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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors use a combination of genetic and pharmacological immersion approaches to investigate the effects of hyperglycemia on development of the retina in zebrafish larvae. They demonstrate a rather mild phenotype (though still convincing) such that photoreceptor maturation is delayed/impaired and the Muller glia are also affected. Visual function is modestly impacted, as measured with an assay that can be influenced by motor as well as sensory defects. The authors conclude that altered timing of the differentiation of retinal cells, together with accumulation of reactive oxygen species (ROS) underly the photoreceptor defects and reduced visual function in the hyperglycemic larvae.

Major comments:

The retinal phenotype related to hyperglycemia is quite subtle, but sufficiently consistent. This phenotype would be more convincing, and lead to more definitive conclusions, if the authors could include some ultrastructural (TEM) information, or even high-resolution/magnification color images of thinner sections processed using conventional histological methods, such as H&E, or toluidine blue/pyronin B. It is difficult to appreciate the features of the apical projections of the photoreceptors in the fluorescently-labeled images.

Comparison of zpr1 labeling with the TaC:eGFP transgenic is unfortunate. Ideally the authors would use the pdx1 mutant on this transgenic background. Alternatively, the authors could perform TaC in situ hybridizations.

The visual function defect is also quite mild. The authors should mention that the OKR assay also relies upon motor function, and so the defect may be related to sensory deficit, motor deficit, or both. Larval ERGs would address this issue.

The "reactive gliosis" phenotype is also mild/subtle, and not entirely convincing. More information should be provided regarding what the authors considered an "abnormal shape" of an MG cell body. Ideally, there is an at least somewhat objective means to score normal vs. abnormal and then quantify.

In Figure 6 legend, the authors state that superoxide production is increased, but the graph does not appear convincing in this regard, and no statistical evaluation is provided.

The authors do not indicate whether they checked datasets for having a normal distribution prior to the selection of a t-test (or ANOVA) for analysis vs. nonparametric tests.

The model and accompanying text in the Discussion seem overly wordy and speculative. This discussion also does not acknowledge that the effects upon the retina may be indirect, mediated by other tissues that are impacted by hyperglycemia. For example, ocular vascular defects have been described to result from hyperglycemia, over a similar time frame of analysis, and the effects on the retina may be downstream of these defects.

Minor comments:

Introduction - the statement appearing in the Discussion (offspring of diabetic pregnancies had significantly thinner inner and outer macula as well as lower macular volume [43].) should appear in the Introduction to better capture the interest of the reader.

Page 1. (..in nearly 10% of US pregnancies) - citation needed.

Page 2. Pdx1 mutation should be briefly described when first mentioned.

Legend for Figure 2 could benefit from a definition of 2-NDBG.

Figure 2B does not show Whole Body [Glucose] because the heads were removed for histological analysis.

It is this reviewer's experience and opinion that zpr-3 labels rods and the RH2 members of the double cones, due to the sequence similarity of RH1 (rhodopsin) and RH2. The cited paper (Yin et al., 2012) hints at this as well, but is slightly unclear due to the terminology used in the paper in describing cone subtypes.

Page 8. The marker used to detect bipolar neurons should be mentioned within the Results section.

Pages 12-13. The localization of TUNEL+ profiles may be related to microglia extending processes into the ONL, engulfing photoreceptors, and then internally transporting the bits to their cellular "eating stations" within other retinal layers.

Significance

Significance/Comparison to published knowledge:

The zebrafish model(s) are sufficiently novel, versatile, and interesting to constitute an advance in this field. A literature search by this reviewer revealed that the focus upon retinal cells in hyperglycemic, larval zebrafish appears novel. However, the phenotype is remarkably mild, and there is concern that follow-up studies in pursuit of more mechanistic insights will be challenging to perform by the authors and by others in the field. This paper does lay some key groundwork, but what comes next sounds like a lot of fishing expeditions.

Interested audiences:

Investigators in vision science/ophthalmology, developmental biology, toxicology/teratology, and diabetes.

Reviewer keywords:

Developmental biology, genetics, retina, zebrafish, photoreceptors.

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Referee #2

Evidence, reproducibility and clarity

Summary:

This paper uses immersion of embryonic zebrafish in high glucose solution to model the effects of hyperglycemia on retinal development. The paper finds that high glucose causes a reduction in the number of photoreceptors and horizontal cells, abnormalities in the morphology of photoreceptors and Müller glia, increased retinal cell apoptosis, a change in the timing of neuronal cell birth, and a defect in the optokinetic response. The mechanistic link between high glucose and changes in retinal development is not well described but may involve an increase in reactive oxygen species.

