plotting vacuole area in Fig.4I vs A-P position (similar to plots 1H, 2F-H) could further strengthen the point of gradual (linear) vacuolation.

As suggested by the reviewer, we have plotted vacuole area as a function of position for the verteporfin treatment experiments, and these data have now been included in Figure 5.

Minor points:

- Scheme of Fig1A could benefit from having the info of zebrafish timeline (hpf)

The scheme has been modified indicating zebrafish timeline

- Figure 3B, what was time 0?

Timepoints have now been included in the text and figure legend

- The authors should address whether Verteporfin-treated mutants are rescued or whether the compound overwhelms the genetic effect.

Given that verteporfin will impact Yap signalling in a global manner, whereas the vgl4b have a localised over-activation of Yap signalling, we think this experiment would be difficult to interpret and would likely be non-informative.

- Cell density is an elegant measure but quite abstract. A plot of cells detected at each AP position would be quite valuable to reinforce more cells are being added to a relatively constant area.

As suggested by the reviewer, we have now plotted these data for mutant and controls and also for verteporfin treatments. These data have now been included in supplementary figures 3 and 7.

Reviewer #1 (Significance (Required)):

Significance included above.

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

Summary

Camacho-Macorra et al. investigate the mechanisms of axis extension in zebrafish embryos, focusing on the notochord and its two key elongation processes: progenitor addition (occurring early and posteriorly) and vacuolization (occurring later and in an anterior to posterior sequence). The authors first develop a mathematical model to predict notochord elongation dynamics by integrating these processes. They demonstrate that the YAP signaling pathway is active in both the notochord and its progenitors during axial extension. Their analysis reveals that vgll4b, an inhibitor of YAP, is expressed in the same regions. Knockdown of vgll4b results in YAP hyperactivation in the notochord and posterior progenitor regions, leading to increased progenitor recruitment into the notochord and a reduction in the progenitor pool. The effects of this mutation on extension are most pronounced during the late phase, which is dominated by vacuolization. The authors observe smaller vacuoles in mutants during this phase. However, early (but not late) YAP inhibition decreases notochord cell density and increases vacuole size, suggesting that YAP primarily regulates notochord progenitor uptake, which indirectly affect vacuolization.

Major Comments

The authors propose that YAP activity mediates a long-range feedback mechanism linking posterior progenitor addition to anterior vacuolization. Two lines of evidence are presented to support this idea. First, there appears to be compensation for tissue length during Phase 2, when both progenitor addition and vacuolization occur. Second, temporal YAP inhibition experiments show that early, but not late, YAP inactivation affects both cell addition and vacuolization. While these observations are intriguing, they do not conclusively demonstrate spatial long-range coordination. Instead, the global decrease of vacuole size could be a simple delayed consequence of cell density increase or cell disorganization at the posterior end without involving a long-range feedback along AP axis. Claiming that such long-range feedback is taking place would require a more precise characterization and/or the identification of its nature (chemical, mechanical).

We would like to thank this reviewer for this point, that we feel requires further clarification. As they suggest, the increased additional rate of posterior progenitors leads to a later impact on vacuolation, once these cells have reached more anterior parts of the body axis- creating an effective long-range feedback mechanism to link the two processes. However, this is not a direct propagation of a signal (mechanical or otherwise) across the length of the notochord, as may have been interpreted to be based on the previous framing of our conclusions. We have modified the title of our manuscript to place less emphasis on the 'long-range feedback', and included an additional discussion paragraph to make this point clearer.

Furthermore, there are several caveats with the interpretations of the claims cited above. The authors do not show quantification of vacuole area using notochord cell segmentation as described in Fig 1C in vgll4b mutants at stages when progenitor addition is increased.

This is an important point highlighted by the reviewer. We have now included analysis at 24 hpf, where we do see a significant reduction in vacuole area within the anterior part of the notochord during the buffering phase in vgl4b mutants- consistent with our model that reduced anterior vacuolation compensates for increased progenitor addition rate during this phase of notochord elongation (Figure 4E).

The slope of internuclear distances in Supplementary Figure 4A at 27 hours post-fertilization suggests that vacuolization is initially normal (similar to wt context in Fig 1H), arguing against an early defect in vacuolation dynamics along the Anterior to Posterior axis that could compensate for extra addition of progenitors.

We have revised Supplementary Figure 4 to present a direct comparison between mutant and control embryos at each time point analyzed. This analysis shows that within the mid-trunk region of the notochord, differences in cell size first emerge at the developmental stage when vacuolation becomes the primary driver of axis elongation. In addition, we observe a progressive decoupling of the scaling relationship in mutant embryos over time. As mentioned above- there is a significant difference in vacuole size within more anterior regions at 22.5 hpf that is consistent with the model that this is buffering against increase posterior addition.

Finally, the timing of the analysis of the effect of Verteporfin treatments is unclear. According to the legend of Figure 4F, analyses for Treatment A (16-27 hpf) and Treatment B (27-38 hpf) were done at 24 hpf and 30 hpf, respectively. If this is the case, the 3-hour window for Treatment B may not allow sufficient time to reveal effects on vacuolization.

We agree that the information regarding the verteporfin experiments was not clearly presented in the original figure, and we have therefore revised the schematic accordingly.

To strengthen the claim of long-range coupling, the authors could:

Provide direct measurements of vacuolization A-P dynamics/area during Phase 2, before the effect on notochord length in the mutant, to see if there is indeed a compensatory effect on notochord length for the additional accretion of notochord progenitors in the Vgll4b mutant.

As suggested by the reviewer, we have added an earlier time point to the A-P area dynamics plot in phase 2, corresponding to a stage at which the effect on notochord length in the mutant is not yet detectable. At this stage, we observed no difference in vacuole area between mutants and controls. We have also included an earlier time point analysis in the anterior region of the axis, which shows a similar cell size difference to that observed later in a more posterior region (Figure 4F; see above response).

Clarify the analysis timing of Treatment B to confirm that YAP inhibition during the vacuolization phase truly has no effect.

This has now been clarified.

Additionally, as a non-specialist, I found the distinction between the two modeling hypotheses difficult to follow. Specifically, it is unclear why the first hypothesis assumes YAP affects vacuolation rate, while the second assumes it affects vacuolation front speed. It is also not intuitive how front speed can be independent of vacuolation rate, as one would expect that if cells form vacuoles more slowly, the front should progress more slowly as well. Therefore, it could be good to clarify these aspects of the modeling part.

We thank the reviewer for this comment and apologise for the lack of clarity in our description of the model. In our framework, the cell size profile along the AP axis of the notochord is governed by two distinct processes: (i) the addition of progenitors at the posterior tip, and (ii) vacuolation, which increases cell size and proceeds from anterior to posterior. We model the latter as a propagating wave with velocity vf​, such that cells begin to vacuolate when the wave front reaches their position.

Importantly, in the model these two aspects of vacuolation are decoupled: the front velocity vf​ determines when a given cell starts vacuolating, whereas the vacuolation rate J determines how fast the cell increases in size once the process has started. Biologically, this corresponds to distinguishing between the propagation of a trigger or competence signal along the tissue, and the execution of vacuole growth within each cell. Our reasoning was that they need not be strictly proportional: a signalling wave could propagate at a given speed even if the downstream cellular response is slower or faster.

This is why we considered two alternative hypotheses: either YAP modulates the propagation of the vacuolation front (affecting vf​), or it modulates the growth dynamics within each cell (affecting J). Our quantitative comparison with the experimental data supports the former scenario. This has now been clarified in the main text.

Minor Comments

While the study is technically sound, a few areas could benefit from improved clarity or additional data.

An intriguing but puzzling finding is the reduction in the noto-expressing progenitor domain in vgll4b mutants, despite elevated YAP activity in progenitors. Intuitively, if YAP promotes progenitor maintenance or expansion, one might expect the noto+ domain to increase, not shrink. This paradox suggests that YAP may not only simply maintain progenitors but instead accelerates their differentiation or migration into the notochord (as stated in the manuscript and graphical abstract). Alternatively, YAP could only deplete the noto+ pool by driving premature entry into the notochord, though the lack of clear YAP upregulation in this domain would imply a non-cell autonomous role of YAP for this interpretation. The authors should discuss these possibilities more explicitly in the Discussion section and could consider including additional markers, such as proliferation assays or apoptosis markers, to clarify whether YAP affects progenitor proliferation, differentiation, or migration.

As also suggested by the reviewer, we have included a cell proliferation analysis in Supplementary Figure 3 and have revised the Discussion section accordingly.

In Figure 2B, the YAP activity reporter signal in the posterior floor plate is not immediately obvious. The authors should consider providing higher-magnification insets.

As suggested by the reviewer, we have included higher-magnification insets in Figure 2

In Figure 2C, the differences in tail shape between wild-type and mutant embryos are visually striking. If these differences have not been quantified or discussed, a brief comment in the text would be helpful.

We did not see a consistent impact on the morphology of the posterior body, this has now been clarified in the main text.

Supplementary Figure 6 describes embryo length differences in mutants but does not include a representative image. Adding one would strengthen the phenotypic description.

As suggested by the reviewer, we have modified Supplementary Figure 6

Figure 1C is not cited in the text as not associated with a result, but just a description of the approach that is used later in Fig 4I

We have modified the text to include the appropriate figure reference.

Finally, the authors might consider citing Michaud & Pourquié (2025) when presenting the role of hydrostatic pressure in axis elongation in the Introduction.

We have now modified the text to include this citation which we agree is relevant to this work.

Reviewer #2 (Significance (Required)):

This study by Camacho-Macorra et al. presents a fascinating exploration of how YAP signaling and its inhibition by vgll4b coordinate progenitor addition and vacuolization during zebrafish notochord elongation. The work is well executed, with clear results and integration of mathematical modeling and experimental data. The findings shed new light on the molecular and mechanical regulation of axis extension, a fundamental process in vertebrate development. However, while the study is innovative and rigorously conducted, the central claim of "long-range coupling" between progenitor addition and vacuolization requires further substantiation. Addressing the points discussed below will make the study more convincing and accessible to developmental biologists and mechanobiologists alike.

reviewer expertise: developmental biologist specialised in morphogenesis

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

In the studies conducted by Camacho-Macorra et al., the authors examine the extension of the body axis is zebrafish, focusing on the notochord. They specifically compare timepoints where progenitor addition to the notochord and vacuolization are important to drive axis extension. They generate a simple mathematical model of notochord extension and show that it recapitulates observations in vivo where progenitor addition and vacuolation drive tissue elongation. They further perturb the system by showing that YAP activity is localized to the midline progenitors of the notochord where when the competitive inhibitor of YAP vgll4b is perturbed it increases YAP signaling and results in increase progenitor addition to the notochord. They further describe a possible indirect-feedback mechanism linking YAP driven progenitor addition to the notochord with anterior vacuolation which when perturbed (i.e. increased YAP) results in reduced notochord elongation.

Major Comments:

NA

Minor comments:

1.Figure 1B - please put the model equation in the figure or at least point out what variables of the equation refer to each part of the schematic.

As suggested by the reviewer, we have modified the scheme in Figure 1

2.Figure 1F - smooth line is misleading, please include individual embryo measurement points. This comment could be applied to several figures

We agree with the reviewer that the graphs in the original manuscript could be improved, and we have therefore modified all figures to better represent data dispersion within each group.

3.Figure 2C/D - To make this manuscript more accessible to individuals who are not familiar with the anatomy of zebrafish tail, please include zoom in panels of the region of interest where arrows are pointing out increased YAP signaling in the floor plate and hypochord.

As suggested by the reviewer, we have included higher-magnification insets in Figure 2

4.In discussion - "In vgll4b mutants, increased progenitor incorporation initially does not alter overall notochord length due to a buffering mechanism for natural variation in progenitor addition" - this is not directly tested in terms of buffering for variation and is an assumption. Please either cite a paper or reword

This point has been clarified in the revised discussion.

Reviewer #3 (Significance (Required)):

Overall, the logic and experiments conducted in these studies are well defined. However, the significance of the work is minimal and makes only a small contribution to the advancement of the field of developmental biology. Regardless, the studies are well done and worth publication.

Strengths:

-The study does a good job of incorporating and testing a computational model in a way that proves/disproves their hypothesis

-The manuscript is well written and follows a logical order, making it easy for readers to understand the main findings

-The study uses multiple routes of YAP inhibition (genetic and drug) to show effect on progenitor addition to the notochord and shortened body axis

-The discussion does aa very good job of giving the context of the study's results.

Weaknesses:

-The study is minimal and fails to illuminate the mechanism that connects progenitor addition to vacuolization, claiming only an indirect relationship with YAP signaling. However, this is admitted by the authors and not overstated

The study provides a minimal advancement to the field by investigating an unexplored area of zebrafish notochord extension. It provides a small step toward connecting mechanical/morphogenic mechanisms with signalling in zebrafish body axis extension.

The audience of this work is a specialized basic research group of developmental biology scientists. The research is of particular relevance to individuals studying zebrafish or axis elongation. While the authors make comparisons to other systems, due to the unique nature of the zebrafish body extension, this generates a narrow field of focus for the manuscript.

We have previously discussed the uniqueness of zebrafish posterior body elongation in light of critical differences in the degree to which posterior growth from self-renewing tailbud progenitor populations contribute to the mechanisms of axis elongation (Sambasivan and Steventon (2021) Frontiers in cell and dev. Biol; Steventon and Martinez Arias (2017) Developmental Biology). Here too, we think zebrafish provide an important system to explore differences in the mechanisms that drive notochord elongation, and we envisage that this study will provoke a similar cross species comparison that takes into account differences in the relative timing of progenitor addition and anterior notochord expansion (that occurs much later in amniotes, for example). It is only by considering these species-specific differences across experimental organisms that we can arrive at the fundamental principles that drive developmental processes, and how evolution has acted upon these to drive change in adult body plans. We therefore respectfully disagree with the review about the scope and importance of this work for these reasons.

In addition, we feel that the principles by which dynamic processes are coupled across an organ are broadly applicable and will illuminate further research into understanding organ growth control.

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Referee #3

Evidence, reproducibility and clarity

In the studies conducted by Camacho-Macorra et al., the authors examine the extension of the body axis is zebrafish, focusing on the notochord. They specifically compare timepoints where progenitor addition to the notochord and vacuolization are important to drive axis extension. They generate a simple mathematical model of notochord extension and show that it recapitulates observations in vivo where progenitor addition and vacuolation drive tissue elongation. They further perturb the system by showing that YAP activity is localized to the midline progenitors of the notochord where when the competitive inhibitor of YAP vgll4b is perturbed it increases YAP signaling and results in increase progenitor addition to the notochord. They further describe a possible indirect-feedback mechanism linking YAP driven progenitor addition to the notochord with anterior vacuolation which when perturbed (i.e. increased YAP) results in reduced notochord elongation.

Major Comments: NA

Minor comments: 1.Figure 1B - please put the model equation in the figure or at least point out what variables of the equation refer to each part of the schematic.

2.Figure 1F - smooth line is misleading, please include individual embryo measurement points. This comment could be applied to several figures

3.Figure 2C/D - To make this manuscript more accessible to individuals who are not familiar with the anatomy of zebrafish tail, please include zoom in panels of the region of interest where arrows are pointing out increased YAP signaling in the floor plate and hypochord.

4.In discussion - "In vgll4b mutants, increased progenitor incorporation initially does not alter overall notochord length due to a buffering mechanism for natural variation in progenitor addition" - this is not directly tested in terms of buffering for variation and is an assumption. Please either cite a paper or reword

Significance

Overall, the logic and experiments conducted in these studies are well defined. However, the significance of the work is minimal and makes only a small contribution to the advancement of the field of developmental biology. Regardless, the studies are well done and worth publication.

Strengths:

• The study does a good job of incorporating and testing a computational model in a way that proves/disproves their hypothesis
• The manuscript is well written and follows a logical order, making it easy for readers to understand the main findings
• The study uses multiple routes of YAP inhibition (genetic and drug) to show effect on progenitor addition to the notochord and shortened body axis
• The discussion does aa very good job of giving the context of the study's results.

Weaknesses:

• The study is minimal and fails to illuminate the mechanism that connects progenitor addition to vacuolization, claiming only an indirect relationship with YAP signaling. However, this is admitted by the authors and not overstated

The study provides a minimal advancement to the field by investigating an unexplored area of zebrafish notochord extension. It provides a small step toward connecting mechanical/morphogenic mechanisms with signalling in zebrafish body axis extension.

The audience of this work is a specialized basic research group of developmental biology scientists. The research is of particular relevance to individuals studying zebrafish or axis elongation. While the authors make comparisons to other systems, due to the unique nature of the zebrafish body extension, this generates a narrow field of focus for the manuscript.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary

Camacho-Macorra et al. investigate the mechanisms of axis extension in zebrafish embryos, focusing on the notochord and its two key elongation processes: progenitor addition (occurring early and posteriorly) and vacuolization (occurring later and in an anterior to posterior sequence). The authors first develop a mathematical model to predict notochord elongation dynamics by integrating these processes. They demonstrate that the YAP signaling pathway is active in both the notochord and its progenitors during axial extension. Their analysis reveals that vgll4b, an inhibitor of YAP, is expressed in the same regions. Knockdown of vgll4b results in YAP hyperactivation in the notochord and posterior progenitor regions, leading to increased progenitor recruitment into the notochord and a reduction in the progenitor pool. The effects of this mutation on extension are most pronounced during the late phase, which is dominated by vacuolization. The authors observe smaller vacuoles in mutants during this phase. However, early (but not late) YAP inhibition decreases notochord cell density and increases vacuole size, suggesting that YAP primarily regulates notochord progenitor uptake, which indirectly affect vacuolization.

Major Comments

The authors propose that YAP activity mediates a long-range feedback mechanism linking posterior progenitor addition to anterior vacuolization. Two lines of evidence are presented to support this idea. First, there appears to be compensation for tissue length during Phase 2, when both progenitor addition and vacuolization occur. Second, temporal YAP inhibition experiments show that early, but not late, YAP inactivation affects both cell addition and vacuolization. While these observations are intriguing, they do not conclusively demonstrate spatial long-range coordination. Instead, the global decrease of vacuole size could be a simple delayed consequence of cell density increase or cell disorganization at the posterior end without involving a long-range feedback along AP axis. Claiming that such long-range feedback is taking place would require a more precise characterization and/or the identification of its nature (chemical, mechanical). Furthermore, there are several caveats with the interpretations of the claims cited above. The authors do not show quantification of vacuole area using notochord cell segmentation as described in Fig 1C in vgll4b mutants at stages when progenitor addition is increased. The slope of internuclear distances in Supplementary Figure 4A at 27 hours post-fertilization suggests that vacuolization is initially normal (similar to wt context in Fig 1H), arguing against an early defect in vacuolation dynamics along the Anterior to Posterior axis that could compensate for extra addition of progenitors. Finally, the timing of the analysis of the effect of Verteporfin treatments is unclear. According to the legend of Figure 4F, analyses for Treatment A (16-27 hpf) and Treatment B (27-38 hpf) were done at 24 hpf and 30 hpf, respectively. If this is the case, the 3-hour window for Treatment B may not allow sufficient time to reveal effects on vacuolization. To strengthen the claim of long-range coupling, the authors could: Provide direct measurements of vacuolization A-P dynamics/area during Phase 2, before the effect on notochord length in the mutant, to see if there is indeed a compensatory effect on notochord length for the additional accretion of notochord progenitors in the Vgll4b mutant. Clarify the analysis timing of Treatment B to confirm that YAP inhibition during the vacuolization phase truly has no effect. Additionally, as a non-specialist, I found the distinction between the two modeling hypotheses difficult to follow. Specifically, it is unclear why the first hypothesis assumes YAP affects vacuolation rate, while the second assumes it affects vacuolation front speed. It is also not intuitive how front speed can be independent of vacuolation rate, as one would expect that if cells form vacuoles more slowly, the front should progress more slowly as well. Therefore, it could be good to clarify these aspects of the modeling part.

Minor Comments

While the study is technically sound, a few areas could benefit from improved clarity or additional data. An intriguing but puzzling finding is the reduction in the noto-expressing progenitor domain in vgll4b mutants, despite elevated YAP activity in progenitors. Intuitively, if YAP promotes progenitor maintenance or expansion, one might expect the noto+ domain to increase, not shrink. This paradox suggests that YAP may not only simply maintain progenitors but instead accelerates their differentiation or migration into the notochord (as stated in the manuscript and graphical abstract). Alternatively, YAP could only deplete the noto+ pool by driving premature entry into the notochord, though the lack of clear YAP upregulation in this domain would imply a non-cell autonomous role of YAP for this interpretation. The authors should discuss these possibilities more explicitly in the Discussion section and could consider including additional markers, such as proliferation assays or apoptosis markers, to clarify whether YAP affects progenitor proliferation, differentiation, or migration. In Figure 2B, the YAP activity reporter signal in the posterior floor plate is not immediately obvious. The authors should consider providing higher-magnification insets. In Figure 2C, the differences in tail shape between wild-type and mutant embryos are visually striking. If these differences have not been quantified or discussed, a brief comment in the text would be helpful. Supplementary Figure 6 describes embryo length differences in mutants but does not include a representative image. Adding one would strengthen the phenotypic description. Figure 1C is not cited in the text as not associated with a result, but just a description of the approach that is used later in Fig 4I Finally, the authors might consider citing Michaud & Pourquié (2025) when presenting the role of hydrostatic pressure in axis elongation in the Introduction.