Major comments:

1. Is the photoreceptor phenotype a degenerative rather a developmental phenotype? In embryos treated with high glucose, photoreceptors in the periphery of the retina near the ciliary margin, which are younger in age, seem to be structurally more normal than those at the center, away from the ciliary margin, which are older in age. Could this reflect the fact that photoreceptor development proceeds normally followed by degenerative changes?
2. For many or most phenotypes the main examined treatment is glucose + dexamethasone. The authors state this combination achieves more uniform glucose concentrations in the embryos as compared to glucose alone. However, dexamethasone may have effects independently of glucose and the dexamethasone only control is not used in some or most experiments. For example in Fig. 3, could dexamethasone alone causes changes in photoreceptor morphology? In the combo treatment, is it possible that some effects are simply due to a synergism of glucose+dex and not because dex causes a more uniformly high intraembryonic glucose?
3. It is interesting that hyperglycemic retinas show more neurons born between 2-5 days post fertilization in the RGC layer than in the outer nuclear layer (Fig 7). One interpretation is delayed birth of RGCs after hyperglycemia as the authors suggest. Another interpretation is that non-RGC cell types are in now in the RGC layer; or that some proliferating progenitors persist at 5dpf. Co-localization of EdU with differentiation markers, and EdU analysis after a short pulse of 2 hours would help to nail down if there is developmental delay or something else going on here.
4. Do Müller cells go into cycle after high glucose treatment?
5. The increase in ROS in Fig. 6 does not seem very convincing. Is the difference between untreated and glucose or glucose/dex treatments statistically significant? I would avoid making too much of this unless some type of phenotype rescue with N-acetylcysteine or vitamin C, or Trolox, can be shown. Methylene blue is a bit non-specific as an antioxidant.

Significance

The translational significance of the findings is that they might provide a model to study how embryonic hyperglycemia due to maternal diabetes changes embryonic development. Pitfalls include the fact that its relevance to humans is unclear. Is maternal diabetes known to cause visual abnormalities due to abnormal retinal development in newborns? The basic biology significance may be to provide a model to investigate how glucose metabolism is connected to developmental decisions. However it is unclear whether glucose metabolism within retinal cells mediates the observed effects; and the high glucose used here is likely unphysiological as at these developmental stages zebrafish embryos feed from the yolk sac.

Audience interested in this work may include zebrafish developmental biologists. My expertise: metabolism, retinal development.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this work, the authors Titialii-Torres and Morris assess how hypergycemia affects the development of the neural retina using a genetic and a nutritional approach in the model organism zebrafish. This is important as diabetes can contribute to retinal degeneration in during the progression of diabetic retinopathy which often leads to blindness in adults.

The authors examine how different cell types in the neural retina are affected in a genetic hyperglycemic model, the pdx1 mutant embryos, and in a nutritional model, in which hyperglycemia is induced by glucose and dexamethasone exposure. Titialii-Torres and Morris show that in both models, photoreceptor rods and cones, as well as horizontal cells, are reduced in number. Additionally, they report a delay in retinal cell differentiation accompanied by increased ROS production in the hyperglycemic retina. Altered expression of metabolism related genes and effects on visual function were also found in their hyperglycemic models. Overall, the assessment of the different retinal cell types impacted by hyperglycemia and examination of potential molecular mechanisms contributes important and novel data to the field. However, the data as presented falls short in supporting the conclusions of the authors.

Major comments

Overall, the conclusions would be more strongly supported by improving the clarity of the images, and by additional analyses.

Figure1:

o Referring to figure 1 E' the text states that an arrowhead points to the shorter and thinner outer segment of a rod. In the figure there is an arrow pointing to a cell without a visible outer segment, making it hard to make the same conclusion.

o Additionally the GFP signal is very weak in D and E in the dorsal retina. Therefore it is not possible to see if there is also a decreased amount of rods in the dorsal retina as claimed.

o In the text it is mentioned that cones in the ventral region are affected. Is there also a difference in the dorsal region?

Figure 3:

o Rods and cones might be better displayed in close-ups from sections rather than from projections of the whole eye.

o The authors write about a reduction of cones upon glucose treatment. In the graph this is not highlighted as significant.

Figure 4: as the overall number of cones was already assessed before, focusing on a smaller region might help the reader to see the Zpr3 staining showing that the outer segments of the cones are stunted (as stated in the main text). In the figure panels presented, outer segments cannot be clearly seen.

Figure 6: scale bar is missing. Please clarify what the red and the green is. Why is there a red signal from Mitosox outside of the embryo (panel C)? The fluorescence of the superoxide probe should be displayed in a more convincing way. For example, in sections to enable assignment of signal to tissues and cells, as shown in Supplemental Figure 5.

Figure 8: Is the coincubation with methylene blue leading to a significant increase in photoreceptors? If yes, this should be indicated in the graph.

Supplemental Figure 2: The authors assert that TUNEL+ cell labeling coincides with Müller glial cells. This would be better supported with a magnified view of the INL, optimally by applying TUNEL staining to hyperglycemic, GFAP:GFP transgenic samples.

It would be of interest to determine if an incubation with methylene blue also affects photoreceptors in pdx1 mutants. Is it possible to confirm that Methylene blue treatment reduces ROS in the retina ? Can changes in ROS response gene expression be demonstrated by qPCR ? The assumptions about ROS should be either strengthened by additional experiments or less emphasized in the discussion.

For completeness, glucose metabolism in the genetic model should be also addressed and compared to the nutritional model.

The authors talk about a "long term" return to normoglycemia and long term effects of hyperglycemia. Analysis at 7 dpf after a 2 day return to normoglycemic conditions can hardly be called long term. To make these statements, an assessment after a longer time period (one week or more if possible?) would be more convincing.

The claims of 'reactive gliosis' in glucose-treated larvae is overstated. Biologically meaningful differences in cell shape between control and treated samples are not evident from the images (Fig. 5A-F). This should at least be quantitated by shape analysis. The Glucose+Dex samples do not show increased number of Müller glial cells, and glucose treatment alone leads to highly variable glucose levels. This complicates and weakens a correlation with hyperglycemia.

In addition, there are many minor inconsistencies and awkwardness in the presentation of the figures, as detailed below.

Minor comments

Some figures would benefit if they would follow the sequence of the text. Eg: figure 1 and 3, the text addresses first the rods and then the cones.

In several places the panels referred to in the text do not match the figures or figure panels are not mentioned at all. For example:

Pg 3 "Quantification revealed a significant decrease in both rod and cone photoreceptors in pdx1 mutants at 5 dpf (Fig. 1C)."

• the quantification is in panels C and F.

The main text does not mention or explain Figure 2A Pg 5 "The results confirmed that rods and cones from hyperglycemic larvae have shorter outer segments compared to wild type larvae at 5 dpf (Fig. 4A-C)."

• panel C is a graph of Saccades.

Fig. S3 - only panel Y is referred to in the text.

Supplemental figure 2: the authors claim a significant increase of apoptotic cells in the genetic model. In the corresponding graph significance is not indicated.

Figure 5: scale bars are missing, the figure text and the numbering of the figure do not fit.

Supplemental figures 4 and 5:

o The Prox1 staining is hard to see and it is unclear what was counted as cells.

o In Supp Fig. 4E the PKC staining looks increased compared to the controls.

o The graphs could have similar y axes, especially because in supplemental figure 5 the amount of cells/µm is also different. Why not always use per 50µm? Shouldn't the amount of cells in wild types and untreated embryos be the same per 50µm?

o Also the labelling of the y axes could be made coherent in the two figures.

Supplemental figure 6: K is not mentioned in the legend.

2-NDBG treatment is not explained in material and methods

Significance

Significance

Titialii-Torres et al. characterize the impaired development of neural retinal cells under hyperglycemic conditions in zebrafish larvae and also show evidence of impaired visual function. This work will be of interest for researchers in the field of diabetes, especially those focused on diabetic retinopathy, and for developmental biologists interested in pathologies that impact human development. While the manuscript provides insights into the development of the retina under hyperglycemic conditions, a revision addressing weaknesses of figure presentation and some additional confirmatory experiments would be of great benefit.

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Reply to the reviewers

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

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Referee #2

Evidence, reproducibility and clarity

Kleijn et al. measured transcript and protein abundance in fission yeast cultures growing on different nutrient sources (and thus at different growth rates) in turbidostats. Their experimental design is sound and the data quality appears good. The authors focus on analyzing their data from the vantage point of previously reported ideas on principles of proteome allocation, and expand beyond this framework with interesting analyses, e.g., on the stoichiometry of translation complexes changes with the growth rate.