Significance

This study by Camacho-Macorra et al. presents a fascinating exploration of how YAP signaling and its inhibition by vgll4b coordinate progenitor addition and vacuolization during zebrafish notochord elongation. The work is well executed, with clear results and integration of mathematical modeling and experimental data. The findings shed new light on the molecular and mechanical regulation of axis extension, a fundamental process in vertebrate development. However, while the study is innovative and rigorously conducted, the central claim of "long-range coupling" between progenitor addition and vacuolization requires further substantiation. Addressing the points discussed below will make the study more convincing and accessible to developmental biologists and mechanobiologists alike.

reviewer expertise: developmental biologist specialised in morphogenesis

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Referee #1

Evidence, reproducibility and clarity

This work focuses on zebrafish notochord morphogenesis during axial elongation. In particular it dissects the role of YAP signalling on regulating the balance between caudal cell addition with the cell enlargement occurring rostrally through vacuolation.

The article is timely to the field and includes several important experiments. The overall presentation and written style are good, citations are adequate and there is a clear effort to integrate experiments and mathematical modelling from the outset. The logic behind experiments is sound and the conclusion coherent (even if not totally unexpected given the literature): YAP affects progenitor addition which in turn changes packing, vacuolation and axis length. I just have a few points that could make the article clearer and more persuasive.

Major points

• Last section of results is difficult and confusing. After analysing vgll4b loss-of-function line, effectively over-activating YAP, the focus is on YAP inhibition using Verteporfin.
  • Concerns on Verteporfin: the molecule has been widely used to module YAP, but there are also plenty of studies suggesting it is non-specific (also degrades YAP, has 14-4-3σ dependency and induces stress). I would consider an alternative: truncated TEAD, LATS over-expression or gain-of-function phosphomimetic versions of YAP.
  • Presentation: regardless of point above, Verteporfin's role on YAP should be verified in the system. As such it is crucial to include: images of 4xGTIIC, noto and YAP stains after treatment. Only then inspect the effects on vacuolation and different treatments.
• In Fig 3F, noto HCR staining is taken as evidence for progenitor exhaustion/ faster depletion. Other scenarios would be possible without more direct demonstration. Evidence (either experimental or literature) that YAP is not involved in self-renewal or induction of these progenitors at these stages should be discussed.
• Individual datapoints in Fig 3C and 4D should be shown. Additional justification is needed as to why spinal cord is the best to benchmark displacement. Additionally looking at this with respect to mesoderm migration could capture another set of progenitors and behaviour/ displacements.
• Plotting vacuole area in Fig.4I vs A-P position (similar to plots 1H, 2F-H) could further strengthen the point of gradual (linear) vacuolation.

Minor points:

• Scheme of Fig1A could benefit from having the info of zebrafish timeline (hpf)
• Figure 3B, what was time 0?
• The authors should address whether Verteporfin-treated mutants are rescued or whether the compound overwhelms the genetic effect.
• Cell density is an elegant measure but quite abstract. A plot of cells detected at each AP position would be quite valuable to reinforce more cells are being added to a relatively constant area.

Significance

Significance included above.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity:

In this paper, Tomasek and colleagues describe a series of experiments illuminating the effects of OM-89, a bacterial lysate taken orally for prevention of recurrent UTI, on intracellular dynamics of UPEC, using cell culture and organoid models. Suggestions for improvement and for clarification of the authors' conclusions and relevance to human UTI (and OM-89 use) are offered below.

Major points:

1. The data indicate that OM-89 exposure in the organoids enhances lysosomal degradation pathways and (in mBOs) autophagic flux, and the authors conclude this is a mechanism by which UPEC regrowth after antibiotic treatment (modeling rUTI) is inhibited by OM-89. They also show enhanced cellular uptake of fluorescently labeled antibiotics (ampicillin) in organoids - this leads them to conclude (and state in the paper's title) that increased intracellular antibiotic concentration effects increased killing of UPEC and decreased regrowth. These are two separate proposed mechanisms, and especially with regard to the antibiotics, they have not shown that increased intracellular antibiotic concentration actually kills intracellular UPEC in their model - only that regrowth as measured microscopically is less. In total, a mechanistic connection between the observed lysosomal effect and the intracellular antibiotic uptake, and which one is more important for UPEC control in this model, is incomplete. The precise wording of the paper's title should be reconsidered accordingly.

We agree with the reviewer that our study does not establish a direct mechanistic connection between OM-89-induced lysosomal remodeling and enhanced intracellular antibiotic accumulation, nor does it definitively determine the relative contribution of each process to intracellular UPEC control. Further studies dissecting the molecular pathways underlying these phenotypes will be required to determine whether they are mechanistically linked or represent parallel epithelial defense responses induced by OM-89.

Importantly, additional CFU experiments performed during revision (as suggested in point number 4) revealed that OM-89 already reduces intracellular bacterial burden following a classical gentamicin protection assay, prior to prolonged ampicillin exposure. These findings suggest that enhanced intracellular bacterial control cannot be explained solely by increased intracellular antibiotic accumulation and support a direct contribution of epithelial antimicrobial mechanisms, including lysosomal activation, to the observed phenotype. Nevertheless, the relative contribution of lysosomal remodeling and enhanced antibiotic uptake to bacterial clearance remains unresolved and will require further investigation.

Accordingly, we changed the title to "Targeted lysosomal activation in bladder epithelium enhances clearance of intracellular uropathogenic Escherichia coli." This revised title avoids implying a direct causal link between increased intracellular antibiotic accumulation and bacterial clearance while reflecting the central biological process identified in our study.

OM-89 is taken orally for rUTI prevention, and some "components" reach the urinary tract (line 81). But it isn't explained how applying OM-89 directly to organoids models how its components may reach the bladder epithelium (from the basolateral side, if the OM-89 is applied outside the organoids) in the whole animal or human. At the least, this limitation should be stated in the Discussion.

We thank the reviewer for pointing out this limitation. Although advanced in vitro models help to better mimic the in vivo situation, they still do not fully recapitulate all aspects of drug exposure and delivery observed in vivo. We included the following statement of limitation now in the discussion in lines 493-503: “One limitation of our study is that OM-89 was applied directly to epithelial cultures and organoids, whereas in clinical use it is administered orally. Although pharmacokinetic studies have demonstrated systemic distribution and urinary accumulation of OM-89-derived components following oral administration (van Dijk, 1982), our experimental setup does not recapitulate the exact route, kinetics or concentration profiles encountered in vivo. Rather, our models were designed to determine whether bladder epithelial cells are capable of responding directly to OM-89-mediated signals and to identify the intracellular pathways involved. Given the documented systemic exposure following oral administration, direct effects on the urothelium are biologically plausible. However, future studies will be required to determine how the epithelial responses identified here integrate with the complex systemic and immune-mediated effects of OM-89 under physiological administration conditions.”

In the lysosome studies starting on line 319, the cultured cells are all infected (and either treated with OM-89 or not). What observations regarding number and size of vesicles, etc (all the measures in Fig 6) are evident when cells are treated with OM-89 only? These data should be presented (at least as a supplemental figure) to enable optimal interpretation of the OM-89+UPEC data in Fig 6. As the authors themselves indicate, OM-89 may be having a generalized effect on endocytic and/or autophagic flux by bladder epithelial cells, independent of infection.

We thank the reviewer for this helpful suggestion and agree that assessing OM-89 treatment in the absence of infection provides important context for interpreting the infection-associated phenotypes as shown in Figure 6.

Accordingly, we have included additional supplementary data examining the effects of OM-89 alone in both murine and human bladder epithelial cells. Specifically, we added analyses of Lamp1-positive lysosomal vesicles, lysosomal acidification (LysoSensor), and Cathepsin L activity under uninfected conditions (Supplementary Figures 4A, 4G and 7D-F). We comment on these additional findings in the Result section in lines 242-246 and lines 366-370, and in the Discussion section in lines 469-483.

These experiments, together with the transcriptional data in SI Figure 3D, demonstrate that key features of lysosome-centered remodeling and activation are already induced by OM-89 in the absence of infection, indicating that OM-89 directly modulates epithelial lysosomal pathways rather than merely amplifying infection-driven responses. Inclusion of these data provides additional context for interpreting the infection-associated phenotypes shown in the main figures and further supports the concept of OM-89 as a direct modulator of epithelial antimicrobial function.

With the organoids, beyond the microscopic quantification of UPEC, can CFUs be measured?

We appreciate the reviewer’s interest in obtaining orthogonal measurements of bacterial burden. Performing CFU quantification directly from microinjected organoids is technically challenging, as it requires highly reproducible injections into identical numbers of organoids while avoiding bacterial leakage into the surrounding extracellular matrix. Even minor variations or accidental release of bacteria into the Matrigel can substantially affect CFU recovery and compromise interpretation.

To address the reviewer’s underlying question while avoiding these limitations, we performed intracellular CFU assays using differentiated mouse bladder epithelial monolayers. Following a classical gentamicin protection assay for 1 hour, OM-89-treated cells displayed significantly reduced intracellular bacterial burden compared with PBS controls (new Figure 2C). Addition of ampicillin for 3 hours after the gentamicin protection phase resulted in a similar trend but did not further significantly reduce the bacterial burden (new Figure 2D). We commented on these findings in the Results section in lines 169-182, and in the Discussion section in lines 463-469 and lines 474-483. We also updated the Methods section in lines 637-652 with the intracellular bacterial burden assay description.

These experiments provide an orthogonal readout of intracellular bacterial burden and are consistent with enhanced epithelial control of intracellular UPEC. In addition, we would like to clarify that the higher-throughput microscopy approach used throughout the organoid experiments does not allow strict discrimination between luminal, intracellular and tissue-associated bacteria. We therefore revised the terminology throughout the manuscript and now consistently refer to the measured signal as “intra-organoid bacterial burden”. To clarify this point, we added the following statement to the Results section (line 115): “Hence, the microscopy data represent the total “intra-organoid” bacterial burden at each experimental stage, without distinguishing the exact localization of the bacteria – which can be luminal, intracellular or tissue-associated.”. Consistent with this clarification, we have replaced the term “antibiotic-mediated killing” throughout the manuscript with the more cautious wording “antibiotic-mediated clearance” or “reduced bacterial burden”, where appropriate.

Minor points:

1. In Fig 1A, the "co-application" horizontal line is under the 7-10 hour window, but the text suggests that the application of antibiotics and OM-89 in this experiment is between 4-7 hours.

We thank the reviewer for pointing this out. Indeed, in the co-application regime, OM-89 is added at the same timepoint as the antibiotic – meaning straight after monitoring the growth phase at 4h post-infection (pi). We now adapted the horizontal line for the “co-application” treatment in Figure 1A accordingly to represent the time-point of OM-89 addition better. Additionally, we added a line for the antibiotic-treatment in order to further facilitate readability.

How are antibiotics and OM-89 "removed" at the 7-hour mark? This was not detailed in the Methods.

Although we had specified this in the methods section (now line 682: “For every media exchange (e.g. antibiotic treatment or withdrawal), each well was washed with 9 ml of the respective media before leaving 1 ml in the well.”), we realized the positioning was not optimal as we had mentioned this part under the point “Bacterial injection” in “Injection experiments”. We therefore now separated this part, together with the lid preparation, from the “Bacterial injection” part and created the new subsection “Lid preparation for media changes” (line 668 onwards).

What time point was used for the transcriptomic profiling of organoids? This is not clear from the relevant Methods or Results sections.

As stated in the methods section, RNA for transcriptomic profiling from mBOs was extracted at 4h post-infection (pi) (now line 892).

In showing that OM-89 "attenuated" the magnitude of inflammatory responses (Fig 2C and S3B), it would be helpful to add a panel showing the comparison of OM89+UPEC to PBS alone - this would be expected to convey activity (red) in the infection-related pathways, but to a lower magnitude than seen in UPEC vs PBS.

Please see our combined response at point 5.

Similarly, in the results outlined starting on line 196, it would be helpful to add a panel showing OM89+UPEC vs OM89 alone.

We thank the reviewer for these suggestions. We performed the requested additional analyses and generated Gene Ontology Biological Process (GOBP) enrichment plots comparing (i) PBS+UPEC versus PBS, (ii) OM-89+UPEC versus PBS and (iii) OM-89+UPEC versus OM-89.

As anticipated by the reviewer, these analyses show that infection-associated pathways remain induced in OM-89-treated infected organoids but with a reduced magnitude compared with infected PBS controls. Specifically, pathways that are strongly enriched in the PBS+UPEC versus PBS comparison display lower enrichment significance and effect size in the OM-89+UPEC versus PBS comparison. Furthermore, many of these pathways are no longer significantly enriched in the direct OM-89+UPEC versus OM-89 comparison, indicating that OM-89 attenuates the transcriptional inflammatory response induced by UPEC infection. These observations are consistent with our original interpretation, concluded from Figure 3C, that OM-89 dampens excessive infection-associated inflammatory signaling while preserving epithelial antimicrobial activity.

Importantly, we found that the direct comparison between PBS+UPEC and OM-89+UPEC, presented in the original Figure 3C, remains the most informative representation of the OM-89 effect because it controls for infection status while specifically highlighting the transcriptional changes induced by OM-89. By contrast, comparisons against PBS or OM-89 alone involve simultaneous changes in both infection and treatment status, making biological interpretation less straightforward.

Nevertheless, because the additional analyses directly address the reviewer's request and provide complementary context for interpreting Figure 3C, we have included them in Supplementary Figure 3B.

In line 236, what is meant by lysosomal "activation"? A more specific term should be chosen here.

We thank the reviewer for this question and aim to increase readability of this section. With lysosomal activation in the first sentence of the mentioned paragraph, we referred to the observed effect of upregulated lysosomal pathways and enhanced lysosomal function (measured by alterations in lysosomal vesicles) in the previous paragraph. However, to make the connection to the previous paragraph better, and given the comment number two of reviewer number two, we changed the whole first paragraph of this section. Therefore, the first sentence of this paragraph (line 252 onwards) reads now: “To test whether the observed effects on lysosomal pathways could mechanistically, at least in parts, explain OM-89-mediated protection, we first used Genebridge analysis (Li et al, 2019) to examine how the lysosomal gene signature identified in our RNA-seq data relates to host defense programs in the human bladder.”

In the Abstract (line 25), the phrase "Using bladder organoids..." is a dangling modifier.

We thank the reviewer for pointing this out and changed the sentence accordingly to “OM-89 promotes lysosomal acidification and increases lysosomal protease activity in bladder organoids and differentiated epithelial monolayers, thereby directing intracellular UPEC toward degradative compartments.” (now line 24)

Typographical and copyediting:

We thank the reviewer for identifying typographical errors and have corrected them throughout the manuscript.

1. Line 74 should read "For instance..."

2. Line 76 should read "when combined with antibiotic therapy..."

As this sentence is to emphasize the already observed protective effects of OM-89, and the two studies mentioned were either performed without or in combination with antibiotics, we changed the sentence to “For instance, rodent infection studies have demonstrated protective effects of OM-89 alone (Bosch et al, 1988; Lee et al, 2006) and in combination with antibiotic therapy (Canton et al, 2025; Bessler et al, 2010), although this observed in vivo protection could not be linked to any major quantitative changes in bladder immune cell infiltration (Canton et al, 2025), leaving the underlying molecular mechanism not fully resolved.” for better readability. (now line 71)

Line 122 should read "...regrowth following antibiotic treatment" or "regrowth post-antibiotic treatment"

Line 138 should use "regimen" not "regime"

Line 196 delete comma after "Although"

Line 244 fully hyphenate "OM-89-mediated"

Line 374 should read "...significantly enhance antibiotic-mediated killing"

Significance:

The paper is very well written and though a lot of data are included, the presentation is excellent and helps the reader to follow the story. The paper makes a strong contribution to the UTI pathogenesis field, and the use of mouse and human bladder organoids is innovative in studying intracellular UPEC. My scientific expertise as a reviewer is in UPEC pathogenesis, directly relevant to the content of this paper.

Reviewer #2

Evidence, reproducibility and clarity:

This study examined the effect of OM-89 on UPEC infection, antibiotic clearance, and resurgence in mouse and human organoid models. The goal of the study was to understand the molecular mechanisms by which OM-89 is effective at preventing rUTI in patients.

Major comments:

The manuscript is well-written and the figures are well presented. Adequate background information is provided to give the study context and sufficient experimental details are provided to allow replication by other groups. Experiments contain appropriate controls and sufficient replicates to allow appropriate statistical analyses. The authors are careful to acknowledge the differences they observed between the mouse and human system and provide satisfactory potential explanations for these differences. The conclusions they draw are well supported by their data and none of their claims from their data are overstatements. Below are some, which I believe if addressed could improve the paper.

1. I think the authors overstate the novelty of the concept that the urothelium is an active targetable determinant of infection and treatment outcomes. This is not an entirely new concept since previous studies have examined antimicrobial peptides and other factors from the urothelium.

We thank the reviewer for this important point and agree that the urothelium has long been recognized as an active participant in host defense through mechanisms such as antimicrobial peptide production, pathogen sensing and regulation of inflammatory responses. We have therefore revised the manuscript to avoid implying that urothelial involvement in infection outcome is itself a novel concept. Instead, we now emphasize the specific advance of our study: the identification of lysosome-centered epithelial activation as a therapeutically targetable mechanism that enhances intracellular bacterial clearance and potentiates antibiotic efficacy.

In the abstract we changed: “Our findings position the bladder epithelium from a passive barrier to an active, targetable determinant of treatment outcome and suggest host-directed modulation of epithelial antimicrobial pathways as a promising strategy to enhance intracellular bacterial clearance.” to “Our findings demonstrate that bladder epithelial antimicrobial pathways can be pharmacologically reinforced to influence treatment outcomes by enhancing intracellular bacterial clearance.” in line 29.

In the introduction we changed: “Together with increased intracellular accumulation of antibiotics across different classes, this leads to improved intracellular killing and reduced bacterial regrowth across diverse UPEC strains.” to “Together with increased intracellular accumulation of antibiotics across different classes, these changes are associated with improved intracellular clearance and reduced bacterial regrowth across diverse UPEC strains.” in line 90 and “Together, these findings reveal a previously unrecognized epithelial lysosome-centered mechanism by which OM-89 enhances intracellular antibiotic performance and repositions the bladder epithelium from a passive reservoir of infection reactivation to an actively transformable antimicrobial compartment influencing treatment outcomes.” to “Together, these findings reveal a previously unrecognized lysosome-centered epithelial mechanism by which OM-89 strengthens bladder epithelial antimicrobial defenses and enhances intracellular bacterial clearance, identifying enhanced lysosomal function as a therapeutically targetable component of host defense.” in line 95.

In the discussion we changed: “Together, these findings provide a mechanistic framework for the long-observed clinical efficacy of OM-89. Our findings reveal that the urothelium itself can be therapeutically targeted to reduce pathogen regrowth by transforming the epithelial barrier from a passive refuge for UPEC into an active defense site.” to “Together, these findings provide a mechanistic framework for the long-observed clinical efficacy of OM-89 and identify epithelial lysosomal pathways as a therapeutically targetable component of host defense that can be used to improve intracellular bacterial clearance.” in line 421 and “In the face of rising antimicrobial resistance (2024), strengthening epithelial antimicrobial function offers a complementary route to shift the bladder mucosa from a passive niche of bacterial survival and infection reactivation toward an active site of accelerated pathogen clearance.” to “In the face of rising antimicrobial resistance (2024), our findings provide a mechanistic rationale for the clinical use of OM-89 and support epithelial lysosomal pathways as a promising target for host-directed therapeutic strategies that enhance intracellular bacterial clearance and improve the efficacy of existing antibiotics.” in line 513.

Depending on the target audience, the Module-Module association analysis could need more introduction. I am not a computational biologist and it was not obviously apparent how Figure 4A is generated and what it actually showing. How specifically does this analysis demonstrate a functional link between lysosomal activity and immune defense pathways? Without further explanation, it is my opinion that this figure panel is an unnecessary distraction that is not required for any of the conclusions that the group can already draw from the rest of their data.

We thank the reviewer for this constructive critique. We agree that the rationale and interpretation of this analysis were not sufficiently explained in the original manuscript. We have therefore expanded the description of the MMAS approach and clarified how these data support the translational relevance of the lysosomal pathways identified in our experimental models.

Specifically, we now explain that the Module-Module Association Score (MMAS) analysis evaluates transcriptional correlations between the lysosomal gene network and functional biological pathways across eight independent human bladder transcriptomic datasets comprising more than 1,400 clinical samples. We further highlight the strong positive associations observed with host defense modules, including “response to molecule of bacterial origin”, “cell activation involved in immune response”, and “innate immune response”. These additions clarify both the methodology and the rationale for including Figure 5A as a translational bridge between our experimental findings and human bladder biology.