Generally I find the paper well written and the conclusions well substantiated. Below are specific recommendations that may help the authors improve their study:

• Your data allow investigating the extend of transcriptional and post-transcriptional regulation in fission yeast, and I think this analysis will be very interesting. PMID: 28481885 provides one simple approach to such analysis, and the authors may use another. Importantly, they authors must account for measurement noise.
• Your analysis of the ribosomal proteins (RP), the ribosome biogenesis regulon (RiBi), and the translation initiation, elongation and termination factors (IET) is interesting. I would love to know whether there changes within these groups of proteins, e.g., different RP in budding yeast change differently with growth rate (PMID: 24767987, PMID: 26565899) and I would love to know if this is the case with fission yeast.
• The Z score ranges on some of the heatmaps (e.g. fig 2A) are so wide that the changes in protein / RNA abundance are difficult to see.
• It will be very useful to perform unbiased gene set enrichment analysis of the functions that show significant growth rate dependent and nutrient dependent effects, e.g., as in Fig 11 of PMID: 21525243

Significance

I am an expert in this field, and I think that this study represents a significant advance.

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Referee #1

Evidence, reproducibility and clarity

In this paper Kleijn et al study global gene expression profiles in S. pombe grown in different nitrogen sources using a turbidostat that result in variation in growth rate. The authors use both RNAseq to quantify RNA expression and mass spectrometry to quantify protein expression. They find that the expression of many genes is correlated with growth rate. This finding builds on prior work performed by other groups in S. cerevisiae and bacteria that show organismal growth rate is a primary determinant of gene expression state for a large fraction of genes. The findings in this paper confirm and extend those results.

Significance

One surprising aspect of this manuscript is that the authors do not seem to have made the most of their experimental design. The acquisition of both protein and mRNA expression across these conditions provides a unique dataset for looking at how these two levels of expression agree with respect to each other. A simple plot showing the strength of the growth rate response for a gene at the level of mRNA and protein would already be interesting, but I would think that there is the opportunity to look more quantitatively at whether the ratio of mRNA to protein remains constant across growth rates or whether there systematic deviations that are biologically interesting. I would encourage the authors to address this question with their unique dataset.

Prior to publication the authors should address the following points.

At what point in the turbidostat cycle was the sampling performed? At steady state or during the dilution phase?

It is unclear in the text what transcripts are included in the category ncRNA. Does this include tRNA and rRNA?

The basis for the abbreviations for positive (R) negative (P) and not significant (Q) are obscure. Why not P, N, NS?

In Brauer et al., the fraction of cells in G1 is correlated with growth rate. Is that the case in S pombe? Is there any relationship between cell cycle gene expression and growth rate related gene expression?

Is there anything unique to the set of ~100 genes that are anticorrelated between mRNA and protein in response to growth rate variation?

A clearer explanation of the FC metric and the rationale for its use should be made in the results. What is FC an abbreviation for? It is unclear why this metric is needed, when the strength of the response to growth rate is captured by the slope.

Airoldi et al., 2016 and Airoldi et al., 2009 looked at methods for normalizing gene expression to growth rate and may be relevant sources.

The contrast in the experimental rationale between using chemostats and turbidostats is interesting, but I am left unclear about whether the result is really that different. What is the key distinction in the observed data in comparing gene expression response to growth rate in the chemostat and turidostat?

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): In this manuscript, using in vivo infection of Zebrafish embryos with Mycobacterium marinum and THP1-derived macrophages infected with Mycobacterium tuberculosis, the authors show that these pathogenic mycobacteria trigger an increase of K+ concentration through the expression of OXSR1. The ESX1 secretion system that is essential for the virulence of M. marinum is required for the expression of OXSR1 and SPAK. OXSR1 and SPAK are involved in the WNK signaling pathway and are cytoplasmic serine/threonine protein kinases that regulate the function of a series of sodium, potassium and chloride co-transporters via phosphorylation. Given that K+ efflux is now accepted as the main inducer of NLRP3 inflammasome, the authors report that this infection-induced OXSR1 expression restrains the protective NLRP3 inflammasome response leading to IL-1b maturation and secretion. Il-1b as a very potent pro-inflammatory triggers TNF-a production and the authors demonstrate that infection-induced OXSR1 expression suppressed host protective TNF-a and cell death early in fection. It appears therefore that virulent mycobacteria induce OXSR1 expression to reduce inflammasome activation by maintaining high intracellular K+. The results presented by the authors are convincing and the conclusions raised by the authors are well supported by the data. In zebrafish embryos, OXSR1 knockdown nicely reduces mycobacteria burden. Based on their conclusions that infection-induced OXSR1 expression reduces NLRP3 inflammasome activation, NLRP3 inflammasome activation has therefore a protective effect against bacterial infection. My main concern is that surprisingly, nlrp3 or il1b knockdown has no effect on bacterial burden in comparison to control embryos. Lane 256, as an explanation, the authors wrote "This may have been because we were using mosaic F0 CRISPR knockout, which is not a complete removal". The removal using mosaic F0 CRISPR knockout is nevertheless sufficient to observe a decrease in bacterial burden following OXSR1 knockdown. Would it be possible that OXSR1 also regulates immunity independently of NLRP3 inflammasome?