The revised text (starting at line 251) now reads: “To test whether the observed effects on lysosomal pathways could mechanistically, at least in parts, explain OM-89-mediated protection, we first used Genebridge analysis (Li et al, 2019) to examine how the lysosomal gene signature identified in our RNA-seq data relates to host defense programs in the human bladder. To evaluate the translational relevance of our experimental findings, we used a computational Module-Module Association Score (MMAS) analysis across eight independent human bladder transcriptomic datasets comprising over 1,400 clinical samples. This network-based approach evaluates the transcriptional correlation between the lysosomal gene network and functional biological pathways across diverse human cohorts. Module-Module association analysis performed on these human bladder datasets indicated that the lysosome module has strong positive associations with specific host defense modules, including "response to molecule of bacterial origin", "cell activation involved in immune response", and "innate immune response" (Figure 5A), highlighting a conserved functional link between lysosomal activity and immune defense pathways in the bladder epithelium. Altogether, these positive correlations suggest that enhanced lysosomal function represents a conserved pathway integrated within mucosal immunity across species, rather than an isolated cellular response unique to our experimental models.”

Significance:

General assessment: Solid experimental design with appropriate controls. Appropriate statistical rigor. Conclusions justified by the data. Limitations acknowledged. Differences in results between mice and humans acknowledged.

Advance: Moderate technical advance building on prior organoid models. Significant mechanistic advance because OM-89 has been widely used for a long time without detailed understanding of why it works. Moderate conceptual advance that urothelial cells are a targetable determinant of treatment outcomes.

Audience: I am a basic science researcher in the field of female urogenital tract microbiome and infections. Other researchers studying UTI will certainly be interested in this study. It also may be of interest to people studying other bladder conditions that involve the urothelium (bladder cancer).

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

This study examined the effect of OM-89 on UPEC infection, antibiotic clearance, and resurgence in mouse and human organoid models. The goal of the study was to understand the molecular mechanisms by which OM-89 is effective at preventing rUTI in patients.

Major comments:

The manuscript is well-written and the figures are well presented. Adequate background information is provided to give the study context and sufficient experimental details are provided to allow replication by other groups. Experiments contain appropriate controls and sufficient replicates to allow appropriate statistical analyses. The authors are careful to acknowledge the differences they observed between the mouse and human system and provide satisfactory potential explanations for these differences. The conclusions they draw are well supported by their data and none of their claims from their data are overstatements. Below are some, which I believe if addressed could improve the paper.

1. I think the authors overstate the novelty of the concept that the urothelium is an active targetable determinant of infection and treatment outcomes. This is not an entirely new concept since previous studies have examined antimicrobial peptides and other factors from the urothelium.
2. Depending on the target audience, the Module-Module association analysis could need more introduction. I am not a computational biologist and it was not obviously apparent how Figure 4A is generated and what it actually showing. How specifically does this analysis demonstrate a functional link between lysosomal activity adn immune defense pathways? Without further explanation, it is my opinion that this figure panel is an unnecessary distraction that is not required for any of the conclusions that the group can already draw from the rest of their data.

Significance

General assessment: The manuscript has several methodological strengths. These include the use of both mouse and human urothelial models, inclusion of appropriate controls, and sufficient replicates to ensure reproducibility. The statistical methods employed were appropriate. No major methodological weaknesses were identified. The descriptions of methods provide sufficient experimental details to allow the experiments to be reproduced by other labs. The authors did a nice job interpreting their data in light of previous literature. They did not overstate the magnitude or significance of their findings and were careful to acknowledge the limitations in their study design.

Advance: Moderate technical advance building on prior organoid models. Significant mechanistic advance because OM-89 has been widely used for a long time without detailed understanding of why it works. Moderate conceptual advance that urothelial cells are a targetable determinant of treatment outcomes.

Audience: I am a basic science researcher in the field of female urogenital tract microbiome and infections. Other researchers studying UTI will certainly be interested in this study. It also may be of interest to people studying other bladder conditions that involve the urothelium (bladder cancer).

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

In this paper, Tomasek and colleagues describe a series of experiments illuminating the effects of OM-89, a bacterial lysate taken orally for prevention of recurrent UTI, on intracellular dynamics of UPEC, using cell culture and organoid models. Suggestions for improvement and for clarification of the authors' conclusions and relevance to human UTI (and OM-89 use) are offered below.

Major points:

1. The data indicate that OM-89 exposure in the organoids enhances lysosomal degradation pathways and (in mBOs) autophagic flux, and the authors conclude this is a mechanism by which UPEC regrowth after antibiotic treatment (modeling rUTI) is inhibited by OM-89. They also show enhanced cellular uptake of fluorescently labeled antibiotics (ampicillin) in organoids - this leads them to conclude (and state in the paper's title) that increased intracellular antibiotic concentration effects increased killing of UPEC and decreased regrowth. These are two separate proposed mechanisms, and especially with regard to the antibiotics, they have not shown that increased intracellular antibiotic concentration actually kills intracellular UPEC in their model - only that regrowth as measured microscopically is less. In total, a mechanistic connection between the observed lysosomal effect and the intracellular antibiotic uptake, and which one is more important for UPEC control in this model, is incomplete. The precise wording of the paper's title should be reconsidered accordingly.
2. OM-89 is taken orally for rUTI prevention, and some "components" reach the urinary tract (line 81). But it isn't explained how applying OM-89 directly to organoids models how its components may reach the bladder epithelium (from the basolateral side, if the OM-89 is applied outside the organoids) in the whole animal or human. At the least, this limitation should be stated in the Discussion.
3. In the lysosome studies starting on line 319, the cultured cells are all infected (and either treated with OM-89 or not). What observations regarding number and size of vesicles, etc (all the measures in Fig 6) are evident when cells are treated with OM-89 only? These data should be presented (at least as a supplemental figure) to enable optimal interpretation of the OM-89+UPEC data in Fig 6. As the authors themselves indicate, OM-89 may be having a generalized effect on endocytic and/or autophagic flux by bladder epithelial cells, independent of infection.
4. With the organoids, beyond the microscopic quantification of UPEC, can CFUs be measured?

Minor points:

1. In Fig 1A, the "co-application" horizontal line is under the 7-10 hour window, but the text suggests that the application of antibiotics and OM-89 in this experiment is between 4-7 hours.
2. How are antibiotics and OM-89 "removed" at the 7-hour mark? This was not detailed in the Methods.
3. What time point was used for the transcriptomic profiling of organoids? This is not clear from the relevant Methods or Results sections.
4. In showing that OM-89 "attenuated" the magnitude of inflammatory responses (Fig 2C and S3B), it would be helpful to add a panel showing the comparison of OM89+UPEC to PBS alone - this would be expected to convey activity (red) in the infection-related pathways, but to a lower magnitude than seen in UPEC vs PBS.
5. Similarly, in the results outlined starting on line 196, it would be helpful to add a panel showing OM89+UPEC vs OM89 alone.
6. In line 236, what is meant by lysosomal "activation"? A more specific term should be chosen here.
7. In the Abstract (line 25), the phrase "Using bladder organoids..." is a dangling modifier.

Typographical and copyediting:

1. Line 74 should read "For instance..."
2. Line 76 should read "when combined with antibiotic therapy..."
3. Line 122 should read "...regrowth following antibiotic treatment" or "regrowth post-antibiotic treatment"
4. Line 138 should use "regimen" not "regime"
5. Line 196 delete comma after "Although"
6. Line 244 fully hyphenate "OM-89-mediated"
7. Line 374 should read "...significantly enhance antibiotic-mediated killing"

Significance

The paper is very well written and though a lot of data are included, the presentation is excellent and helps the reader to follow the story. The paper makes a strong contribution to the UTI pathogenesis field, and the use of mouse and human bladder organoids is innovative in studying intracellular UPEC. My scientific expertise as a reviewer is in UPEC pathogenesis, directly relevant to the content of this paper.

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

Learn more at Review Commons

Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity:

In this paper, Tomasek and colleagues describe a series of experiments illuminating the effects of OM-89, a bacterial lysate taken orally for prevention of recurrent UTI, on intracellular dynamics of UPEC, using cell culture and organoid models. Suggestions for improvement and for clarification of the authors' conclusions and relevance to human UTI (and OM-89 use) are offered below.

Major points:

1. The data indicate that OM-89 exposure in the organoids enhances lysosomal degradation pathways and (in mBOs) autophagic flux, and the authors conclude this is a mechanism by which UPEC regrowth after antibiotic treatment (modeling rUTI) is inhibited by OM-89. They also show enhanced cellular uptake of fluorescently labeled antibiotics (ampicillin) in organoids - this leads them to conclude (and state in the paper's title) that increased intracellular antibiotic concentration effects increased killing of UPEC and decreased regrowth. These are two separate proposed mechanisms, and especially with regard to the antibiotics, they have not shown that increased intracellular antibiotic concentration actually kills intracellular UPEC in their model - only that regrowth as measured microscopically is less. In total, a mechanistic connection between the observed lysosomal effect and the intracellular antibiotic uptake, and which one is more important for UPEC control in this model, is incomplete. The precise wording of the paper's title should be reconsidered accordingly.

We agree with the point raised by the reviewer that we did not show a mechanistic connection between the observed lysosomal effect and the intracellular antibiotic uptake. Further experiments dissecting the exact involved mechanistic pathways driving both - either in conjunction or separately - would improve our understanding on how OM-89 leads to its positive effects. In future studies we will focus on dissecting the underlying pathways and determining whether a mechanistic connection exists to explain the observed positive effects of OM-89 between lysosomal degradation and enhanced intracellular antibiotic accumulation.

Accordingly, we changed the title to "Targeted lysosomal activation in bladder epithelium enhances clearance of intracellular uropathogenic ____Escherichia coli". This revised title avoids implying a direct causal link between increased intracellular antibiotic accumulation and bacterial clearance, while still reflecting the central biological process identified in our study.

Additionally, we incorporated changes in the introduction, as highlighted in our reply to point number one raised by reviewer number two.

OM-89 is taken orally for rUTI prevention, and some "components" reach the urinary tract (line 81). But it isn't explained how applying OM-89 directly to organoids models how its components may reach the bladder epithelium (from the basolateral side, if the OM-89 is applied outside the organoids) in the whole animal or human. At the least, this limitation should be stated in the Discussion.

We thank the reviewer for pointing out this limitation. Although advanced in vitro models help to better mimic the in vivo situation, they still do not fully recapitulate all aspects of drug exposure and delivery observed in vivo. We included the following statement of limitation now in the discussion in line 449-459: "One limitation of our study is that OM-89 was applied directly to epithelial cultures and organoids, whereas in clinical use it is administered orally. Although pharmacokinetic studies have demonstrated systemic distribution and urinary accumulation of OM-89-derived components following oral administration (van Dijk, 1982), our experimental setup does not recapitulate the exact route, kinetics or concentration profiles encountered ____in vivo. Rather, our models were designed to determine whether bladder epithelial cells are capable of responding directly to OM-89-mediated signals and to identify the intracellular pathways involved. Given the documented systemic exposure following oral administration, direct effects on the urothelium are biologically plausible. However, future studies will be required to determine how the epithelial responses identified here integrate with the complex systemic and immune-mediated effects of OM-89 under physiological administration conditions."

In the lysosome studies starting on line 319, the cultured cells are all infected (and either treated with OM-89 or not). What observations regarding number and size of vesicles, etc (all the measures in Fig 6) are evident when cells are treated with OM-89 only? These data should be presented (at least as a supplemental figure) to enable optimal interpretation of the OM-89+UPEC data in Fig 6. As the authors themselves indicate, OM-89 may be having a generalized effect on endocytic and/or autophagic flux by bladder epithelial cells, independent of infection.

We thank the reviewer for this suggestion and agree that evaluating OM-89 treatment in the absence of infection provides important context for interpreting the infection-associated phenotypes shown in Figure 6. Our original intention was to focus the main manuscript on the effects of OM-89 during UPEC infection, and we therefore did not include the corresponding uninfected conditions.

As part of the planned revision, we will include additional supplementary data examining the effects of OM-89 alone in both murine and human bladder epithelial cells. Specifically, we will present analyses of Lamp1-positive lysosomal vesicles, lysosomal acidification (LysoSensor), and Cathepsin L activity under uninfected conditions. These experiments will allow readers to assess the extent to which OM-89 activates epithelial lysosomal pathways independently of infection and will provide important context for interpreting the infection-associated responses presented in the main figures.

We agree with the reviewer that OM-89 may exert broader effects on epithelial lysosomal pathways beyond the setting of infection, and inclusion of these data will strengthen the interpretation of OM-89 as a direct modulator of epithelial antimicrobial function.

With the organoids, beyond the microscopic quantification of UPEC, can CFUs be measured?

We understand the wish of the reviewer to see CFU measurements performed on organoids. However, this imposes strong technical limitations, mainly due to the tedious and technically challenging microinjections, e.g. the exact same amount of organoids would need to be infected by microinjections in both conditions (OM-89 and control) and injections would need to be performed extremely precise with no bacteria spreading into the surrounding extracellular matrix (frequently, organoids would get penetrated with the microneedle all the way, leading to bacteria being not injected into the lumen but rather into the wall of the organoid or even be released on the other side of the organoid) as otherwise also bacteria escaping into the extracellular matrix would be collected upon recovering the organoids from the extracellular matrix domes, strongly affecting the CFU measurements.

However, using differentiated monolayers of mouse bladder epithelial cells and performing a classic gentamicin protection assay would add an additional layer of information on the purely intracellular bacterial population, whilst overcoming the previously mentioned technical challenges. Therefore, we aim to perform CFU measurements on monolayers with and without OM-89 treatment to support our microscopic quantification and specifically be able to make a statement on reduced intracellular bacterial burden with OM-89 treatment. The CFUs will therefore provide an orthogonal measure of intracellular bacterial burden and complement the microscopy-based quantification during the infection and antibiotic-treatment phases.

Adding to this point of the reviewer, we wanted to clarify that with the higher-throughput microscopic quantification used in our approach (Thunder widefield microscope at 25x magnification), we cannot distinguish between strictly intracellular or tissue-associated bacteria, hence we used the wording "intra-organoid" in our methods section. We now added this information also into the results section for clarification (line 116): "Hence, the microscopy data represent the total "intra-organoid" bacterial burden at each experimental stage, without distinguishing the exact localization of the bacteria - which can be luminal, intracellular or tissue-associated.". To further reflect this, we stepped back from referring to antibiotic-mediated "killing", but changed the wording to antibiotic-mediated "clearance" or referred to reduced bacterial burden throughout the manuscript.

__Minor points:____ __

1. In Fig 1A, the "co-application" horizontal line is under the 7-10 hour window, but the text suggests that the application of antibiotics and OM-89 in this experiment is between 4-7 hours.

We thank the reviewer for pointing this out. Indeed, in the co-application regime, OM-89 is added at the same timepoint as the antibiotic - meaning straight after monitoring the growth phase at 4h post-infection (pi). We now adapted the horizontal line for the "co-application" treatment in Figure 1A accordingly to represent the time-point of OM-89 addition better. Additionally, we added a line for the antibiotic-treatment in order to further facilitate readability.

How are antibiotics and OM-89 "removed" at the 7-hour mark? This was not detailed in the Methods.

Although we had specified this in the methods section at line 603 "For every media exchange (e.g. antibiotic treatment or withdrawal), each well was washed with 9 ml of the respective media before leaving 1 ml in the well.", we realized the positioning was not optimal as we had mentioned this part under the point "Bacterial injection" in "Injection experiments". We therefore now separated this part, together with the lid preparation, from the "Bacterial injection" part and created the new subsection "Lid preparation for media changes" (line 613 onwards).

What time point was used for the transcriptomic profiling of organoids? This is not clear from the relevant Methods or Results sections.

As stated in the methods section, RNA for transcriptomic profiling from mBOs was extracted at 4h post-infection (pi) (line 842).

In showing that OM-89 "attenuated" the magnitude of inflammatory responses (Fig 2C and S3B), it would be helpful to add a panel showing the comparison of OM89+UPEC to PBS alone - this would be expected to convey activity (red) in the infection-related pathways, but to a lower magnitude than seen in UPEC vs PBS.

We thank the reviewer for this suggestion, as well as comment number 5 below. We comment more on both suggestions below.

Similarly, in the results outlined starting on line 196, it would be helpful to add a panel showing OM89+UPEC vs OM89 alone.

We performed the requested, combined GOBP analyses and they confirm that infection-associated pathways remain strongly activated in OM89-treated infected organoids relative to baseline (PBS) controls and relative to OM89-treated uninfected organoids. These results confirm the reviewer's hypotheses and further confirm the results presented in Figure 2C. In fact, induction of genes involved in detrimental effects of UPEC infections are induced at a lower extent when organoids are exposed to OM-89 only.

However, because the direct comparison between OM89+UPEC and PBS+UPEC already highlights the effect of OM-89 while controlling for the infection status, we believe our original analysis presented in Figure 2C remains the most informative representation of attenuation. Therefore, we will include the new comparison in the supplementary section of the manuscript.

In line 236, what is meant by lysosomal "activation"? A more specific term should be chosen here.

We thank the reviewer for this question and aim to increase readability of this section. With lysosomal activation in the first sentence of the mentioned paragraph, we referred to the observed effect of upregulated lysosomal pathways and altered lysosomal vesicles in the previous paragraph. However, to make the connection to the previous paragraph better, and given the comment number two of reviewer number two, we changed the whole first paragraph of this section. Therefore, the first sentence of this paragraph (line 235 onwards) reads now: "To test whether the observed effects on lysosomal pathways could mechanistically, at least in parts, explain OM-89-mediated protection, we first used Genebridge analysis (Li et al, 2019) to examine how the lysosomal gene signature identified in our RNA-seq data relates to host defense programs in the human bladder."

In the Abstract (line 25), the phrase "Using bladder organoids..." is a dangling modifier.

We thank the reviewer for pointing this out and changed the sentence accordingly to "In bladder organoids and differentiated epithelial monolayers, OM-89 promotes lysosomal acidification and increases lysosomal protease activity, driving intracellular UPEC toward degradative compartments."

Typographical and copyediting:

We thank the reviewer for pointing out the typographical errors below and we corrected them all.

1. Line 74 should read "For instance..."

2. Line 76 should read "when combined with antibiotic therapy..."

As this sentence is to emphasize the already observed protective effects of OM-89, and the two studies mentioned were either performed without or in combination with antibiotics, we changed the sentence to "For instance, rodent infection studies have demonstrated protective effects of OM-89 alone (Bosch et al, 1988; Lee et al, 2006) and in combination with antibiotic therapy (Canton et al, 2025; Bessler et al, 2010), although this observed in vivo protection could not be linked to any major quantitative changes in bladder immune cell infiltration (Canton et al, 2025), leaving the underlying molecular mechanism not fully resolved." for better readability.

Line 122 should read "...regrowth following antibiotic treatment" or "regrowth post-antibiotic treatment"

Line 138 should use "regimen" not "regime"

Line 196 delete comma after "Although"

Line 244 fully hyphenate "OM-89-mediated"

Line 374 should read "...significantly enhance antibiotic-mediated killing"

• *

__Significance:____ __

The paper is very well written and though a lot of data are included, the presentation is excellent and helps the reader to follow the story. The paper makes a strong contribution to the UTI pathogenesis field, and the use of mouse and human bladder organoids is innovative in studying intracellular UPEC. My scientific expertise as a reviewer is in UPEC pathogenesis, directly relevant to the content of this paper.

Reviewer #2

---

Evidence, reproducibility and clarity:

This study examined the effect of OM-89 on UPEC infection, antibiotic clearance, and resurgence in mouse and human organoid models. The goal of the study was to understand the molecular mechanisms by which OM-89 is effective at preventing rUTI in patients.

Major comments:

The manuscript is well-written and the figures are well presented. Adequate background information is provided to give the study context and sufficient experimental details are provided to allow replication by other groups. Experiments contain appropriate controls and sufficient replicates to allow appropriate statistical analyses. The authors are careful to acknowledge the differences they observed between the mouse and human system and provide satisfactory potential explanations for these differences. The conclusions they draw are well supported by their data and none of their claims from their data are overstatements. Below are some, which I believe if addressed could improve the paper.

1. I think the authors overstate the novelty of the concept that the urothelium is an active targetable determinant of infection and treatment outcomes. This is not an entirely new concept since previous studies have examined antimicrobial peptides and other factors from the urothelium.

We thank the reviewer for this important point and agree that the urothelium has long been recognized as an active participant in host defense through mechanisms such as antimicrobial peptide production, pathogen sensing and regulation of inflammatory responses. We have therefore revised the manuscript to avoid implying that urothelial involvement in infection outcome is itself a novel concept. Instead, we now emphasize the specific advance of our study: the identification of lysosome-centered epithelial activation as a therapeutically targetable mechanism that enhances intracellular bacterial clearance and potentiates antibiotic efficacy.

In the abstract we changed: "Our findings position the bladder epithelium from a passive barrier to an active, targetable determinant of treatment outcome and suggest host-directed modulation of epithelial antimicrobial pathways as a promising strategy to enhance intracellular bacterial clearance." to "Our findings demonstrate that bladder epithelial antimicrobial pathways can be pharmacologically reinforced to influence treatment outcomes by enhancing intracellular bacterial clearance." in line 30.

In the introduction we changed: "Together with increased intracellular accumulation of antibiotics across different classes, this leads to improved intracellular killing and reduced bacterial regrowth across diverse UPEC strains." to "Together with increased intracellular accumulation of antibiotics across different classes, this leads to improved intracellular clearance and reduced bacterial regrowth across diverse UPEC strains." in line 91 and "Together, these findings reveal a previously unrecognized epithelial lysosome-centered mechanism by which OM-89 enhances intracellular antibiotic performance and repositions the bladder epithelium from a passive reservoir of infection reactivation to an actively transformable antimicrobial compartment influencing treatment outcomes." to "Together, these findings reveal a previously unrecognized epithelial-centered mechanism by which OM-89 enhances intracellular antibiotic performance and establishes lysosomal activation as a therapeutically targetable component of epithelial host defense against intracellular UPEC." in line 96.

In the discussion we changed: "Together, these findings provide a mechanistic framework for the long-observed clinical efficacy of OM-89. Our findings reveal that the urothelium itself can be therapeutically targeted to reduce pathogen regrowth by transforming the epithelial barrier from a passive refuge for UPEC into an active defense site." to "Together, these findings provide a mechanistic framework for the long-observed clinical efficacy of OM-89 and identify epithelial lysosomal pathways as a therapeutically targetable component of host defense that can be used to improve intracellular bacterial clearance." in line 398 and "In the face of rising antimicrobial resistance (2024), strengthening epithelial antimicrobial function offers a complementary route to shift the bladder mucosa from a passive niche of bacterial survival and infection reactivation toward an active site of accelerated pathogen clearance." to "In the face of rising antimicrobial resistance (2024), our findings provide a mechanistic rationale for the clinical use of OM-89 and support epithelial lysosomal pathways as a promising target for host-directed therapeutic strategies that enhance intracellular bacterial clearance and improve the efficacy of existing antibiotics." in line 469.

Depending on the target audience, the Module-Module association analysis could need more introduction. I am not a computational biologist and it was not obviously apparent how Figure 4A is generated and what it actually showing. How specifically does this analysis demonstrate a functional link between lysosomal activity and immune defense pathways? Without further explanation, it is my opinion that this figure panel is an unnecessary distraction that is not required for any of the conclusions that the group can already draw from the rest of their data.

We thank the reviewer for this constructive critique. We agree that the rationale and interpretation of this analysis were not sufficiently explained in the original manuscript. We have therefore expanded the description of the MMAS approach and clarified how these data support the translational relevance of the lysosomal pathways identified in our experimental models. We also agree that for a broader biological audience, the computational framework and the strategic necessity of Figure 4A required a clearer introduction and stronger justification.

To address the reviewer's concerns, we have thoroughly revised the text (lines 235-250) to clarify the methodology and emphasize the essential translational value this analysis adds to our study:

• How the figure is generated and what it shows: We have added explicit language clarifying that we used a computational Module-Module Association Score (MMAS) to evaluate the transcriptional correlation between the lysosomal gene network and functional biological pathways. Rather than relying on a single experimental dataset, this analysis compiles data across eight independent human bladder transcriptomic datasets encompassing over 1,400 clinical samples.
• Demonstrating the link to immune pathways: We have explicitly named the specific host defense modules highlighted in Figure 4A, namely "Response to molecule of bacterial origin", "cell activation involved in immune response", and "innate immune response" to guide the reader directly to the strong positive correlations shown in the panel.
• Justifying its inclusion (mouse-to-human translational bridge): While the rest of our data characterizes the cellular mechanics of OM-89 in murine organoids and cell culture, Figure 4A demonstrates that the link between lysosomal activity and bacterial defense is a conserved feature of bladder tissue biology across species. This cross-species alignment (our mouse-data at this stage of the manuscript compared to human-derived data) provides critical clinical justification for targeting epithelial lysosomal pathways as a therapeutic strategy in human patients. The new paragraph reads as follows: "To test whether the observed effects on lysosomal pathways could mechanistically, at least in parts, explain OM-89-mediated protection, we first used Genebridge analysis (Li et al., 2019) to examine how the lysosomal gene signature identified in our RNA-seq data relates to host defense programs in the human bladder. To evaluate the translational relevance of our experimental findings, we used a computational Module-Module Association Score (MMAS) analysis across eight independent human bladder transcriptomic datasets comprising over 1,400 clinical samples. This network-based approach evaluates the transcriptional correlation between the lysosomal gene network and functional biological pathways across diverse human cohorts. Module-Module association analysis performed on these human bladder datasets indicated that the lysosome module has strong positive associations with specific host defense modules, including "response to molecule of bacterial origin", "cell activation involved in immune response", and "innate immune response" (Figure 4A), highlighting a conserved functional link between lysosomal activity and immune defense pathways in the bladder epithelium. Altogether, these positive correlations suggest that lysosomal activation represents a conserved pathway integrated within mucosal immunity across species, rather than an isolated cellular response unique to our experimental models."

__Significance:____ __

General assessment: Solid experimental design with appropriate controls. Appropriate statistical rigor. Conclusions justified by the data. Limitations acknowledged. Differences in results between mice and humans acknowledged.

Advance: Moderate technical advance building on prior organoid models. Significant mechanistic advance because OM-89 has been widely used for a long time without detailed understanding of why it works. Moderate conceptual advance that urothelial cells are a targetable determinant of treatment outcomes.

Audience: I am a basic science researcher in the field of female urogenital tract microbiome and infections. Other researchers studying UTI will certainly be interested in this study. It also may be of interest to people studying other bladder conditions that involve the urothelium (bladder cancer).

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Referee #2

Evidence, reproducibility and clarity

This study examined the effect of OM-89 on UPEC infection, antibiotic clearance, and resurgence in mouse and human organoid models. The goal of the study was to understand the molecular mechanisms by which OM-89 is effective at preventing rUTI in patients.

Major comments:

The manuscript is well-written and the figures are well presented. Adequate background information is provided to give the study context and sufficient experimental details are provided to allow replication by other groups. Experiments contain appropriate controls and sufficient replicates to allow appropriate statistical analyses. The authors are careful to acknowledge the differences they observed between the mouse and human system and provide satisfactory potential explanations for these differences. The conclusions they draw are well supported by their data and none of their claims from their data are overstatements. Below are some, which I believe if addressed could improve the paper.

1. I think the authors overstate the novelty of the concept that the urothelium is an active targetable determinant of infection and treatment outcomes. This is not an entirely new concept since previous studies have examined antimicrobial peptides and other factors from the urothelium.
2. Depending on the target audience, the Module-Module association analysis could need more introduction. I am not a computational biologist and it was not obviously apparent how Figure 4A is generated and what it actually showing. How specifically does this analysis demonstrate a functional link between lysosomal activity adn immune defense pathways? Without further explanation, it is my opinion that this figure panel is an unnecessary distraction that is not required for any of the conclusions that the group can already draw from the rest of their data.

Significance

General assessment: The manuscript has several methodological strengths. These include the use of both mouse and human urothelial models, inclusion of appropriate controls, and sufficient replicates to ensure reproducibility. The statistical methods employed were appropriate. No major methodological weaknesses were identified. The descriptions of methods provide sufficient experimental details to allow the experiments to be reproduced by other labs. The authors did a nice job interpreting their data in light of previous literature. They did not overstate the magnitude or significance of their findings and were careful to acknowledge the limitations in their study design.

Advance: Moderate technical advance building on prior organoid models. Significant mechanistic advance because OM-89 has been widely used for a long time without detailed understanding of why it works. Moderate conceptual advance that urothelial cells are a targetable determinant of treatment outcomes.

Audience: I am a basic science researcher in the field of female urogenital tract microbiome and infections. Other researchers studying UTI will certainly be interested in this study. It also may be of interest to people studying other bladder conditions that involve the urothelium (bladder cancer).

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #1

Evidence, reproducibility and clarity

In this paper, Tomasek and colleagues describe a series of experiments illuminating the effects of OM-89, a bacterial lysate taken orally for prevention of recurrent UTI, on intracellular dynamics of UPEC, using cell culture and organoid models. Suggestions for improvement and for clarification of the authors' conclusions and relevance to human UTI (and OM-89 use) are offered below.

Major points:

1. The data indicate that OM-89 exposure in the organoids enhances lysosomal degradation pathways and (in mBOs) autophagic flux, and the authors conclude this is a mechanism by which UPEC regrowth after antibiotic treatment (modeling rUTI) is inhibited by OM-89. They also show enhanced cellular uptake of fluorescently labeled antibiotics (ampicillin) in organoids - this leads them to conclude (and state in the paper's title) that increased intracellular antibiotic concentration effects increased killing of UPEC and decreased regrowth. These are two separate proposed mechanisms, and especially with regard to the antibiotics, they have not shown that increased intracellular antibiotic concentration actually kills intracellular UPEC in their model - only that regrowth as measured microscopically is less. In total, a mechanistic connection between the observed lysosomal effect and the intracellular antibiotic uptake, and which one is more important for UPEC control in this model, is incomplete. The precise wording of the paper's title should be reconsidered accordingly.
2. OM-89 is taken orally for rUTI prevention, and some "components" reach the urinary tract (line 81). But it isn't explained how applying OM-89 directly to organoids models how its components may reach the bladder epithelium (from the basolateral side, if the OM-89 is applied outside the organoids) in the whole animal or human. At the least, this limitation should be stated in the Discussion.
3. In the lysosome studies starting on line 319, the cultured cells are all infected (and either treated with OM-89 or not). What observations regarding number and size of vesicles, etc (all the measures in Fig 6) are evident when cells are treated with OM-89 only? These data should be presented (at least as a supplemental figure) to enable optimal interpretation of the OM-89+UPEC data in Fig 6. As the authors themselves indicate, OM-89 may be having a generalized effect on endocytic and/or autophagic flux by bladder epithelial cells, independent of infection.
4. With the organoids, beyond the microscopic quantification of UPEC, can CFUs be measured?

Minor points:

1. In Fig 1A, the "co-application" horizontal line is under the 7-10 hour window, but the text suggests that the application of antibiotics and OM-89 in this experiment is between 4-7 hours.
2. How are antibiotics and OM-89 "removed" at the 7-hour mark? This was not detailed in the Methods.
3. What time point was used for the transcriptomic profiling of organoids? This is not clear from the relevant Methods or Results sections.
4. In showing that OM-89 "attenuated" the magnitude of inflammatory responses (Fig 2C and S3B), it would be helpful to add a panel showing the comparison of OM89+UPEC to PBS alone - this would be expected to convey activity (red) in the infection-related pathways, but to a lower magnitude than seen in UPEC vs PBS.
5. Similarly, in the results outlined starting on line 196, it would be helpful to add a panel showing OM89+UPEC vs OM89 alone.
6. In line 236, what is meant by lysosomal "activation"? A more specific term should be chosen here.
7. In the Abstract (line 25), the phrase "Using bladder organoids..." is a dangling modifier.

Typographical and copyediting:

1. Line 74 should read "For instance..."
2. Line 76 should read "when combined with antibiotic therapy..."
3. Line 122 should read "...regrowth following antibiotic treatment" or "regrowth post-antibiotic treatment"
4. Line 138 should use "regimen" not "regime"
5. Line 196 delete comma after "Although"
6. Line 244 fully hyphenate "OM-89-mediated"
7. Line 374 should read "...significantly enhance antibiotic-mediated killing"

Significance

The paper is very well written and though a lot of data are included, the presentation is excellent and helps the reader to follow the story. The paper makes a strong contribution to the UTI pathogenesis field, and the use of mouse and human bladder organoids is innovative in studying intracellular UPEC. My scientific expertise as a reviewer is in UPEC pathogenesis, directly relevant to the content of this paper.

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Reply to the reviewers

Point-by-point response to the reviewers (____blue____)

Dear Editor,

Thank you for taking care of our manuscript. We are pleased to see that the reviewers are positive about our manuscript. We have amended our manuscript to address nearly all the reviewer’s comments. See below our point by points answer Although we cannot fully establish the exact function of the serine protease homolog Skanda in the Drosophila immune response, our study that combines both biochemistry and genetic provides important insight on the Toll-PO cascade and its complexity

With best regards,

Bruno Lemaitre on the behalf of the authors

---

__Review____er #1 (Evidence, reproducibility and clarity (Required)): __

In the manuscript entitled "The serine protease homolog Skanda modulates Toll-phenoloxidase-mediated immunity in Drosophila," Vasanth et al characterize in detail a previously unstudied component of the insect immune response using first biochemical and then in vivo methods. Using proteins overexpressed and purified from insect cells, the authors provide evidence that Skanda could be a negative regulator of the SP cascade, impacting cleavage of proHayan and proPsh, and consequently Toll pathway and PPO1 activation. This work reaches further by transposing these findings into the D. melanogaster in vivo model. Here, however, the picture becomes more confusing as Skanda at native levels does not appear to regulate either the Toll pathway or the melanization cascade. Only one strong phenotype was identified in that decreased expression of Skanda increased susceptibility to S. aureus infection while increased expression decreased susceptibility. The mechanism for this remains unclear. To their credit, the authors carry out an in-depth analysis to rule out all the obvious possibilities. In the discussion, the authors explore the basis of discrepancies between their biochemical and genetic findings. We would suggest that an additional one to consider is differing roles or behaviors of Skanda in the microenvironments of the local site of injury (where S. aureus may be contained when it is tolerated) and the hemolymph. In summary, this is a valuable analysis of the innate immune component Skanda whose role has become somewhat clearer through these studies, but still remains obscure.

We thank the reviewer for this general assessment of our article. We agree with his idea that discrepancies between the biochemical and genetic findings arise from differing roles or behaviors of Skanda in the microenvironments of the local site of injury and the hemolymph’. We added the following sentence in the discussion: ‘The presence of Skanda in the hemolymph (Rommelaere et al. 2025) suggests a role in the systemic immune response; however, we cannot exclude that it may be particularly important within the local microenvironments at sites of injury’.

__Major Comments __ - To assess bimodal distribution of bacterial ds within single flies in Fig 6E, authors should either: increase the sample size to allow for proper statistical assessment of different distributions among genotypes, specifically between w1118 and skanda_d107; or, provide a modelling framework for statistical testing. Otherwise, the present results seem insufficient to conclude that Skanda is playing a role in resistance to S. aureus. We agree with the reviewer that our bacterial count was not enough developed. In the revised version we add a new Figure 6E with two time points 13h and 16h that were chosen before flies start to die from S. aureus. We observe at 13h a significantly higher bacterial count in the Skanda mutants but not at the 16 hours although there is higher proportion of wild-type flies that have clear the bacteria. These observations suggest a role of Skanda to resist, but also tolerate S. aureus. The fast killing induced by systemic injury with a low dose S. aureus made difficult to find a condition that would allow to see a clear load difference. So we have amended our text to highlight that Skanda could also play a role in tolerance.

• Another way to assess a role for tolerance in the Skanda mutant would be to measure BLUDs (https://doi.org/10.7554/eLife.28298 ) and/or transcription of CrebA.

We agree with the reviewer but measuring the BLUD with S. aureus is rather challenging as flies die quickly to this bacterium. As mentioned above and following revised figure 6E, we discuss in the revised version that Skanda could be involved in both resistance and tolerance.

• The error bars on qRT-PCR datasets are large, the data points are not shown so we do not know how many replicates were included in the graphs (Fig 5 B and C, Fig 6C, Fig 7 A and B, and Fig 8B). Bar plots are not the most faithful reproduction of biological datasets, as they can hinder significant information regarding datapoints distribution and variation (Beyond Bar and Line Graphs: Time for a New Data Presentation Paradigm | PLOS Biology). We advise that, particularly in the case of datasets such as qRT-PCR, the final values of fold change are represented with individual dots, with the mean value clearly represented, whether with or without the additional bar graph. Furthermore, no statistical tests were applied to determine significance. Data points should be shown and appropriate statistical tests should be applied. The number of biological replicates should be included in the analysis and the statistical test applied should be noted in the figure legends.

We have changed the figures related to qRT-PCR to show the individual points and we have added statistics in the revised version.

• Although there are claims of Skanda conferring resistance to S. aureus infection, only Drs levels are tested. These conclusions could be strengthened by assessing expression levels of additional AMPs.

In the revised manuscript, we report the expression of BomS1 in wild-type, skanda, and spz mutants following S. aureus infection. As previously observed for Drosomycin, Skanda does not markedly affect BomS1 expression (new Supplementary Figure S3E).

__Minor Comments __ - Parag. 1: (data not shown) should be removed and if possible AlphaFold prediction of skanda conformation added. Alternatively, remove sentence.

We have removed (data not shown) and indicated that the information derived from Alphafold.

• Parg. 3: 1000 mL? why not 1L?

Corrected.

• Parag. 5: , in last sentence that should be .

Corrected.

• Parag. 6: "a role at the same position..." does not convey the correct messageWe have improved the sentence for ‘Our results indicate that Grass processes Skanda in the Toll–PO SP cascade, consistent with Skanda acting at the same level of the proteolytic cascade as Hayan and Psh’.

• Figure axes (5D, 5E, 6D, etc...) of melanization assays are wrongly named "% melanisation", with "s"

We have corrected for “Melanization”.

• Parag. 21: compound mutants (if correctly interpreted as dataset presented in Fig. 8B) were tested at 6h, 24h and 48h, and not 32h, as written in the text

Indeed, in figure 8B, we monitored expression at 6, 24 and 32h and not 48h. This has been corrected.

• Results section "skanda is not mandatory for the activation of the Toll pathway" adopts a literal translation which would probably be better phrased as "is not essential"

We have corrected accordingly.

• Discussion parag. 2: "Skanda exhibits..."

• Discussion last parag: "..., but also underlies..."

• It has been evidenced that

This has been corrected.

Additional comments: - The sentence on page 2 beginning with "Upon binding, these PRRs..." is very long and difficult to follow. This should be rewritten.

We have split this sentence in two shorter ones for clarity.

• In many places in the manuscript bacterial "dose" is used in place of bacterial burden. The dose is the amount of a substance or bacterium given to the animal.

We have changed ‘bacterial dose’ for ‘bacterial burden’ when relevant, and we have kept the term “dose” when we mentioned the OD used to infect flies.

Page 11: Skanda is described as a placeholder when I think a (competitive) inhibitor would be more appropriate.

We agree that Skanda functionally resembles a competitive inhibitor, but several key differences set it apart from classical small-molecule inhibitors. First, Skanda is comparable in size and structure to Persephone and Hayan, natural substrates of Grass. Second, Skanda-like SPHs, which have close SP paralogs (e.g., Psh), are common in insects (Cao and Jiang, 2019), indicating that they may constitute a distinct class of negative regulators that warrants its own terminology. Moreover, because amplification in protease cascades typically occurs at the terminal step. Negative regulation by Skanda in an intermediate step could be more stochiometric than the freely reversible inhibition expected for a typical competitive inhibitor. As Skanda’s mechanism remains unclear. the neutral term “placeholder” seems more appropriate than “competitive inhibitor”.

**Referee cross-commenting**

I agree with the comments of the other reviewers.

Reviewer #1 (Significance (Required)):

Strengths: The authors take a multi-disciplinary biochemical and in vivo approach to understand the molecular interactions among SPs and SPHs and thereby uncover the role of the protein Skanda that might otherwise not have been appreciated. They have made extensive use of novel transgenic fly lines, generated in the context of this study, and have thoroughly tested their specificity and cis-acting potential. These will provide a resource to the field. In addition to the new description of Skanda, these findings strengthen previous knowledge regarding systemic infections with different bacteria (M. luteus, S. aureus) and reproduce the known redundancies of Psh and Hayan modes of action. Moreover, this research is relevant for the expansion of basic knowledge on innate immunity, particularly in the field of insect-pathogen interactions, making use of S. frugiperda cell lines and D. melanogaster adults and larvae. Although not at the focus of this work, the evolutionary conserved nature of these aspects of innate immunity across these two distant species enhance the importance of these findings.

Weaknesses: Some assays do not include enough biological replicates and others do not have enough information on how many biological replicates were performed. Therefore, the conclusions drawn are difficult to assess. Lack of statistical analysis on the qPCR experiments complicates the interpretation of results.

We thank the reviewer for his assessment. We have added the number of replicates in the revised version and make visible the variability of our data.

__Review____er #2 (Evidence, reproducibility and clarity (Required)): __

Summary In this work the authors identify the SPH skanda as an important player in Drosophila resistance to S. aureus infections independent of Toll and classical melanization. The authors conducted rigorous in vitro assays using recombinant proteins of various SPs in the Drosophila Toll-PO cascade to show that skanda negatively regulates activation cleavage of SPs at the level of and downstream of Psh and hayan, two key SPs that converge on Toll pathway activation with the latter playing a central role in cuticular melanization. In parallel, genetic analysis using mutant flies showed that skanda does not negatively regulate Toll pathway nor melanization. Only skanda over expression in vivo led to a reduction in S. aureus melanization which, in my opinion, is most likely due to the artificial increase in the in vivo concentration of the protein rather than an indication of a potential true function. Altogether this an interesting work as it shows the discrepancies between the biochemical and genetic approaches when it comes to dissecting the insect SP cascades regulating melanization and Toll as highlighted by the authors themselves in the discussion section. All experimental work is well controlled, methodology is robust and results are adequately discussed. I have some comments concerning few experiments and interpretations that in my opinion warrant further discussion.

We thank the reviewer for the analysis and agree that the result showing than Skanda negatively regulates melanization could be due to over-expression.