Yes, we will add text to the discussion to address potential NLRP3-independent mechanisms that connect OXSR1 to immunity against mycobacterial infection.

The lack of effect of il1b knockdown on M. marinum burden has been corroborated by independent laboratories including a publication from the Elks lab in Journal of Immunology: Ogryzko et al 2019. The Ogryzko study found no effect of il1b knockout on M. marinum burden.

**Other comments:** OXSR1 WB in extended Data 3 is really poor quality so that it is hard to see the increased expression of OXSR1 following infection.

The western blot will be repeated for cleaner images.

Figure 2C. It is not shown but I guess that similar results should be obtain using M. tuberculosis.

Material leaving our BSL3 facility must be decontaminated which makes this suggested analysis impossible in our facility.

Figures 5D and 5E. To confirm the involvement of NLRP3, in addition of using MCC950, NLRP3 knock down using siRNA should be also performed. NLRP3-deficient THP-1 cells are also commercially available if the siRNA-mediated knock down of NLRP3 is not convincing enough.

We will purchase NLRP3 deficient THP-1 cells and use our existing shRNA vector to create NLRP3 and OXSR1 deficient cells. We will repeat the experiments in 5D and 5E in these cells to confirm NLRP3 involvement.

**Minor comments:** How do the authors think that mycobacterium induces OXSR1 expression following infection? It has not been investigated and it is not discussed.

In Fig1A we showed upregulation of oxsr1a transcription and in Fig2A we showed upregulation of OXSR1 protein. In line 204 of the discussion we described our hypothesis that oxsr1a transcription is responsive to the mycobacterial ESX1 secretion system.*

*

Reviewer #1 (Significance (Required)): The observations reported in this manuscript are interesting since for the first time, it is described that virulent mycobacteria induce OXSR1 expression to reduce NLRP3 inflammasome activation by maintaining high intracellular K+. This is quite a significant advance in the field. To escape immune control, many successful intracellular pathogens have evolved methods to limit inflammasome activation. While it is known that potassium efflux is a trigger for inflammasome activation, the interaction between mycobacterial infection, potassium efflux and inflammasome activation was not explored. My field of expertise is the regulation of inflammasome activation. As far as I remember, I've never reviewed a paper using zebrafish embryos but here, the explanations and data are clear so that it was easy to understand and to evaluate. Likewise, I did not know the WNK signaling pathway but the literature clearly shows that it is involved in intracellular ionic balance.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): Hortle et al, in this study evaluated the role of WNK kinases SPAK and OXSR1 during M. marinum and M. tuberculosis infection. These two kinases inhibit the KCC channels which have a tendency to export potassium out of the cell. Since potassium efflux is a known stimulator of NLRP3 inflammasome activation, this raises the possible role of these kinases in inflammation and infection. Authors showed that inhibiting OXSR1 genetically and chemically reduced the mycobacterium survival in cells and zebrafish model, thus proposing OXSR1 as a host-directed therapeutic candidate. They showed that knockdown of OXSR1a leads to NLRP3 inflammasome mediated IL1B induction, which results in increase in TNFa and suppression of mycobacterium growth. Furthermore, reduction in mycobacterium growth in OXSR1a KD zebrafish embryos was found to be dependent on ESX1 machinery of Mycobacterium. The role of potassium in regulating Mycobacterium host response is novel. However there are few things which are missing from this interesting work. **Main comments**

1. Since OXSR1 is known to inhibit KCC channels, which will lead to increase intracellular potassium. Why in infected control cells there is no increase potassium, Fig 2C. What would be the role of potassium in OXSR1 mediated control of Mtb growth?

We will perform more experiments with altered levels of extracellular potassium to determine if infected control cells have increased intracellular potassium compared to OXSR1 knockdown cells.