__Major comments: __ 1- It seems that SP48 and Grass can redundantly cleave Skanda although the later cleaves more strongly. (Fig 3B) Can other downstream SPs cleave skanda? Can ModSp alone cleave skanda? (ModSP + skanda lane was absent for Fig 3B). It is important to test these possibilities as the in vitro system may be quite relaxed as to the specificity of these cleavage events and may not reflect what happens in vivo. In fact it has been shown in Anopheles gambiae that SPH can be redundantly cleaved by multiple SP in the protease cascade. Although these are cascades with certain hierarchy, information can still flow in more than one direction along the different branches of these cascades.

We tested whether ModSP could cleave pro-Skanda and found that it did not (data not shown). This result is consistent with our expectations, as ModSP has a chymoelastase-like specificity and preferentially cleavage after Leu. In contrast, Skanda is cleaved by Grass and cSP48, both of which are trypsin-like proteases.

At present, there is no straightforward way to assess whether downstream SPs activate pro-Skanda. Obtaining an active downstream SP would require sequential activation of all its upstream enzymes, and it is nearly impossible to completely remove these activating proteases afterward. As a result, it is difficult to distinguish the activity of a downstream SP from that of cSP48 and Grass. We are currently developing a new approach to overcome this limitation.

2- In Fig 4B and 4C the bands of active forms should be quantified from at least 3 immunoblots for robust results especially in Fig 4C where the differences are minimal.

As suggested by the reviewer, we quantified the band intensities from four independent blots and presented the data in Fig. 4B and 4C (lower panels).

3- It is not clear to me why skanda should have a specific role in resisting S. aureus infections despite that S. aureus is not a natural pathogen of Drosophila? Has other Gram-positive and Gram-negative bacteria been tested?

It is true that S. aureus is unlikely to be a natural pathogen of Drosophila. However, this bacterium has been used in several studies (notably Dudzic 2019) to uncover a specific activity associated with melanization modules that is distinct from cuticular blackening. For this reason, we believe that S. aureus provides a sensitive assay to monitor this particular immune mechanism. We further hypothesize that other bacteria related to S. aureus—possibly members of the Staphylococcus family—may infect Drosophila and could be controlled by Skanda. We chose not to elaborate on this point to avoid overextending the scope of the article.

4- In Fig 6E more points should be collected for statistical power. It is also better to show these data that are not normally distributed in violin charts or boxes and whiskers which give a better indication as to which quartile the bulk of the data belongs.

We have addressed this point (see answer to Reviewer 1).

Minor comments: 5- In Figures 3 and 4, It would be easier to follow the cleavage events if a schematic drawing is provided showing the sequence of activation cleavage events of the tested SPs

Because the order of the two cleavage events is unclear, we felt it was simpler to include the putative cleavage sites in Fig. 2B and refer interested readers to Fig. S1, Table S1, and Fig. 3 legend.

6- The fact that PPO1/PPO2 depleted flies exhibit increased Drs expression could be due to increased bacterial proliferation in this mutant background that trigger increased Toll stimulation, rather than a negative feedback mechanism. This increased proliferation is shown in Fig 6E.

This is a good point. The higher expression of Drs in PO1/PPO2 depleted flies could be associated to higher bacterial load in the mutant, or to negative feedback of the melanization reaction. This higher Toll pathway activation has been further characterized in Liu et al., (Plos pathogen 2025) where it was suggested that it relate to a negative feedback loop between the Toll and the melanization cascade.

7- In Fig 6E more points should be collected for statistical power. It is also better to show these data that are not normally distributed in violin charts or boxes and whiskers which give a better indication as to which quartile the bulk of the data belongs.

We have addressed this point. See answer to reviewer 1 for discussion.

8- A phenotype for skanda in melanization was observed only in over-expression assays which may artificially alter molecular interactions in the cascade.

We agree with this statement and we have added a comment in the discussion of the revised manuscript about the potential artifactual results due to over-expression.

9- Page 10 last paragraph "peak expression at 32 hrs or 48 hrs as shown on the figure?"

This is 32h and has been corrected.

10- The differences in Drs expression levels in Hayan-pshDef and psh-skandaDef double mutant flies infected with M. luteus and S. aureus is surprising. I wonder whether the observed differences are due to biochemical differences in the microbial surfaces to which these cascades are recruited.

Drs expression is markedly higher following systemic infection with M. luteus than with S. aureus, consistent with the different bacterial doses used. We deliberately employed a low dose of S. aureus because this condition reveals a pronounced susceptibility in skanda flies. Consequently, direct comparison between these two infection regimes remains challenging.

11- There are several typos in the manuscript

We have carefully re-read the manuscript and corrected several typos.

Reviewer #2 (Significance (Required)):

The main strength of this work is that it combines biochemistry and genetics in a strong genetic model to characterize the biochemical interactions between SPH and Sp in clip cascades and relate the relevant interactions observed in vitro with potential in vivo functions. This is the first time that such a rigorous combined approach was adopted to the study of these cascades. The results obtained also show the advantages and limitations of each approach. As such i believe this study will be of interest to a broad audience in the field of insect immunity.

__Review____er #3 (Evidence, reproducibility and clarity (Required)): __

__Summary: __

Serine protease cascades are central for activation of immune responses in insects. In Drosophila melanogaster, Toll signaling pathway has been quite extensively studied, and several serine proteases, serpins and serine protease homologs (SPH) with functions in Toll activation have been identified. In this work, the authors characterize a new component of this system, a SPH which they name Skanda. Skanda seems to have multiple roles/points of action, on one hand participating in the regulation of Toll together with the established serine protease in the Toll activation, Psh, and on the other hand controlling the response to a systemic S. aureus infection, via not yet fully specified mechanism.

__Major comments: __

Key conclusions made in this work are convincing, and backed up by the data presented. The data and methods are presented in a way that allows reproduction of the experiment. The number of individuals used especially in the infection experiment (20 male flies per a replicate) is on the lower side, but the experiments are adequately replicated and the effects seen are clear.

While this work contributes to our understanding of the regulatory mechanisms governing Toll signaling, at times the authors' reasoning is difficult to follow. I recognize that this is a complex topic, with multiple upstream branches activating Toll signaling, and the authors do consider various mechanisms that could explain their findings. However, the manuscript would benefit from additional clarification, perhaps through a schematic model illustrating the proposed effects of Skanda, to help readers position Skanda within the broader context of Toll signaling. We have done our best to explain the Toll serine protease and added a figure at the beginning of the manuscript. Since we cannot position Skanda in the Toll-Po cascade yet, we prefer to avoid drawing a model. We believe that this study highlights our ignorance of the complexity of serine protease cascades acting upstream of Spätzle and Melanization.

Statistical analyses for the Drs expression experiments are lacking.

The statistical analysis for Drs expression has been added in the revised version.

__Minor comments: __

The authors could explain what type of cells the sf9 cells are and why they decided to use them.

Sf9 cells are an insect ovarian cell line derived from Spodoptera frugiperda and are widely used for baculovirus-mediated expression of eukaryotic proteins. They support proper protein folding, disulfide bond formation, and post-translational processing. This information is now mentioned in the Result section in addition to methods.

Band intensities could be measured and plotted for the immunoblots. The immunoblot methods should be fully described in the Materials and methods section.

Thanks for the suggestion. We have done this accordingly and included the results in Fig. 4B and Fig. 4C (lower panels). Brief descriptions of densitometric analyses have been added to the figure legends.

Protein levels of Skanda in the Skanda mutant could be shown as the mRNA levels remain relatively high (Sup. Fig 3B). If this is not possible, could the authors comment on the remaining expression of Skanda in the Skanda mutants?

We have added a comment on this point: The skanda mutation is a frameshift mutation that affects the coding sequence. There are still transcripts although not functional. The decreased expression of Skanda in SkandaD107 is probably due to non-sense-mediated RNA decay caused by the frameshift.

Under the heading "Loss of skanda does not further enhance the cuticular melanization defects caused by the loss of Hayan or psh" the text should refer to figure 5D not 5B.

We have corrected this mistake in the revised version.

Figure 6C shows that Drs expression is higher in the Skanda mutant than in controls at 32 h post S. aureus infection (although this has not been statistically tested). The authors don't mention this result in the manuscript, but to me it fits with the idea of Skanda acting as a negative regulator (the effect of which is accumulating and seen only late after infection). Could the authors comment on this? We do not think that the higher expression of Drs in Skanda mutant upon S. aureus systemic infection is due a negative regulation the Toll pathway but rather to higher S. aureus burden. We conclude this because Drs is not higher than the wild-type upon injection of M. luteus and proteases. At this stage, we cannot exclude that there are differences between M. luteus and S. aureus.

Under the heading "Psh and skanda redundantly regulate Toll signaling", the comparison should likely be between Figures 7A-7B and 5B-C (rather than 5A). When examining the effects of single versus double mutants on Drs expression, the Psh-Skanda double mutant clearly reduces Drs more than the Psh single mutant. However, in the context of microbial proteases, the pattern appears different: there is virtually no difference at 6 hours, while at 48 hours there may be a slight decrease in Drs expression in the double mutant compared to the Psh single mutant, although this difference would likely not reach statistical significance if tested. I don't know what this could mean, but I'd like to hear the authors' take on this. The reviewer is correct and we have revised our manuscript to mention the appropriate figure. Figures 7A-7B and 5B-C.

The reviewer raised a good point; we believe that the additional effect of Skanda in absence of Psh is less marked upon microbial proteases because Psh already has a strong effect by itself in sensing proteases. In contrast there is higher redundancy between Psh and Hayan upon M. luteus and consequently the double mutant psh, Skanda have a stronger effect.

__**Referee cross-commenting** __

I also agree with the comments and points raised by the other reviewers.

__Review____er #3 (Significance (Required)): __

Research on the Drosophila immune response has significantly advanced our understanding of (innate) immune responses, both generally and in an evolutionary context. Despite over three decades of study, this work demonstrates that there are aspects of Toll signaling that remain unresolved. The authors identify a novel regulator of the Toll pathway and begin to elucidate its functions. Equally important, their findings underscore the complexity and context-dependency of the regulatory events that shape immune responses.

We fully agree with the assessment of the reviewer. Our study highlights the complexity (and our ignorance) of this important facet of Drosophila immunity, as mentioned in the last sentence of the discussion.

My fields of expertise are Drosophila melanogaster, innate immunity, cell-mediated immunity.

__Review____er #4 (Evidence, reproducibility and clarity (Required)): __

__Summary __

In this study, the authors investigate the function of Skanda, a serine protease homolog (SPH) in Drosophila innate immunity using both biochemical and genetical approaches. The reason to focus on this SPH is that it lies at the same locus as two key proteases of Drosophila immune defenses, Hayan and Persephone, all of which are induced by an immune challenge. After having modeled this SPH and shown that the three amino-acid of the serine protease catalytic triad are either mutated or poorly oriented, they report that Skanda may limit the cleavage of proteases downstream of Grass, a key event for their biochemical activation. The study of an isogenized, putatively null, mutant line failed to reveal any impact of skanda on Toll pathway activation nor on melanization, albeit a strong but not moderate overexpression somewhat inhibits the formation of a melanization scab only after "clean" but not septic injury. These results are not in keeping with the biochemical analysis: the mutant would have been expected to display an enhanced immune response. Unexpectedly, skanda mutants are as highly susceptible to a low amount of Staphylococcus aureus injection as flies deleted for the adult-expressed phenoloxidases PPO1 and PPO2, melanization playing a key role in host defense in this infection paradigm. No strong impact on the bacterial load was detected at the sole investigated time point, 24h. Because the analysis of the single skanda mutant did not unambiguously reveal its role in host defense, the authors then studied double or triple mutants of the three protease genes and found a redundant role for Skanda with Persephone for Toll pathway activation after a challenge with a nonpathogenic Gram-positive bacterium or a bacterial protease. In the case of S. aureus infection, a strong induction of the Drosomycin gene, is observed at 48h of infection in the compound mutants, which was not observed with the nonpathogenic challenges. Evidence, reproducibility and clarity

__Major comments __

The authors state that "These results are consistent with a role of Skanda in resistance to S. aureus". This conclusion rests on a very fragile experiment that measured the bacterial burden 24h after challenge with a low dose of S. aureus: whereas wild-type control flies exhibit a dual low and high distribution of bacterial loads, skanda flies exhibit only the higher values. However, the bacterial load in skanda appears to be as high in persephone mutant flies that are much less sensitive to S. aureus than skanda flies. This makes it highly unlikely that the high susceptibility of skanda to S. aureus is due solely to resistance. The problem is compounded by the poor description of the experiment: it is not stated anywhere how many times the experiment has been performed, whether pooled data are shown, what each data point represents, pooled or single flies. A fine-grained time course with more biological samples would definitely be needed to convince the reader of a (limited) role in resistance. The authors do not consider the alternative, but not exclusive, possibility that skanda plays also a role in disease tolerance. The determination of the bacterial load upon death of single flies may provide some clues about this alternative function (Duneau et al., eLife, 2017). Another approach might be to determine whether the bacterial supernatant is toxic and whether skanda might protect from this toxicity. As Bomanins play a role in the host defense against S. aureus (this study, but see also Hanson et al., eLife 2019 in which the 55C deficiency susceptibility phenotype was stronger) and given the role of Bomanins in host defense against Gram-positive bacteria or fungal infections both in resistance and disease tolerance (e.g., Clemmons et al. PLoS Pathogens 2015, Lindsay et al., J. Innate Immun, 2018, Xu et al., EMBO Reports 2023, Lou et al., BioRxiv, 2025) and that BomS1 has an optimal Dorsal-related Immune Factor Binding site (Busse et al. EMBO J. , 2007), it may be useful to monitor the expression of several Bom genes in complement to that of the expression of Drosomycin, especially after S. aureus challenge. Furthermore, BomT1 is the only peptide that appears to play a role in resistance against Gram-positive bacteria, namely against E. faecalis. This series of qPCR experiments is rapid to make, provided the authors have kept the cDNAs of their samples.

To address the reviewer’s comment, we extended the bacterial load analysis of S. aureus in skanda mutants (new figure 6E). Our results support a role for Skanda in both resistance and disease tolerance. This point is now briefly discussed in the Results section, and we have added references highlighting a role of the Toll pathway in disease tolerance. We did not elaborate further, as accurately monitoring S. aureus burden following low-dose infection remains technically challenging given the high pathogenicity of this bacterium.

In the Discussion, the authors speculate "that Skanda acts at the level of Persephone-Hayan to allow Hayan to activate the Toll pathway. Skanda would skew the activity of the Persephone-Hayan platform to induce Toll signaling and resistance to S. aureus rather than cuticular melanization". This model does not fit with the fact that SPE is only moderately susceptible to S. aureus (Dudzic et al., 2019) and that spätzle mutant flies are either not sensitive at all (Dudzic et al., 2019) or moderately sensitive to it (Hanson et al., eLife, 2019) (see also below). Whether it may apply to host defense against other pathogens remains to be determined. To better understand the function of skanda, considering only S. aureus may be limiting as this bacterium is fundamentally not susceptible to the canonical Toll intracellular signaling cascade (e.g., Bischoff et al, Nat Immunol, 2004, Dudzic et al, Cell Reports, 2019) and to the final part of the Toll-activation proteolytic cascade as discussed above with SPE and Spätzle. The authors appear to have chosen not to display the results they have gained with Enterococcus faecalis (but forgot to remove their mention at two places in the Material and Methods): it would definitely be interesting to know what the outcome of these experiments was and also to investigate the susceptibility and microbial burden of skanda mutants to representative yeast and filamentous fungal pathogens, Aspergillus fumigatus being of special interest since its proliferation is limited through melanization whereas the Toll pathway protects against secreted virulence factors (Xu et al., EMBO Reports, 2023). This series of experiments would likely take some three months and might give additional insights into Skanda function(s).

We agree with the reviewer that examining the role of Skanda in response to additional bacterial species could further help elucidate its function. However, the most robust phenotype we identified is a strong acute susceptibility to S. aureus, which is dependent on the Psh–Hayan–Skanda axis but independent of the SPE–Spätzle pathway. Because the bacterial strains suggested by the reviewers are primarily controlled by the SPE–Spätzle–Toll pathway, we did not pursue this direction further. However, in the revised version we have added survival analysis with Skanda to Candida albicans and Enterococcus faecalis (new supplement Figure 3F and G). Notably, we also observed an intermediate susceptibility to both Candida albicans and E. faecalis (see below). This indicates that Skanda is not a classical regulator of the Toll-PO cascade such as Grass, ModSP, SPE or Hayan/SPE.

In general, figure legends are not highly informative and fail to provide key information such as the number of independent experiments, whether the data are representative or pooled, which statistical test was used, e.g., qPCR experiments (the descriptions are available for the analysis of survival and melanization experiments at the end of the Mat. and Meth section). As noted above, critical information is lacking to understand microbial load graphs. It is also difficult to check statements such as: ", while psh[sk1] flies showed a reduced Toll pathway reponse". Indeed, no statistical analysis has been performed to analyze any RTqPCR data. Given the low number of experimental data points, each data point ought to be displayed and not bar graphs, for which in addition the error bars are not defined. The Material and Methods section is incomplete. It does not include a description of all the in vitro synthesized proteins used in this study nor indicate the different tags. The primary and secondary antibodies used for Western blot analysis are not reported, e.g., those that detect cleaved spätzle. This would need to be included in the Table at the beginning of this section.

In the revised version, we have addressed these points by adding statistical tests to the RT–qPCR analyses, displaying all data points, and improving the microbial load measurement. As discussed in the Material and Methods section, Table S2 provides information for all in vitro synthesized proteins used in this study, including affinity tags and the primary and secondary antibodies. On a more personal note, we first identified the striking susceptibility of Skanda/CG15046 flies more than 10 years ago, and the skanda project subsequently experienced a long period of discontinuation before we decided to reassemble and consolidate the most important findings. Unfortunately, this study did not result in a straightforward narrative with a “happy ending.” Nevertheless, we still consider this work an important step toward a better characterization of this aspect of fly immunity.

__Minor points __ Introduction: 1. The authors may want to cite Stein, Cho&Stevens, FLY, 2013 when referring to the proteolytic cascade regulating the establishment of dorso-ventral patterning.

This reference has been added

The statement "The Toll-PO SP cascade can be DIRECTLY activated at the level of Psh-Hayan, through direct cleavage of the Psh protease bait region by microbial proteases" may be slightly misleading as only subtilisin is able to do this, the other tested proteases producing an inactive cleaved Psh that needed to be secondarily activated by a couple of specific cathepsins (Issa et al., Molecular Cell, 2018).

Good point. This point has been corrected with the Issa reference added.

Results 3. The reasoning of the second paragraph is difficult to follow as the reader does not understand how the cleavage sites can be computed. It would be important to state that the recombinant proteins are tagged. It would actually be very helpful to provide a scheme of the various recombinant proteins used in the study as had been done in the Shan et al., Science Advances article.

We followed the reviewer’s good suggestions, modified the text accordingly, and added Table S2.

With respect to Western blots, many of the bands are faint, e.g., SPE after the addition of Skanda cannot be detected on a printed version of the figure. It is also difficult to determine whether the reduction in band amount is reproducible as no indications are given in this respect. It is important that the images be quantified in several independent blots so that the observed reduction can be statistically assessed. With respect to PPO1 cleavage, it would be important to also check its cleavage in vivo, which would yield higher confidence on the relevance of in vitro study to the in vivo situation.

In response to the reviewer’s suggestions, we repeated SDS-PAGE and immunoblot analysis, quantified band intensities, and performed statistical analyses for the samples shown in Fig. 3B and 3C (lower panels). The total number of blots for each representative is 3 to 4. For practical reasons, we are unable to assess PPO1 cleavage in vivo.

First sentence of the paragraph "skanda mutants are highly susceptible": the authors might also want to cite Hanson et al, eLife 2019.

We have added the Hanson reference and Ryckebusch et al 2025, which is more appropriate.

In Dudzic et al., Cell Reports, 2019, the authors did not observe any susceptibility to S. aureus with Hayan[sk3] whereas here they find an intermediate sensitivity phenotype with Hayan[sk6]. Was the former not a null allele of Hayan? With respect to the 55C Bomanin deficiency, Hanson et al., 2019 had reported a stronger phenotype than that shown in Fig. 8A, with some 75% of flies dead within three days. Which study should we trust or does this reflect variations between experiments (hence the question about the representation of survival data: are these pooled data from thre independent experiments; how much variation was there between independent experiments?).

Both Hayan mutant flies were null. We observed differences along the years with different experimenters; although the main results stand. We also tend to observe a stronger impact of psh than initially reported in response to M. luteus (Figure 5B), although this is consistent with its role in the PRR-Grass-SPE pathway. Considering all the parameters that influence survival experiments (temperature, humidity, time to form the bacterial pellet and sometimes bacterial strains) and possible cryptic infections (Nora infection), we consider these variations as expectable.

It would be interesting to measure the S. aureus bacterial load upon skanda overexpression to confirm a putative role in resistance.

This is an interesting suggestion but we did not do it because of the technical challenge that monitoring S. aureus burden represents. We have preferred to focus our attention on monitoring S. aureus in Skanda loss-of-function mutants.

UAS-skanda: besides Fig. 6B, the authors should also refer the reader to Fig. S4A.

The link to Fig S4A has been added.

Genetic dissection of the skanda-psh-hayan gene cluster: the last sentence of the paragraph does not reflect what Fig. S7B is showing: one of the double mutants and the triple mutant displayed a significant intermediate susceptibility to S. aureus.

This is in fact Ecc15 that we discussed. The reviewer is correct as the triple mutants and hayan,psh double have increased susceptibility to Ecc15.

Paragraphs Compound mutants are EXTREMELY susceptible to S. aureus. The wording is likely too ...extreme: they do not seem to die much faster than skanda simple mutants, which were HIGHLY susceptible to S. aureus, like PPO1-PPO2 double mutants.

The reviewer is correct and we have avoided to use the term ‘extremely’ in the revised version (replaced by ‘highly’ or removed).

Last paragraph: psh mutants should be compared side-by-side with psh-skanda double mutants in the same RTqPCR experiment: it is difficult to judge whether the statement of equivalent Drosomycin expression after S. aureus challenge is true given the low resolution of the figures (Fig. 6C vs. Fig. 7B). Last sentence: it would be more appropriate to mention "host defense" rather than "resistance" since the authors did not check the bacterial burdens of the compound mutants.

Experiments were done simultaneously on single and double/triple mutant but this represents kinetic with 4 times in 10 different backgrounds! We have preferred to separate the data to simplify the reading. We believe that the reader can compare the data despite display in two different panels. We have changed in all the manuscript host defense instead of resistance as following bacterial counting, we suspect that Skanda may play both in resistance and disease tolerance.

Fig. 1: the scheme is not up to date and oversimplified. It should take into account the complexity revealed in the Shan et al. Science Advances article.

We disagree on this point. This schema reflect inference done by genetics. An up-to-date figure is shown in Westlake, Hanson Lemaitre Handbook but would require a broad introduction. In the revised version, we have highlighted that this is simplified model based on genetics.

Fig. S1: numbering the amino-acids in the sequence would help follow the text from Document S1. What are the residues written in light blue? It may be worth highlighting residue E194. Of note, there is a difference between the sequence for peptide 4 as found in the sequence displayed on Fig. S1: KTDRD YV and the sequence of peptide 4 in Table S1: KTDRE YV; the presence of a potential SNP should be indicated, even though it is not making a major change in terms of charge of the peptide.

We included an asterisk at every tenth position and a numerical indicator near the end of each line to facilitate counting. Residues highlighted in cyan may represent cleavage sites of cSP48, Grass, or a trypsin-like protease released by Sf9 cells. The peptide (E194… R212) appears to undergo cleavage to generate P204LNLPLQP__R212__, which is detected in the secondary MS. The reviewer is correct on peptide 4 that we attribute to a potential SNP. This is now indicated in the legend of Figure S1.

Document S1: trypsin digestion (just before second call to Fig. S1); should it not be purified proteases instead? The text should be somewhat reworded as it is currently slightly misleading.

"In lane 8, peptide-1 through -19 were nearly undetectable". Table S1 shows that even though peptides 1, 2, 6, , 7 , and 11 are not expressed to strong enough a level to be displayed Fig. S1 lane 8 given the chosen scale, peptides 1, 2, 6, and 7 are expressed in the same range for slices 8B and 8C, whereas peptide 1 is found with just a two-fold difference in slices 8A and 8C.

Points taken. To better illustrate the differences in band intensities in the top right panel of Fig. S1, we kept the same scale for bands A and B in line 8 (as well as for bands A-C in the top left and middle panels) and used the second y-axis for band C.

Fig. S2: the effect of skanda on SP7 cleavage is not detectable when Hayan isoforms are co-incubated. The main text should be modified to take this into account. How do the authors explain that pro-MP1 levels are not different upon co-incubation with Psh or Hayan-PB with or without adding Skanda, even though the active MP1 form is detected only in the absence of Skanda? In contrast, the pro-MP1 band can be detected upon co-incubation with Skanda and Hayan-PA.

Thanks for the comments. We repeated the experiments and obtained four independent blots for each. After scanning, integrated band densities for all paired bands (i.e., with and with Skanda) were quantified using ImageJ (Fig. S2 and data not shown). In the representative blots, Skanda had little effect on SP7 activation by Hayan-PA (507/527; 96%) or Hayan-PB (15,763/15,828; ~100%), in contrast to Psh (937/7,917; 12%). However, when ratios from all blots were considered, the mean reductions were 56 ± 14% for Psh, 49 ± 19% for Hayan-PA, and 65 ± 18% for Hayan-PB. For MP1, comparison of precursor bands is less reliable because small decreases in precursor intensity are difficult to quantify; therefore, we focused on the MP1 product. MP1 levels were reduced to 58 ± 8% (Psh), 44 ± 3% (Hayan-PA), and 90 ± 30% (Hayan-PB). SPE intensity was reduced to 38 ± 12% (Psh), 43 ± 5% (Hayan-PA), and 23 ± 4% (Hayan-PB). Ser7 intensity was reduced to 9 ± 4% (Psh), 35 ± 1% (Hayan-PA), and 27 ± 13% (Hayan-PB). In general, Skanda suppressed the activation of SP7, SPE, MP1, and Ser7 by Psh, Hayan-PA, or Hayan-PB. We included the information in Fig. S2 legend.

Fig. S3B, S7A: the three genes of the locus are inducible upon immune challenge. Have any NF-kappaB binding sites been detected at the locus. It might be relevant to repeat the experiment shown in S3B and especially S7A after a challenge with M. luteus. These experiments are definitely not essential.

We did not look to the presence of NF-kB sites in their promoters but they have been shown to be induced and regulated by the Toll pathway (De Gregorio 2002). We did not extend our manuscript in this direction.

The mention 'Data not shown" is used twice. Not allReview Commons-affiliated journals accept it.

These mentions have been removed.

Reviewer #4 (Significance (Required)): A strength of this work is the dual biochemical and genetic characterization of a SPH, an endeavor that is important to understand further the function of this class of protease-like family of secreted proteins that have been so far imperfectly studied from both perspectives (Kambris et al., CB, 2006, but see Westlake Reproducibility study on BioRxiv, Jin et al. Frontiers Immunol. 2023). Unfortunately, the two approaches fail to provide an integrated view of Skanda's function(s). A weakness is that this study does not unambiguously reveal at this stage what are the functions of Skanda in the host defense against S. aureus, let alone against other pathogens controlled to some extent by the Toll pathway or melanization. The authors have not considered a possible role in disease tolerance to S. aureus. These limitations decrease the conceptual advance of this article.

In the revised version, we have considered a role of Skanda in resilience. This article will be of interest to investigators working on the innate immunity of insects. This reviewer is an expert in the Drosophila innate immunity field.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #4

Evidence, reproducibility and clarity

Summary

In this study, the authors investigate the function of Skanda, a serine protease homolog (SPH) in Drosophila innate immunity using both biochemical and genetical approaches. The reason to focus on this SPH is that it lies at the same locus as two key proteases of Drosophila immune defenses, Hayan and Persephone, all of which are induced by an immune challenge. After having modeled this SPH and shown that the three amino-acid of the serine protease catalytic triad are either mutated or poorly oriented, they report that Skanda may limit the cleavage of proteases downstream of Grass, a key event for their biochemical activation. The study of an isogenized, putatively null, mutant line failed to reveal any impact of skanda on Toll pathway activation nor on melanization, albeit a strong but not moderate overexpression somewhat inhibits the formation of a melanization scab only after "clean" but not septic injury. These results are not in keeping with the biochemical analysis: the mutant would have been expected to display an enhanced immune response. Unexpectedly, skanda mutants are as highly susceptible to a low amount of Staphylococcus aureus injection as flies deleted for the adult-expressed phenoloxidases PPO1 and PPO2, melanization playing a key role in host defense in this infection paradigm. No strong impact on the bacterial load was detected at the sole investigated time point, 24h. Because the analysis of the single skanda mutant did not unambiguously reveal its role in host defense, the authors then studied double or triple mutants of the three protease genes and found a redundant role for Skanda with Persephone for Toll pathway activation after a challenge with a nonpathogenic Gram-positive bacterium or a bacterial protease. In the case of S. aureus infection, a strong induction of the Drosomycin gene, is observed at 48h of infection in the compound mutants, which was not observed with the nonpathogenic challenges. Evidence, reproducibility and clarity

Major comments

The authors state that "These results are consistent with a role of Skanda in resistance to S. aureus". This conclusion rests on a very fragile experiment that measured the bacterial burden 24h after challenge with a low dose of S. aureus: whereas wild-type control flies exhibit a dual low and high distribution of bacterial loads, skanda flies exhibit only the higher values. However, the bacterial load in skanda appears to be as high in persephone mutant flies that are much less sensitive to S. aureus than skanda flies. This makes it highly unlikely that the high susceptibility of skanda to S. aureus is due solely to resistance. The problem is compounded by the poor description of the experiment: it is not stated anywhere how many times the experiment has been performed, whether pooled data are shown, what each data point represents, pooled or single flies. A fine-grained time course with more biological samples would definitely be needed to convince the reader of a (limited) role in resistance. The authors do not consider the alternative, but not exclusive, possibility that skanda plays also a role in disease tolerance. The determination of the bacterial load upon death of single flies may provide some clues about this alternative function (Duneau et al., eLife, 2017). Another approach might be to determine whether the bacterial supernatant is toxic and whether skanda might protect from this toxicity. As Bomanins play a role in the host defense against S. aureus (this study, but see also Hanson et al., eLife 2019 in which the 55C deficiency susceptibility phenotype was stronger) and given the role of Bomanins in host defense against Gram-positive bacteria or fungal infections both in resistance and disease tolerance (e.g., Clemmons et al. PLoS Pathogens 2015, Lindsay et al., J. Innate Immun, 2018, Xu et al., EMBO Reports 2023, Lou et al., BioRxiv, 2025) and that BomS1 has an optimal Dorsal-related Immune Factor Binding site (Busse et al. EMBO J. , 2007), it may be useful to monitor the expression of several Bom genes in complement to that of the expression of Drosomycin, especially after S. aureus challenge. Furthermore, BomT1 is the only peptide that appears to play a role in resistance against Gram-positive bacteria, namely against E. faecalis. This series of qPCR experiments is rapid to make, provided the authors have kept the cDNAs of their samples. In the Discussion, the authors speculate "that Skanda acts at the level of Persephone-Hayan to allow Hayan to activate the Toll pathway. Skanda would skew the activity of the Persephone-Hayan platform to induce Toll signaling and resistance to S. aureus rather than cuticular melanization". This model does not fit with the fact that SPE is only moderately susceptible to S. aureus (Dudzic et al., 2019) and that spätzle mutant flies are either not sensitive at all (Dudzic et al., 2019) or moderately sensitive to it (Hanson et al., eLife, 2019) (see also below). Whether it may apply to host defense against other pathogens remains to be determined. To better understand the function of skanda, considering only S. aureus may be limiting as this bacterium is fundamentally not susceptible to the canonical Toll intracellular signaling cascade (e.g., Bischoff et al, Nat Immunol, 2004, Dudzic et al, Cell Reports, 2019) and to the final part of the Toll-activation proteolytic cascade as discussed above with SPE and Spätzle. The authors appear to have chosen not to display the results they have gained with Enterococcus faecalis (but forgot to remove their mention at two places in the Material and Methods): it would definitely be interesting to know what the outcome of these experiments was and also to investigate the susceptibility and microbial burden of skanda mutants to representative yeast and filamentous fungal pathogens, Aspergillus fumigatus being of special interest since its proliferation is limited through melanization whereas the Toll pathway protects against secreted virulence factors (Xu et al., EMBO Reports, 2023). This series of experiments would likely take some three months and might give additional insights into Skanda function(s). In general, figure legends are not highly informative and fail to provide key information such as the number of independent experiments, whether the data are representative or pooled, which statistical test was used, e.g., qPCR experiments (the descriptions are available for the analysis of survival and melanization experiments at the end of the Mat. and Meth section). As noted above, critical information is lacking to understand microbial load graphs. It is also difficult to check statements such as: ", while psh[sk1] flies showed a reduced Toll pathway reponse". Indeed, no statistical analysis has been performed to analyze any RTqPCR data. Given the low number of experimental data points, each data point ought to be displayed and not bar graphs, for which in addition the error bars are not defined. The Material and Methods section is incomplete. It does not include a description of all the in vitro synthesized proteins used in this study nor indicate the different tags. The primary and secondary antibodies used for Western blot analysis are not reported, e.g., those that detect cleaved spätzle. This would need to be included in the Table at the beginning of this section.

Minor points

Introduction:

1. The authors may want to cite Stein, Cho&Stevens, FLY, 2013 when referring to the proteolytic cascade regulating the establishment of dorso-ventral patterning.
2. The statement "The Toll-PO SP cascade can be DIRECTLY activated at the level of Psh-Hayan, through direct cleavage of the Psh protease bait region by microbial proteases" may be slightly misleading as only subtilisin is able to do this, the other tested proteases producing an inactive cleaved Psh that needed to be secondarily activated by a couple of specific cathepsins (Issa et al., Molecular Cell, 2018). Results
3. The reasoning of the second paragraph is difficult to follow as the reader does not understand how the cleavage sites can be computed. It would be important to state that the recombinant proteins are tagged. It would actually be very helpful to provide a scheme of the various recombinant proteins used in the study as had been done in the Shan et al., Science Advances article.
4. With respect to Western blots, many of the bands are faint, e.g., SPE after the addition of Skanda cannot be detected on a printed version of the figure. It is also difficult to determine whether the reduction in band amount is reproducible as no indications are given in this respect. It is important that the images be quantified in several independent blots so that the observed reduction can be statistically assessed. With respect to PPO1 cleavage, it would be important to also check its cleavage in vivo, which would yield higher confidence on the relevance of in vitro study to the in vivo situation.
5. First sentence of the paragraph "skanda mutants are highly susceptible": the authors might also want to cite Hanson et al, eLife 2019.
6. In Dudzic et al., Cell Reports, 2019, the authors did not observe any susceptibility to S. aureus with Hayan[sk3] whereas here they find an intermediate sensitivity phenotype with Hayan[sk6]. Was the former not a null allele of Hayan? With respect to the 55C Bomanin deficiency, Hanson et al., 2019 had reported a stronger phenotype than that shown in Fig. 8A, with some 75% of flies dead within three days. Which study should we trust or does this reflect variations between experiments (hence the question about the representation of survival data: are these pooled data from thre independent experiments; how much variation was there between independent experiments?).
7. It would be interesting to measure the S. aureus bacterial load upon skanda overexpression to confirm a putative role in resistance.
8. UAS-skanda: besides Fig. 6B, the authors should also refer the reader to Fig. S4A.
9. Genetic dissection of the skanda-psh-hayan gene cluster: the last sentence of the paragraph does not reflect what Fig. S7B is showing: one of the double mutants and the triple mutant displayed a significant intermediate susceptibility to S. aureus.
10. Paragraphs Compound mutants are EXTREMELY susceptible to S. aureus. The wording is likely too ...extreme: they do not seem to die much faster than skanda simple mutants, which were HIGHLY susceptible to S. aureus, like PPO1-PPO2 double mutants.
11. Last paragraph: psh mutants should be compared side-by-side with psh-skanda double mutants in the same RTqPCR experiment: it is difficult to judge whether the statement of equivalent Drosomycin expression after S. aureus challenge is true given the low resolution of the figures (Fig. 6C vs. Fig. 7B). Last sentence: it would be more appropriate to mention "host defense" rather than "resistance" since the authors did not check the bacterial burdens of the compound mutants.
12. Fig. 1: the scheme is not up to date and oversimplified. It should take into account the complexity revealed in the Shan et al. Science Advances article.
13. Fig. S1: numbering the amino-acids in the sequence would help follow the text from Document S1. What are the residues written in light blue? It may be worth highlighting residue E 194. Of note, there is a difference between the sequence for peptide 4 as found in the sequence displayed on Fig. S1: KTDRD YV and the sequence of peptide 4 in Table S1: KTDRE YV; the presence of a potential SNP should be indicated, even though it is not making a major change in terms of charge of the peptide.
14. Document S1: trypsin digestion (just before second call to Fig. S1); should it not be purified proteases instead? The text should be somewhat reworded as it is currently slightly misleading " In lane 8, peptide-1 through -19 were nearly undetectable". Table S1 shows that even though peptides 1, 2, 6, , 7 , and 11 are not expressed to strong enough a level to be displayed Fig. S1 lane 8 given the chosen scale, peptides 1, 2, 6, and 7 are expressed in the same range for slices 8B and 8C, whereas peptide 1 is found with just a two-fold difference in slices 8A and 8C.
15. Fig. S2: the effect of skanda on SP7 cleavage is not detectable when Hayan isoforms are co-incubated. The main text should be modified to take this into account. How do the authors explain that pro-MP1 levels are not different upon co-incubation with Psh or Hayan-PB with or without adding Skanda, even though the active MP1 form is detected only in the absence of Skanda? In contrast, the pro-MP1 band can be detected upon co-incubation with Skanda and Hayan-PA.
16. Fig. S3B, S7A: the three genes of the locus are inducible upon immune challenge. Have any NF-kappaB binding sites been detected at the locus. It might be relevant to repeat the experiment shown in S3B and especially S7A after a challenge with M. luteus. These experiments are definitely not essential.
17. The mention 'Data not shown" is used twice. Not all Review Commons-affiliated journals accept it.

Significance

A strength of this work is the dual biochemical and genetic characterization of a SPH, an endeavor that is important to understand further the function of this class of protease-like family of secreted proteins that have been so far imperfectly studied from both perspectives (Kambris et al., CB, 2006, but see Westlake Reproducibility study on BioRxiv, Jin et al. Frontiers Immunol. 2023). Unfortunately, the two approaches fail to provide an integrated view of Skanda's function(s). A weakness is that this study does not unambiguously reveal at this stage what are the functions of Skanda in the host defense against S. aureus, let alone against other pathogens controlled to some extent by the Toll pathway or melanization. The authors have not considered a possible role in disease tolerance to S. aureus. These limitations decrease the conceptual advance of this article.

This article will be of interest to investigators working on the innate immunity of insects. This reviewer is an expert in the Drosophila innate immunity field.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Serine protease cascades are central for activation of immune responses in insects. In Drosophila melanogaster, Toll signaling pathway has been quite extensively studied, and several serine proteases, serpins and serine protease homologs (SPH) with functions in Toll activation have been identified. In this work, the authors characterize a new component of this system, a SPH which they name Skanda. Skanda seems to have multiple roles/points of action, on one hand participating in the regulation of Toll together with the established serine protease in the Toll activation, Psh, and on the other hand controlling the response to a systemic S. aureus infection, via not yet fully specified mechanism.

Major comments:

Key conclusions made in this work are convincing, and backed up by the data presented. The data and methods are presented in a way that allows reproduction of the experiment. The number of individuals used especially in the infection experiment (20 male flies per a replicate) is on the lower side, but the experiments are adequately replicated and the effects seen are clear.

While this work contributes to our understanding of the regulatory mechanisms governing Toll signaling, at times the authors' reasoning is difficult to follow. I recognize that this is a complex topic, with multiple upstream branches activating Toll signaling, and the authors do consider various mechanisms that could explain their findings. However, the manuscript would benefit from additional clarification, perhaps through a schematic model illustrating the proposed effects of Skanda, to help readers position Skanda within the broader context of Toll signaling.

Statistical analyses for the Drs expression experiments are lacking.

Minor comments:

The authors could explain what type of cells the sf9 cells are and why they decided to use them.

Band intensities could be measured and plotted for the immunoblots. The immunoblot methods should be fully described in the Materials and methods section.

Protein levels of Skanda in the Skanda mutant could be shown as the mRNA levels remain relatively high (Sup. Fig 3B). If this is not possible, could the authors comment on the remaining expression of Skanda in the Skanda mutants?

Under the heading "Loss of skanda does not further enhance the cuticular melanization defects caused by the loss of Hayan or psh" the text should refer to figure 5D not 5B.

Figure 6C shows that Drs expression is higher in the Skanda mutant than in controls at 32 h post S. aureus infection (although this has not been statistically tested). The authors don't mention this result in the manuscript, but to me it fits with the idea of Skanda acting as a negative regulator (the effect of which is accumulating and seen only late after infection). Could the authors comment on this?

Under the heading "Psh and skanda redundantly regulate Toll signaling", the comparison should likely be between Figures 7A-7B and 5B-C (rather than 5A). When examining the effects of single versus double mutants on Drs expression, the Psh-Skanda double mutant clearly reduces Drs more than the Psh single mutant. However, in the context of microbial proteases, the pattern appears different: there is virtually no difference at 6 hours, while at 48 hours there may be a slight decrease in Drs expression in the double mutant compared to the Psh single mutant, although this difference would likely not reach statistical significance if tested. I don't know what this could mean, but I'd like to hear the authors' take on this.

Referee cross-commenting

I also agree with the comments and points raised by the other reviewers.

Significance

Research on the Drosophila immune response has significantly advanced our understanding of (innate) immune responses, both generally and in an evolutionary context. Despite over three decades of study, this work demonstrates that there are aspects of Toll signaling that remain unresolved. The authors identify a novel regulator of the Toll pathway and begin to elucidate its functions. Equally important, their findings underscore the complexity and context-dependency of the regulatory events that shape immune responses.