Does addition of extracellular potassium restricts mycobacterium in OXSR1-KD cells?

We will perform additional experiments with the addition of potassium to the cell culture medium to address this concern.

Since OXSR1 is known to inhibit KCC channels, What happens to the activity of these channels in OXSR1 KD cells? This is important, because authors could not find any difference in intracellular potassium between uninfected control and uninfected OXSR1 KD cells (Fig 2C). It will be good to add the flowcytometric histogram or dot plots of potassium staining in the main figure or in extended figures.

We have data showing that although there is minimal difference in basal K+ level in OXSR1 KD cells, there is significantly lower K+ level when the cells are placed in High K+ media, or osmotic shock. We will include this data in the revised manuscript. We will amend the figures to include Flow plots.

Acquisition of potassium stained cells - In methodology it has been mentioned that ion K+ Green stained undifferentiated THP1 cells were acquired using PE channel while differentiated THP1 cells were acquired using FITC channel. Furthermore in methods its mentioned that Leica Sp8 microscope was used to acquire images, however I do not see any of this data in the manuscript.

Ion K+ green emits into both the PE and FITC channels. Our choice to use the FITC or PE channel depended on whether the cells were also infected with red fluorescent bacteria which “contaminates” the PE channel.

Fig 2E and 3D - Meaning of "Normalized CFU/ml"? Each dot represents what? How many times this experiment was performed, please add in the legend.

Normalized CFU/ml means that the CFU at 3 day post infection were normalized to the 0 day post infection intracellular bacterial burden, to adjust for any differences in phagocytosis of bacteria. Each dot represents the CFU from an infected well in a single representative experiment and the experiment was repeated 3 times. This information will be added to the figure legend.

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Fig 1D - What could be the reason of no statistical significant difference between wild type and homozygous oxsr1a-KO fish?

This data is from two experimental replicates. We are currently growing more breeding fish to generate embryos for experimental replicates.

Good to have a schematic model showing the finding s of the study

We will add a schematic model to the manuscript.

TNFa is double edge sword and can lead to pathology. Hence treatment of chronically infected animals (say mice) by Compound B, will be needed to confirm the HDT activity of OXSR1.

Yes, we will add discussion of this point as a caveat to our future direction of using OXSR1 inhibition as a HDT.

Reviewer #2 (Significance (Required)): This study showed role of kinases, which regulate trafficking of potassium, in mycobacterium-host interaction. Since kinases are draggable, so this opens a new area for developing host-directed therapies for TB. Reviewer #3 (Evidence, reproducibility and clarity (Required)): In this study, the authors suggest to have evidence for OXSR1 to inhibit NLRP3 inflammasome activation by limiting potassium efflux during mycobacterial infection. To my opinion, the study lacks important results supporting their main conclusions. In many instances, the authors have over-interpreted their data and I therefore do not support publication of this study. **Main comments:** Activation of the NLRP3 inflammasome upon OXSR1 knockdown was not convincingly demonstrated.

We will address the activation state of the NLRP3 inflammasome with NLRP3 KO and OXSR1 KD cells as also suggested by reviewer 1: We will purchase NLRP3 deficient THP-1 cells and use our existing shRNA vector to create NLRP3 and OXSR1 deficient cells. We will repeat the experiments in 5D and 5E in these cells to confirm NLRP3 involvement.

Clearance of bacteria in an organism, herein zebrafish, involves mechanisms in different cell types including downstream of inflammasome activation. Thus, bacterial clearance experiments in THP-1 cells might not necessarily be related to in vivo experiments in an organismal context. Finally, a mechanism as to how mycobacteria enhance OXSR1 expression to block a NLRP3-mediated response has not been addressed.

We are not able to perform in depth analysis of the bacterial side of this host-pathogen interaction as my lab will close in the next 4 months. We have shown that transcriptional upregulation of oxsr1a is ESX1-dependent. We will include data on OXSR1 protein expression with WT and ESX1 mutant bacteria when we repeat the western blots in Extended data 3.

**Specific comments:**

1. The author showed that the M. marinum ESX1 secretion system induced OXSR1 expression to inhibit the NLRP3 inflammasome activation. This is contradictory to another recent study (PMID: 18852239), which showed that the ESX1 secretion system activated the NLRP3 inflammasome. These effects are not mutually exclusive. The ESX1 secretion system has a “deliberate” purpose in exporting mycobacterial effector proteins to subvert cellular immunity while also having an “accidental” role in exposing the host cell cytosol to vacluolar contents that can activate cellular immunity. We do not assert that mycobacteria completely inhibit all NLRP3 activation – rather that attempts to stop full activation via inducing the expression of host OXSR1. This can be seen in the IL-1b data in figure 3E, where infected WT cells release more IL-1b than MCC950 treated cells, but less than OXSR1 KD cells.