My fields of expertise are Drosophila melanogaster, innate immunity, cell-mediated immunity.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this work the authors identify the SPH skanda as an important player in Drosophila resistance to S. aureus infections independent of Toll and classical melanization. The authors conducted rigorous in vitro assays using recombinant proteins of various SPs in the Drosophila Toll-PO cascade to show that skanda negatively regulates activation cleavage of SPs at the level of and downstream of Psh and hayan, two key SPs that converge on Toll pathway activation with the latter playing a central role in cuticular melanization. In parallel, genetic analysis using mutant flies showed that skanda does not negatively regulate Toll pathway nor melanization. Only skanda over expression in vivo led to a reduction in S. aureus melanization which, in my opinion, is most likely due to the artificial increase in the in vivo concentration of the protein rather than an indication of a potential true function. Altogether this an interesting work as it shows the discrepancies between the biochemical and genetic approaches when it comes to dissecting the insect SP cascades regulating melanization and Toll as highlighted by the authors themselves in the discussion section. All experimental work is well controlled, methodology is robust and results are adequately discussed. I have some comments concerning few experiments and interpretations that in my opinion warrant further discussion.

Major comments:

1. It seems that SP48 and Grass can redundantly cleave Skanda although the later cleaves more strongly. (Fig 3B) Can other downstream SPs cleave skanda? Can ModSp alone cleave skanda? (ModSP + skanda lane was absent for Fig 3B). It is important to test these possibilities as the in vitro system may be quite relaxed as to the specificity of these cleavage events and may not reflect what happens in vivo. In fact it has been shown in Anopheles gambiae that SPH can be redundantly cleaved by multiple SP in the protease cascade. Although these are cascades with certain hierarchy, information can still flow in more than one direction along the different branches of these cascades.
2. In Fig 4B and 4C the bands of active forms should be quantified from at least 3 immunoblots for robust results especially in Fig 4C where the differences are minimal.
3. It is not clear to me why skanda should have a specific role in resisting S. aureus infections despite that S. aureus is not a natural pathogen of Drosophila? Has other Gram-positive and Gram-negative bacteria been tested?
4. In Fig 6E more points should be collected for statistical power. It is also better to show these data that are not normally distributed in violin charts or boxes and whiskers which give a better indication as to which quartile the bulk of the data belongs.

Minor comments:

1. In Figures 3 and 4, It would be easier to follow the cleavage events if a schematic drawing is provided showing the sequence of activation cleavage events of the tested SPs
2. The fact that PPO1/PPO2 depleted flies exhibit increased Drs expression could be due to increased bacterial proliferation in this mutant background that trigger increased Toll stimulation, rather than a negative feedback mechanism. This increased proliferation is shown in Fig 6E.
3. In Fig 6E more points should be collected for statistical power. It is also better to show these data that are not normally distributed in violin charts or boxes and whiskers which give a better indication as to which quartile the bulk of the data belongs.
4. A phenotype for skanda in melanization was observed only in over-expression assays which may artificially alter molecular interactions in the cascade.
5. Page 10 last paragraph "peak expression at 32 hrs or 48 hrs as shown on the figure?"
6. The differences in Drs expression levels in Hayan-pshDef and psh-skandaDef double mutant flies infected with M. luteus and S. aureus is surprising. I wonder whether the observed differences are due to biochemical differences in the microbial surfaces to which these cascades are recruited.
7. There are several typos in the manuscript

Significance

The main strength of this work is that it combines biochemistry and genetics in a strong genetic model to characterize the biochemical interactions between SPH and Sp in clip cascades and relate the relevant interactions observed in vitro with potential in vivo functions. This is the first time that such a rigorous combined approach was adopted to the study of these cascades. The results obtained also show the advantages and limitations of each approach. As such i believe this study will be of interest to a broad audience in the field of insect immunity.

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Referee #1

Evidence, reproducibility and clarity

In the manuscript entitled "The serine protease homolog Skanda modulates Toll-phenoloxidase-mediated immunity in Drosophila," Vasanth et al characterize in detail a previously unstudied component of the insect immune response using first biochemical and then in vivo methods. Using proteins overexpressed and purified from insect cells, the authors provide evidence that Skanda could be a negative regulator of the SP cascade, impacting cleavage of proHayan and proPsh, and consequently Toll pathway and PPO1 activation. This work reaches further by transposing these findings into the D. melanogaster in vivo model. Here, however, the picture becomes more confusing as Skanda at native levels does not appear to regulate either the Toll pathway or the melanization cascade. Only one strong phenotype was identified in that decreased expression of Skanda increased susceptibility to S. aureus infection while increased expression decreased susceptibility. The mechanism for this remains unclear. To their credit, the authors carry out an in-depth analysis to rule out all the obvious possibilities. In the discussion, the authors explore the basis of discrepancies between their biochemical and genetic findings. We would suggest that an additional one to consider is differing roles or behaviors of Skanda in the microenvironments of the local site of injury (where S. aureus may be contained when it is tolerated) and the hemolymph. In summary, this is a valuable analysis of the innate immune component Skanda whose role has become somewhat clearer through these studies, but still remains obscure.

Major Comments

• To assess bimodal distribution of bacterial loads within single flies in Fig 6E, authors should either: increase the sample size to allow for proper statistical assessment of different distributions among genotypes, specifically between w1118 and skanda_d107; or, provide a modelling framework for statistical testing. Otherwise, the present results seem insufficient to conclude that Skanda is playing a role in resistance to S. aureus.
• Another way to assess a role for tolerance in the Skanda mutant would be to measure BLUDs (https://doi.org/10.7554/eLife.28298 ) and/or transcription of CrebA (https://doi.org/10.1371/journal.ppat.1006847).
• The error bars on qRT-PCR datasets are large, the data points are not shown so we do not know how many replicates were included in the graphs (Fig 5 B and C, Fig 6C, Fig 7 A and B, and Fig 8B). Bar plots are not the most faithful reproduction of biological datasets, as they can hinder significant information regarding datapoints distribution and variation (Beyond Bar and Line Graphs: Time for a New Data Presentation Paradigm | PLOS Biology). We advise that, particularly in the case of datasets such as qRT-PCR, the final values of fold change are represented with individual dots, with the mean value clearly represented, whether with or without the additional bar graph. Furthermore, no statistical tests were applied to determine significance. Data points should be shown and appropriate statistical tests should be applied. The number of biological replicates should be included in the analysis and the statistical test applied should be noted in the figure legends.
• Although there are claims of Skanda conferring resistance to S. aureus infection, only Drs levels are tested. These conclusions could be strengthened by assessing expression levels of additional AMPs.

Minor Comments

• Parag. 1: (data not shown) should be removed and if possible AlphaFold prediction of skanda conformation added. Alternatively, remove sentence.
• Parg. 3: 1000 mL? why not 1L?
• Parag. 5: , in last sentence that should be .
• Parag. 6: "a role at the same position..." does not convey the correct message< replace with equivalent?
• Figure axes (5D, 5E, 6D, etc...) of melanization assays are wrongly named "% melanisation", with "s"
• Parag. 21: compound mutants (if correctly interpreted as dataset presented in Fig. 8B) were tested at 6h, 24h and 48h, and not 32h, as written in the text
• Results section "skanda is not mandatory for the activation of the Toll pathway" adopts a literal translation which would probably be better phrased as "is not essential"
• Discussion parag. 2: "Skanda exhibits..."
• Discussion last parag: "..., but also underlies..."
• It has been evidenced that

Additional comments:

• The sentence on page 2 beginning with "Upon binding, these PRRs..." is very long and difficult to follow. This should be rewritten.
• In many places in the manuscript bacterial "dose" is used in place of bacterial burden. The dose is the amount of a substance or bacterium given to the animal.
• Page 11: Skanda is described as a placeholder when I think a (competitive) inhibitor would be more appropriate.

Referee cross-commenting

I agree with the comments of the other reviewers.

Significance

Strengths: The authors take a multi-disciplinary biochemical and in vivo approach to understand the molecular interactions among SPs and SPHs and thereby uncover the role of the protein Skanda that might otherwise not have been appreciated. They have made extensive use of novel transgenic fly lines, generated in the context of this study, and have thoroughly tested their specificity and cis-acting potential. These will provide a resource to the field. In addition to the new description of Skanda, these findings strengthen previous knowledge regarding systemic infections with different bacteria (M. luteus, S. aureus) and reproduce the known redundancies of Psh and Hayan modes of action. Moreover, this research is relevant for the expansion of basic knowledge on innate immunity, particularly in the field of insect-pathogen interactions, making use of S. frugiperda cell lines and D. melanogaster adults and larvae. Although not at the focus of this work, the evolutionary conserved nature of these aspects of innate immunity across these two distant species enhance the importance of these findings.

Weaknesses: Some assays do not include enough biological replicates and others do not have enough information on how many biological replicates were performed. Therefore, the conclusions drawn are difficult to assess. Lack of statistical analysis on the qPCR experiments complicates the interpretation of results.

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Reply to the reviewers

We thank the reviewers for their insightful comments.Please find below a point-by-point response.

• As the authors acknowledge in the section at the end of the discussion (Limitations of this study) it is not established that LIN-15A has a cell-autonomous function in Y-to-PDA transdifferentiation. Given that LIN-15A has a cell non-autonomous function in vulval development (Herman and Hedgecock, 1990) it is possible that its function here could also be. The authors have used an egl-5 promoter to rescue lin-15A through expression in rectal cells; however, all these cells are in a neighborhood. The lack of a promoter that is specfic for Y has impeded answering this question (a standard genetic mosaic analysis would be problematic because of the incomplete penetrance of the mutation). Although this issue is addressed in the section at the end of the Discussion, I think most readers would like to see this acknowledged earlier in the presentation, perhaps after describing the egl-5 rescue experiment.

We thank the reviewer for this comment and agree that our data do not formally demonstrate a Y-cell autonomous role for LIN-15A during Y-to-PDA transdifferentiation, as we discussed in the manuscript. As suggested, we have modified the Results section immediately after the egl-5 rescue experiment to explicitly acknowledge this limitation early-on (see p8, l168-170) and retained the discussion in the "Limitations of the study" section.

• The experiment shown in Figure S1B is unconvincing. To show that they are detecting a LIN-15A-LIN-56 heterodimer, the authors need to show that antibody tags to both proteins detect the band. Mass spectrometry or biochemical purifications would also be helpful. As it is, they show the protein(s) detected depend genetically on lin-56 and lin-15A. It was also unclear what the other bands were in the mutant backgrounds

We agree that the experiment shown in Figure S1B does not provide sufficient evidence to conclusively demonstrate the existence of a LIN-15A-LIN-56 heterodimer. While the detected species depend genetically on both lin-15A and lin-56, we agree that additional controls, such as detection through reciprocal tagging, biochemical purification, or mass spectrometry, would be required to firmly establish the molecular nature of the complex and to interpret the additional bands observed in the mutant backgrounds. As this experiment is not essential to the conclusions of the manuscript, we have removed Figure S1B and the associated statements from the revised version.

• Lines 207-212. The authors are making an argument that LIN-15A and LIN-56 function as "Licensers" not "Drivers" because they are not strictly required but appear to facilitate the process. Could it be that LIN-15A and LIN-56 function as "Drivers" but that in their absence the fidelity of the process is compromise? There are many ways that genetic redundancy can be manifested at biochemical levels and the concern is that there are other interpretations of the data. In this regard, the authors should consider rewriting the Abstract to focus on the genetic results underpinning the work. The current version or the Abstract focuses on an interpretation of the data, not the data itself.

We thank the reviewer for this thoughtful comment. We agree that the Driver/Licenser terminology represents an interpretation of the genetic data and that additional activities acting alongside LIN-15A may exist: lin-15A alleles used in this study correspond to null alleles - that is total loss of lin-15A activity - and approximately half of the animals still successfully undergo Y-to-PDA transdifferentiation in these null mutants. Thus, lin-15A activity is either not strictly required to facilitate the initiation of the process (e.g., threshold model). Or this may point to other factors (than lin-56) able to somewhat compensate for lin-15A absence and that remain to be identified. In line with this interpretation, while we retrieved several alleles for some of the genes identified in our forward genetic screen (in which lin-15A was identified), that screen may not have been saturated. Note that both these hypotheses are compatible with a role for LIN-15A as a licenser of the initiation of the process.

Importantly, our distinction between "Drivers" and "Licensers" is not solely based on the incomplete penetrance of lin-15A and lin-56 null mutants. First, the distinction reflects the different biological roles inferred from our genetic analyses. The previously characterized factors CEH-6, SOX-2, SEM-4, EGL-27, EGL-5 and HLH-16 are conserved plasticity factors that promote the initiation of transdifferentiation. Their loss results in a complete, or near-complete, failure of Y-to-PDA initiation, and they act within a common plasticity-promoting network. By contrast, LIN-15A and LIN-56 define a genetically distinct pathway. They are neither upstream nor downstream of the Driver cassette, and display additive interactions with partial Driver mutants. Second, loss of LIN-15A does not affect the fidelity or outcome of transdifferentiation. In all defective animals examined, the Y cell retains its normal position, morphology and rectal markers, indicating a failure to initiate the process rather than the production of an aberrant cell type. Third, the fact that a core Driver set is involved in different transdifferentiation events (ie Y-to-PDA and K-to-DVB) but not lin-15A or lin-56 further argues against LIN-15A acting as a Driver. And finally, and most importantly, lin-15A and lin-56 antagonize SynMuvB chromatin regulators known to safeguard differentiated cell identities, while the Drivers do not. In fact, the transdifferentiation process is mostly restored in some lin-15A; SynMuvB double null mutants, suggesting that LIN-15A main function is to block these genes activities. We therefore favor a model in which the Drivers cassette triggers transdifferentiation, whereas LIN-15A and LIN-56 facilitate the process by alleviating inhibitory constraints imposed by identity-safeguarding mechanisms. We have reformulated this in the manuscript in order to make it clearer and also clarified how we define Drivers and Licencers activitities (see p10, l211-217; p13, l283-289 and p14 l312-315). We have further reformulated the abstract to integrate the reviewer's comments.

Minor Points

__ 1. Line 279. The authors state that "LIN-15A becomes dispensable when member of the SynMuvB factors are absent." This statement is not completely accurate as the suppression is incomplete.__

• Addressed, the statement has been reworded in the revised version (see p13, l285-286)

2. Line 294. The number in Tagble S1 is 58.8% not 65%

• Addressed, thank you for spotting this, Table S1 was correct, and the typo in the Results section was corrected (see p15, l319).

3__. Lines 300-301. I couldn't find the data for lin-40. __

__- __The data can be found in Fig. 3Bii (which we have more clearly indicated in the text) and SI table 1.

__. Line 363. Should be "represses cell cycle genes." __

- Addressed

__5. Line 862. AJM-1 is not a tight junction component. AJM-1 is best described as a component of apical junctions. __

__- __Absolutely ! Addressed

Reviewer 2

• The conclusions derived from the presented data are generally comprehensible but should be phrased more carefully to grant full legitimacy. The reason is that the central mechanistic claim that LIN-15A licenses Td by antagonizing most of the SynMuvBs chromatin factors, including DREAM, rests on whole-animal ChIP-seq that cannot resolve the Y cell. The authors acknowledge that "it was not technically feasible to purify sufficient Y cells for analysis" and therefore use synchronized unstarved L1 whole-animal lysates. This is certainly legitimate, but demands more tact when using such a conclusion as the headline claim.

We thank the reviewer for this important comment and agree that the mechanistic conclusions drawn from the ChIP-seq data should be presented more cautiously. As noted by the referee and in the manuscript, it was not technically feasible to isolate sufficient Y cells for chromatin profiling and therefore all ChIP-seq experiments were performed on synchronized whole-animal L1 populations. We agree that these experiments cannot directly establish the mechanism operating in the Y cell. Rather, our genetic analyses demonstrate that LIN-15A antagonizes identity-safeguarding SynMuvB factors during Y-to-PDA transdifferentiation. The ChIP-seq data provide an additional and independent line of evidence suggesting that this antagonism may involve modulation of DREAM chromatin occupancy. We have rephrased to state this more clearly. We thus have revised the Abstract (see p2, l7), Introduction (p6, L110-112), Results (see p18-19, l405-420) and Discussion (see p23-24, l523-542 and p25 l566-575) to more clearly separate the conclusions supported by the genetic analyses from the mechanistic interpretation suggested by the ChIP-seq data. We further clarify that the relevance of this mechanism to the Y cell remains a hypothesis consistent with, but not directly demonstrated by, the available data.

• Also, in the context of the ChIP-Seq experiments, it is understandable that it could not be conducted in a cell-specific manner, but two duplicates in some ChIP-Seq experiments (as stated in the material and methods) is below standard.

We thank the reviewer for this comment and agree that two biological replicates represent the lower end of what is generally desirable for ChIP-seq analyses. To clarify, more biological samples were initially generated than are represented in the final analysis. In total, five independent biological preparations were performed for each genotype. However, the experimental design imposed substantial technical constraints. Because the experiments required tightly synchronized fed L1 populations (ie, not using a starvation step), standard synchronization procedures could not be used and animals instead had to be collected through successive hatch pulses, resulting in considerably lower yields. Combined with the mutant backgrounds analyzed, this led to variable ChIP-seq quality across preparations. To ensure robustness, we restricted the final analyses to datasets that passed all predefined quality-control criteria. As a result, some conditions were ultimately represented by only two high-quality biological replicates. We agree that this limitation should be made more explicit and have added this information in the Materials and Methods section (p35 l774-779). Despite the reduced number of replicates retained for some conditions, the genome-wide binding patterns observed for LIN-15B and LIN-35 in wild-type animals closely recapitulated those reported previously by the Ahringer laboratory (Gal et al., 2022; SI table 2), supporting the overall robustness and biological validity of the datasets used in this study. More generally, we have also tempered the interpretation of the ChIP-seq experiments throughout the manuscript. We view these data as supportive evidence consistent with a chromatin-level mechanism, rather than as definitive mechanistic proof, and have revised the text to reflect this more clearly.

• Regarding the genetic interactions with met-2: as MET-2 works in concert with other SET domain proteins, such as SET-25, and also HPL-2, is there a possibility they may be implicated?

We also considered the possibility that the interaction observed with MET-2 could reflect a broader involvement of the H3K9 methylation machinery, given the well-established functional relationships between MET-2 and other SET domain proteins. To address this possibility, we tested whether SET-25 and SET-32 losses suppressed the lin-15A phenotype. In contrast to met-2 loss-of-function, neither set-25 nor set-32 mutations modified the transdifferentiation defects observed in lin-15A mutants. These observations suggest that the interaction is not a general property of all MET-2-associated SET domain proteins and may instead reflect a more specific role for MET-2 in this context, although we have not tested triple mutant combinations, such as met-2; set-25; lin-15A or met-2; set-32; lin-15A, and therefore cannot exclude additional contributions from these factors. However, based on the available genetic evidence, our data support a model in which the phenotype is more closely linked to the SynMuvB-centered identity-safeguarding machinery than to the canonical MET-2/SET pathways. We now mention these negative results p14, l290-295 and in the discussion (p22, l510-511) of the revised manuscript. HPL-2 itself was tested alongside the other SynMuvBs, as previously reported to be a SynMuvB (Fig. 4Ci). Loss of HPL-2 had the same effect than loss of the other SynMuvBs. Together these data further suggest that the canonical SynMuvB machinery is at play, including MET-2, but not a generic requirement for all H3K9 methyltransferases, and instead points toward a more specific role of MET-2 within the SynMuvB.

• The fact that Y-to-PDA in males (which involves a cell division) shows the same lin-15A dependence as in hermaphrodites is informative and a bit underplayed. Since this argues against a cell-cycle-coupled mechanism (an important aspect of the reprogramming field) for LIN-15A, it is worth elaborating on this in the discussion.

We thank the reviewer for this insightful comment and agree that this result deserves further discussion. One of our initial hypotheses was indeed that LIN-15A might be specifically required in transdifferentiation events that occur without a cell division. Cell division and DNA replication have long been proposed to facilitate cellular reprogramming by promoting the dilution or resetting of identity-safeguarding mechanisms. In this context, it was conceivable that LIN-15A and LIN-56 might compensate for the absence of such a process during hermaphrodite Y-to-PDA transdifferentiation. However, our data do not support this model. We found that LIN-15A and LIN-56 are similarly required for Y-to-PDA transdifferentiation in males, despite the fact that this event occurs through a cell division. Conversely, neither factor is required for the K-to-DVB transdifferentiation, which also occurs in the rectum at a similar developmental stage and likewise involves a cell division. Together, these observations argue that the requirement for LIN-15A is not determined by the presence or absence of cell division. Rather, they suggest that the Licensers activity is context-dependent and linked to specific cellular identities. We agree that this point also strengthens the notion that Licensers are distinct from Driver factors, which function in both Y-to-PDA and K-to-DVB transdifferentiation. We have therefore modified the discussion (see p20 l441-443 and l455-480).

Minor: __ - in the legend of Figure 1 and other places, it should be "Fisher's exact" instead of "Fisher exact" - line 31; exhibits instead of exhibit - line 85: results instead of result - line 228: involvement instead of involvment - line 293: "of missing" in loss of lin-36 had no effect while loss ... lin-53 further - lines 297 - 299: check sentence; reads not correct - line 395: "with an increase" - line 484: "with regard"__

• All points were all addressed in the revised version.