In line 102, based on Data shown in Fig 1D, the authors concluded that homozygous, but not heterozygous, oxsr1asyd5 embryos showed reduced bacterial burden. However, in Fig 1D, the difference among the genotypes is not significant.

This concern will be addressed with additional replicates.

In line 196, the authors stated that "We present evidence that pathogenic mycobacteria increase macrophage K+ concentration by inducing expression of OXSR1." However, the authors did not provide evidence for this.

We will soften this phrase in the discussion to replace “by inducing” with “and induce”.

Based on Extended data 3, the authors concluded that infection increases the expression of OXSR1. However, this is not evidenced in the Western Blot. In addition, in panel B, the OXSR1 blot showed many non-specific bands with decreased intensity in OXSR1 knockdown conditions suggesting that there is unequal protein loading making it impossible to interpret these results.

We will repeat the western blots as per Reviewer 1’s comment as well.

The authors concluded that infection-induced OXSR1 expression suppressed inflammasome activity to aid mycobacterial infection. Experiments with Compound B, that inhibits OXSR1 phosphorylation, are used in support of the above conclusion. I do not really see a connection between OXSR1 expression and the inhibitor experiment.

We will reword “expression” to “activity” in regards to the inhibitor experiment.

In line 187, "Knockdown of tnfa reduced the amount of infection-induced tnfa promoter-driven GFP produced around sites of infection ....". How can a knockdown of tnfa affect the GFP expression driven by the tnfa promoter ?

The promoter fragment used in the TgBAC construct contains target sites for two of our guide RNAs. We will also include qPCR validation of the knockdown.

Reviewer #3 (Significance (Required)): Mechanism underlying decreased intracellular potassium level is of great interest in the inflammasome field. However, their observation is not in line with published studies. Audience in the pathogen-host interaction field will be interested. Expertise: dissection of signalling pathway regulation, molecular and cellular mechanism underlying NLRP3 inflammasome activation. We are not using zebrafish model.

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Referee #3

Evidence, reproducibility and clarity

In this study, the authors suggest to have evidence for OXSR1 to inhibit NLRP3 inflammasome activation by limiting potassium efflux during mycobacterial infection. To my opinion, the study lacks important results supporting their main conclusions. In many instances, the authors have over-interpreted their data and I therefore do not support publication of this study.

Main comments:

Activation of the NLRP3 inflammasome upon OXSR1 knockdown was not convincingly demonstrated. Clearance of bacteria in an organism, herein zebrafish, involves mechanisms in different cell types including downstream of inflammasome activation. Thus, bacterial clearance experiments in THP-1 cells might not necessarily be related to in vivo experiments in an organismal context. Finally, a mechanism as to how mycobacteria enhance OXSR1 expression to block a NLRP3-mediated response has not been addressed.

Specific comments:

1. The author showed that the M. marinum ESX1 secretion system induced OXSR1 expression to inhibit the NLRP3 inflammasome activation. This is contradictory to another recent study (PMID: 18852239), which showed that the ESX1 secretion system activated the NLRP3 inflammasome.
2. In line 102, based on Data shown in Fig 1D, the authors concluded that homozygous, but not heterozygous, oxsr1asyd5 embryos showed reduced bacterial burden. However, in Fig 1D, the difference among the genotypes is not significant.
3. In line 196, the authors stated that "We present evidence that pathogenic mycobacteria increase macrophage K+ concentration by inducing expression of OXSR1." However, the authors did not provide evidence for this.
4. Based on Extended data 3, the authors concluded that infection increases the expression of OXSR1. However, this is not evidenced in the Western Blot. In addition, in panel B, the OXSR1 blot showed many non-specific bands with decreased intensity in OXSR1 knockdown conditions suggesting that there is unequal protein loading making it impossible to interpret these results.
5. The authors concluded that infection-induced OXSR1 expression suppressed inflammasome activity to aid mycobacterial infection. Experiments with Compound B, that inhibits OXSR1 phosphorylation, are used in support of the above conclusion. I do not really see a connection between OXSR1 expression and the inhibitor experiment.
6. In line 187, "Knockdown of tnfa reduced the amount of infection-induced tnfa promoter-driven GFP produced around sites of infection ....". How can a knockdown of tnfa affect the GFP expression driven by the tnfa promoter ?