  Reviewer 3

Based on the observation that LIN-15A does not affect SynMuvB expression in Y (figure S4), the authors conclude that antagonism of the SynMuvBs by LIN-15A is not likely mediated by a negative control of their expression, but rather by impacting their activity. However, as suggested by the authors, antagonistic functions on the same targe genes is also a possibility. The classical approach to test this would be through expression profiling. I understand that RNA-seq on single Y cells cannot be carried out for technical reasons and that bulk RNA-seq would not be informative. Importantly, the same reasoning applies to the ChIP-seq data that is presented in support for common regulatory functions of a subset of synMuvs and LIN-15A (Figure 6 and S6), which was obtained from whole animals. The relevance of these results to the Y to PDA Td process is therefore extremely limited, as the claim that LIN-15A restricts lin-35/DREAM binding on a subset of target genes is based on a reported decrease in DREAM binding in lin-15 mutants in bulk chromatin. This is especially true as both DREAM and LIN-15A are widely expressed proteins.

We agree with the general limitation highlighted here. As the reviewer notes, neither expression profiling nor chromatin profiling can currently be performed specifically in the Y cell due to the extremely small number of cells involved and the lack of suitable purification strategies. Consequently, the ChIP-seq experiments were performed on synchronized - and fed - whole-animal L1 populations. These data do not directly establish the mechanism operating during Y-to-PDA transdifferentiation. Rather, our conclusions are based on two distinct observations. First, the genetic analyses demonstrate an antagonistic relationship between LIN-15A and multiple SynMuvB factors during transdifferentiation. Second, the ChIP-seq experiments provide independent evidence that LIN-15A can influence DREAM chromatin occupancy at the organismal level. We interpreted these observations together as supporting a model in which the genetic antagonism may involve modulation of SynMuvB/DREAM chromatin activity. We agree, however, that the ChIP-seq data do not demonstrate that these chromatin changes occur in the Y cell itself, nor do they identify the relevant target genes involved in Y-to-PDA transdifferentiation. We have therefore revised the manuscript to more clearly distinguish between the conclusions supported directly by the genetic analyses and the mechanistic interpretation suggested by the ChIP-seq experiments. Throughout the revised version, and in the discussion in particular, we present the chromatin-level model as a hypothesis consistent with the available data rather than as a demonstrated mechanism operating in Y (see p2, l7 ; p6, l110-112 ; p18-19, l405-420 ; p23-24, l523-542 and p25 l566-575).

In addition there are specific issues with Figure 6, which is mislabeled: upregulated and downregulated applies to gene expression, while the numbers refer to binding peaks. Why are some numbers in red (not mentioned in the legend). An example of the corresponding genome browser tracks should be shown in supplementary. Was a spike-in used to normalize data?

We thank the reviewer for these helpful suggestions. We agree that the terminology "upregulated" and "downregulated" is potentially confusing in the context of ChIP-seq peaks. In the revised manuscript, we have replaced these terms with "up-bound" and "down-bound" in Figure 6. Regarding the red numbers, these were originally highlighted to emphasise the relatively small number of peaks showing decreased occupancy in lin-15A mutants compared to the other genotypes analyzed. However, as this information was not explained in the legend and may be confusing to readers, we have removed the color coding in the revised figure. Following the reviewer's suggestion, we have also added representative genome browser tracks in the Figure S6E to illustrate the binding changes described in Figure 6. No exogenous spike-in controls were used in these experiments. The ChIP-seq workflow was intentionally designed to closely follow that used by Gal et al. (2022), to allow direct comparison with the published LIN-15B and LIN-35 datasets. However, several observations suggest that the patterns reported here are unlikely to result from normalization artifacts alone. First, the genome-wide binding profiles obtained for LIN-15B and LIN-35 in wild-type animals closely recapitulate those reported previously, providing an independent validation of the overall quality of the datasets. In addition, the different mutant backgrounds exhibit distinct peak gain/loss profiles rather than a common directional shift that would be expected from a systematic technical bias. Nevertheless, we acknowledge the absence of spike-in controls as a limitation of the dataset and have clarified this point in the revised manuscript in the Material and Methods section (see p36 l84-805).

Overall the discussion is highly speculative and could be shortened and refocused on the actual findings reported. For example, the fact that GO terms associated LIN-15B targets are associated with membrane processes (mentioned above) is not sufficient to speculate that LIN-15A could increase the delaminating capacities of Y by alleviating SynMuvB repression of membrane process genes.

Our intention was to discuss possible mechanisms that could connect the observed genetic interactions to the cellular events underlying Y-to-PDA transdifferentiation. We fully agree that some of these interpretations, such as the impact of the DREAM/LIN-15A antagonisms on membrane remodeling, are purely speculative in nature. We have removed the following sentence : "In brief, the role of the Licensers would be to provide a favorable chromatin context for cellular processes that favor/install a plastic state, possibly through the modulation of membrane processes as suggested by our ChIP-seq analyses (Fig. S6). » and changed it to "In this framework, Td Licensers would facilitate transdifferentiation by alleviating identity-safeguarding chromatin states, thereby creating a permissive context for the Drivers to execute the Td program. », and have removed the paragraph describing Y delamination. More generally, we have substantially shortened and refocused the Discussion section to answer the referee's comment.

The classical definition of a licensing factor is a protein (or complex) that allows the start of DNA replication from a replication origin. In the field of reprogramming, the term "licenser" has been applied to pioneer factors which 'license' transcriptional reprogramming by accessing chromatin to initiate a series of events, including binding of additional, non-pioneer transcription factors and additional chromatin regulators. Here the authors apply the term 'Licensers' to LIN-15A and LIN-56 as factors that facilitate the Td process. This may lead to confusion (and implications) as to what these factors are actually doing.

We thank the reviewer for raising this point. We agree that the term "licensing" has been used in several biological contexts, including DNA replication and, more recently, cellular reprogramming, where it is often associated with pioneer factors that initiate chromatin remodeling and transcriptional changes. However, our use of the term "Licenser" is intended to describe a distinct functional concept emerging from the genetic analyses presented here. We introduced this terminology to distinguish a class of factors that facilitate transdifferentiation by alleviating identity-safeguarding mechanisms from the previously identified "Driver" factors that actively promote the cell-fate transition itself. In this framework, LIN-15A and LIN-56 are not proposed to act as pioneer factors or direct initiators of transcriptional reprogramming. Rather, the genetic data support a role in creating a permissive context for transdifferentiation by antagonizing mechanisms that oppose cell-fate change. We agree, however, that this distinction was not sufficiently defined in the original manuscript and may lead to confusion. We have therefore revised the Results and Discussion to explicitly frame it in the context of transdifferentiation ("Td Licenser"), define what we mean, and to clearly distinguish this usage from previous applications of the term in DNA replication and reprogramming studies (for instance, see p10, l211-217; p13, l283-289 and p14 l312-315).

__Minor comments: __

__ Abstract: why are Drivers and Licensers in capitals? How is Driver defined? __

__- __We use capital letters to signal that these represent two conceptual categories. However, this could be changed if that impairs reading. Drivers are defined in this study as plasticity factors whose loss completely prevents Td initiation (see p10, l211-217 and p14 l312-315).

__Figure Aii: no PDE, ajm-1::GFP positive Y cells. It is not clear how the Y cell is identified-isn't ajm-1 supposed to surround the cell? The difference between the top and bottom ajm-1:egl-5 panels is not clear to a non expert. LIN-26 panel is missing. __

• The Y cell is identified by its location at the ventral-most position on the anterior side of the rectal slit. AJM-1 is a component of the apical junctions, hence it is expressed at the apical domain of the Y cell. The LIN-26 typo has been corrected, the marker used in this experiment is the rectal-specific gene egl-5 which labels the nucleus of the Y cell.

2F color scheme : licensers are not in yellow but pink

• Addressed : they now are yellow in the revised version

Fig S1: need to provide more details about experimental conditions for WB-stage, conditions (reducing agents?), nature of Q2015 antibody. In the absence of this information hard to substantiate claim of a LIN-15/LIN-56 heterodimer in the text -

See answer to reviewer #1 : we agree that this experiment is dispensable for the results presented in this manuscript and adds more questions than useful information, and it has been removed from the revised version.

__Line 130. What is the nature of the LIN-56 protein? This would be useful information __

• Addressed. We have indicated this early on in the introduction (p5, l95-96) and in the Results section (p7, l132-134). Note that little is known about LIN-56 except its association with LIN-15A in VPC specification and that is equally possesses a THAP-like C2CH motif.

__ Line 38 yielding__

• Addressed

__Line 48 identities suggested by Blau and Baltimore (1991). __

• Addressed

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Referee #3

Evidence, reproducibility and clarity

Through classical genetic analysis and the use of markers for different cell fates the authors identify the THAP domain protein LIN-15A as a novel factor in rectal-to-neuronal Y-to-PDA transdifferentiation (Td) in Caenorhabditis elegans. They show that lin-15A is not a core plasticity factor per se, but acts specifically in the Y cell to initiate Td by antagonizing a subset of chromatin-modifying complexes of the synmuvB class. Based on their data, the authors propose that lin-15A acts as a "licenser", as opposed to their previously described "drivers", to facilitate transdifferentiation.

Most of the key conclusions are convincing, and experiments overall well executed and controlled.

The lab previously showed that NODE-like complex components SEM-4/SALL4, CEH-6/OCT, EGL-27/MTA1 act together with the HOX TF EGL-5, SOX-2/SOX2 and HLH-16 to drive transdifferentiation of Y to PDA: in their absence Td does not initiate. The genetic evidence they provide here supports a model in which LIN-15A (together with another factor LIN-56) contributes (but is not essential) to the Td process: its loss results in a 50% decrease in Td (Figure 1A).

Genetic rescue experiments are consistent with lin-15A acting specifically in rectal cells (Figure 1D), and genetic interaction studies support a role in parallel to "driver" genes (Figure 2). The genetic experiments showing that lin-15A does not act in a second natural transdifferentiation process (K-to-DVB), and actually restricts plasticity in blastomeres, are also well executed and support a specific role for LIN-15A in the rectal Y cell.

The genetic data in Fig 4 is consistent with SynMuvB genes and LIN-15A acting antagonistically in the same pathway or on the same targets (figure 5). This is interesting, since in vulval cell fate specification lin-15A and synMuvB genes are redundant.

Major comments:

Based on the observation that LIN-15A does not affect SynMuvB expression in Y (figure S4), the authors conclude that antagonism of the SynMuvBs by LIN-15A is not likely mediated by a negative control of their expression, but rather by impacting their activity.

However, as suggested by the authors, antagonistic functions on the same targe genes is also a possibility. The classical approach to test this would be through expression profiling. I understand that RNA-seq on single Y cells cannot be carried out for technical reasons and that bulk RNA-seq would not be informative. Importantly, the same reasoning applies to the ChIP-seq data that is presented in support for common regulatory functions of a subset of synMuvs and LIN-15A (Figure 6 and S6), which was obtained from whole animals. The relevance of these results to the Y to PDA Td process is therefore extremely limited, as the claim that LIN-15A restricts lin-35/DREAM binding on a subset of target genes is based on a reported decrease in DREAM binding in lin-15 mutants in bulk chromatin. This is especially true as both DREAM and LIN-15A are widely expressed proteins.

In addition there are specific issues with Figure 6, which is mislabeled: upregulated and downregulated applies to gene expression, while the numbers refer to binding peaks. Why are some numbers in red (not mentioned in the legend). An example of the corresponding genome browser tracks should be shown in supplementary. Was a spike-in used to normalize data?

Overall conclusions based on ChIP-seq data should be significantly toned down throughout - eg line 445 in the discussion: a role in the modulation of membrane processes based on ChIP-seq would require some type of validation using available cell membrane markers. The GO term analysis (Figure S1) identifies many very broad classes.

Overall the discussion is highly speculative and could be shortened and refocused on the actual findings reported. For example, the fact that GO terms associated LIN-15B targets are associated with membrane processes (mentioned above) is not sufficient to speculate that LIN-15A could increase the delaminating capacities of Y by alleviating SynMuvB repression of membrane process genes.

A general comment: The classical definition of a licensing factor is a protein (or complex) that allows the start of DNA replication from a replication origin. In the field of reprogramming, the term "licenser" has been applied to pioneer factors which 'license' transcriptional reprogramming by accessing chromatin to initiate a series of events, including binding of additional, non-pioneer transcription factors and additional chromatin regulators. Here the authors apply the term 'Licensers' to LIN-15A and LIN-56 as factors that facilitate the Td process. This may lead to confusion (and implications) as to what these factors are actually doing.

Minor comments:

Abstract: why are Drivers and Licensers in capitals? How is Driver defined?

Figure Aii: no PDE, ajm-1::GFP positive Y cells. It is not clear how the Y cell is identified-isn't ajm-1 supposed to surround the cell? The difference between the top and bottom ajm-1:egl-5 panels is not clear to a non expert. LIN-26 panel is missing.

2F color scheme : licensers are not in yellow but pink

Fig S1: need to provide more details about experimental conditions for WB-stage, conditions (reducing agents?), nature of Q2015 antibody. In the absence of this information hard to substantiate claim of a LIN-15/LIN-56 heterodimer in the text

Line 130. What is the nature of the LIN-56 protein? This would be useful information

Line 38 yielding

Line 48 identities suggested by Blau and Baltimore (1991).

Significance

The present work builds upon previous work from the lab identifying drivers of the Y to PDA transdifferentiation process and additional players. This is the only group working on this specific Td process. The main limitation of this study is that it relies almost exclusively on classical genetic analysis and reporter gene expression. LIN-15A and SynMuvB proteins are broadly expressed chromatin associated factors and no LIN-15A homolog has been identified outside nematodes; technical difficulties have hindered the implementation of single cell expression data or chromatin binding profiles of the individual cells studied, which would constitute a major brekthrough. In addition the notion of chromatin factors as reprogramming barriers is already well documented. The novelty here lies in the study of natural developmentally regulated transdifferentiation process.

The work may nonetheless be of broad interest in the reprogramming field by providing an example of the complexity of interaction driving a natural transdifferentiation process, highlighting the activity of parallel pathways and the central role of chromatin associated proteins.

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Referee #2

Evidence, reproducibility and clarity

The study describes the implication of LIN-15A, which is a THAP zinc-finger-like protein, in the Y-to-PDA conversion. This cell fate conversion is an intriguing type of direct reprogramming, as it is a developmentally programmed transdifferentiation process in the nematode C. elegans and offers a unique model for investigating cell fate conversion in vivo. The Jarriault research group has demonstrated in the past how powerful this cell-fate conversion model is for identifying novel players in transdifferentiation. This is a well-executed genetic study that establishes lin-15A as a new player in the Y-to-PDA transdifferentiation phenomenon and introduces a useful conceptual distinction between Driver and Licenser factors. The genetic interactions with class B SynMuvs are clean and informative. LIN-15A is proposed to act as a Licenser in a context-dependent manner because it is also expressed in other cell types; mechanistic insights are indispensable for understanding the nature of this context dependence. Overall, I support the publication of this study, but have some comments prior to its acceptance.

Main comments:

The conclusions derived from the presented data are generally comprehensible but should be phrased more carefully to grant full legitimacy. The reason is that the central mechanistic claim that LIN-15A licenses Td by antagonizing most of the SynMuvBs chromatin factors, including DREAM, rests on whole-animal ChIP-seq that cannot resolve the Y cell. The authors acknowledge that "it was not technically feasible to purify sufficient Y cells for analysis" and therefore use synchronized unstarved L1 whole-animal lysates. This is certainly legitimate, but demands more tact when using such a conclusion as the headline claim.

Also, in the context of the ChIP-Seq experiments, it is understandable that it could not be conducted in a cell-specific manner, but two duplicates in some ChIP-Seq experiments (as stated in the material and methods) is below standard.

Regarding the genetic interactions with met-2: as MET-2 works in concert with other SET domain proteins, such as SET-25, and also HPL-2, is there a possibility they may be implicated?

The fact that Y-to-PDA in males (which involves a cell division) shows the same lin-15A dependence as in hermaphrodites is informative and a bit underplayed. Since this argues against a cell-cycle-coupled mechanism (an important aspect of the reprogramming field) for LIN-15A, it is worth elaborating on this in the discussion.

Minor:

• in the legend of Figure 1 and other places, it should be "Fisher's exact" instead of "Fisher exact"
• line 31; exhibits instead of exhibit
• line 85: results instead of result
• line 228: involvement instead of involvment
• line 293: "of missing" in loss of lin-36 had no effect while loss ... lin-53 further
• lines 297 - 299: check sentence; reads not correct
• line 395: "with an increase"
• line 484: "with regard"

Significance

This is a well-executed genetic study that establishes lin-15A as a new player in Y-to-PDA transdifferentiation and introduces a useful conceptual distinction between Driver and Licenser factors. The genetic interactions are clean and informative.

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Referee #1

Evidence, reproducibility and clarity

Summary

This manuscript from Sophie Jarriault's lab investigates the genetic mechanisms underpinning Y-to-PDA transdifferentiation in the nematode Caenorhabditis elegans. Transdifferentiation is the process by which one differentiated cell type converts to a different differentiated cell type without passing through a pluripotent stem cell stage. Understanding the biology and molecular mechanisms of transdifferentiation in an in vivo context will ultimately aid in engineering transdifferentiation for regenerative medical applications.

Through a forward genetic screen the authors isolated a mutant allele of the lin-15A gene, which encodes a THAP domain chromatin factor. lin-15A has been well-studied for its role in redundant chromatin pathways that repress the expression of LIN-3/EGF during vulval development. Hence it is referred to as a SynMuvA gene. The authors show that lin-15A null mutants exhibit an incompletely penetrant defect in Y-to-PDA transdifferentiation, with approximately 50% of the animals exhibiting the defect. They show that lin-15A functions in rectal cells, a group of cells in the vicinity of Y and they provide evidence that LIN-15A functions in the initiation of transdifferentiation. Genetic evidence supports a model in which LIN-15A functions in parallel to "Drivers" of transdifferentiation, which include the transcriptional regulators, CEH-6, SOX-2, EGL-5, SEM-4, EGL-27, and SEM-4. An interesting genetic result is that LIN-15A, together another synMuvA gene LIN-56, functions antagonistically to synMuvB genes. Through an analysis of ChIP-seq data, they suggest a model in which LIN-15A antagonizes SynMuvB function in the transdifferentiation decision.

Critique

This is a well-written manuscript on an interesting topic. The work provides genetic insights that will be useful for setting "boundary conditions" and predictions for subsequent molecular studies. The authors should consider the following points.

Major Points

1. As the authors acknowledge in the section at the end of the discussion (Limitations of this study) it is not established that LIN-15A has a cell-autonomous function in Y-to-PDA transdifferentiation. Given that LIN-15A has a cell non-autonomous function in vulval development (Herman and Hedgecock, 1990) it is possible that its function here could also be. The authors have used an egl-5 promoter to rescue lin-15A through expression in rectal cells; however, all these cells are in a neighborhood. The lack of a promoter that is specfic for Y has impeded answering this question (a standard genetic mosaic analysis would be problematic because of the incomplete penetrance of the mutation). Although this issue is addressed in the section at the end of the Discussion, I think most readers would like to see this acknowledged earlier in the presentation, perhaps after describing the egl-5 rescue experiment.
2. The experiment shown in Figure S1B is unconvincing. To show that they are detecting a LIN-15A-LIN-56 heterodimer, the authors need to show that antibody tags to both proteins detect the band. Mass spectrometry or biochemical purifications would also be helpful. As it is, they show the protein(s) detected depend genetically on lin-56 and lin-15A. It was also unclear what the other bands were in the mutant backgrounds
3. Lines 207-212. The authors are making an argument that LIN-15A and LIN-56 function as "Licensers" not "Drivers" because they are not strictly required but appear to facilitate the process. Could it be that LIN-15A and LIN-56 function as "Drivers" but that in their absence the fidelity of the process is compromise? There are many ways that genetic redundancy can be manifested at biochemical levels and the concern is that there are other interpretations of the data. In this regard, the authors should consider rewriting the Abstract to focus on the genetic results underpinning the work. The current version or the Abstract focuses on an interpretation of the data, not the data itself.

Minor Points

1. Line 279. The authors state that "LIN-15A becomes dispensable when member of the SynMuvB factors are absent." This statement is not completely accurate as the suppression is incomplete.
2. Line 294. The number in Tagble S1 is 58.8% not 65%
3. Lines 300-301. I couldn't find the data for lin-40.
4. Line 363. Should be "represses cell cycle genes."
5. Line 862. AJM-1 is not a tight junction component. AJM-1 is best described as a component of apical junctions.

David Greenstein

Significance

General Assessment

This is well-written genetic study on an interesting topic-a natural case of transdifferentiation. The experiments are well conducted and properly analyzed. The identification of LIN-15A as a player in Y-to-PDA transdifferentiation will enable experimental tests of the authors' model. The limitations of the study are that for technical reasons the authors acknowledge, it is not established whether the function of LIN-15A is cell autonomous to Y. The authors have undertaken the beginnings of molecular work to get at mechanism, but the downstream targets of the apparent chromatin regulation are not yet apparent.

Advance

The identification of LIN-15A as a regulator of Y-to-PDA transdifferentation and the suppression by mutations in synMuvB genes are of interest to the field.

Audience

This manuscript will be of keen interest to developmental geneticists focusing on chromatin regulation in genetic model systems as well as developmental biologists studying transdifferentiation processes.