Significance

Mechanism underlying decreased intracellular potassium level is of great interest in the inflammasome field. However, their observation is not in line with published studies.

Audience in the pathogen-host interaction field will be interested.

Expertise: dissection of signalling pathway regulation, molecular and cellular mechanism underlying NLRP3 inflammasome activation. We are not using zebrafish model.

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Referee #2

Evidence, reproducibility and clarity

Hortle et al, in this study evaluated the role of WNK kinases SPAK and OXSR1 during M. marinum and M. tuberculosis infection. These two kinases inhibit the KCC channels which have a tendency to export potassium out of the cell. Since potassium efflux is a known stimulator of NLRP3 inflammasome activation, this raises the possible role of these kinases in inflammation and infection. Authors showed that inhibiting OXSR1 genetically and chemically reduced the mycobacterium survival in cells and zebrafish model, thus proposing OXSR1 as a host-directed therapeutic candidate. They showed that knockdown of OXSR1a leads to NLRP3 inflammasome mediated IL1B induction, which results in increase in TNFa and suppression of mycobacterium growth. Furthermore, reduction in mycobacterium growth in OXSR1a KD zebrafish embryos was found to be dependent on ESX1 machinery of Mycobacterium.

The role of potassium in regulating Mycobacterium host response is novel. However there are few things which are missing from this interesting work.

Main comments

1. Since OXSR1 is known to inhibit KCC channels, which will lead to increase intracellular potassium. Why in infected control cells there is no increase potassium, Fig 2C. What would be the role of potassium in OXSR1 mediated control of Mtb growth? Does addition of extracellular potassium restricts mycobacterium in OXSR1-KD cells?
2. Since OXSR1 is known to inhibit KCC channels, What happens to the activity of these channels in OXSR1 KD cells? This is important, because authors could not find any difference in intracellular potassium between uninfected control and uninfected OXSR1 KD cells (Fig 2C). It will be good to add the flowcytometric histogram or dot plots of potassium staining in the main figure or in extended figures.
3. Acquisition of potassium stained cells - In methodology it has been mentioned that ion K+ Green stained undifferentiated THP1 cells were acquired using PE channel while differentiated THP1 cells were acquired using FITC channel. Furthermore in methods its mentioned that Leica Sp8 microscope was used to acquire images, however I do not see any of this data in the manuscript.
4. Fig 2E and 3D - Meaning of "Normalized CFU/ml"? Each dot represents what? How many times this experiment was performed, please add in the legend.
5. Fig 1D - What could be the reason of no statistical significant difference between wild type and homozygous oxsr1a-KO fish?
6. Good to have a schematic model showing the finding s of the study
7. TNFa is double edge sword and can lead to pathology. Hence treatment of chronically infected animals (say mice) by Compound B, will be needed to confirm the HDT activity of OXSR1.

Significance

This study showed role of kinases, which regulate trafficking of potassium, in mycobacterium-host interaction. Since kinases are draggable, so this opens a new area for developing host-directed therapies for TB.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, using in vivo infection of Zebrafish embryos with Mycobacterium marinum and THP1-derived macrophages infected with Mycobacterium tuberculosis, the authors show that these pathogenic mycobacteria trigger an increase of K+ concentration through the expression of OXSR1. The ESX1 secretion system that is essential for the virulence of M. marinum is required for the expression of OXSR1 and SPAK. OXSR1 and SPAK are involved in the WNK signaling pathway and are cytoplasmic serine/threonine protein kinases that regulate the function of a series of sodium, potassium and chloride co-transporters via phosphorylation. Given that K+ efflux is now accepted as the main inducer of NLRP3 inflammasome, the authors report that this infection-induced OXSR1 expression restrains the protective NLRP3 inflammasome response leading to IL-1b maturation and secretion. Il-1b as a very potent pro-inflammatory triggers TNF-a production and the authors demonstrate that infection-induced OXSR1 expression suppressed host protective TNF-a and cell death early in fection. It appears therefore that virulent mycobacteria induce OXSR1 expression to reduce inflammasome activation by maintaining high intracellular K+.

The results presented by the authors are convincing and the conclusions raised by the authors are well supported by the data.

In zebrafish embryos, OXSR1 knockdown nicely reduces mycobacteria burden. Based on their conclusions that infection-induced OXSR1 expression reduces NLRP3 inflammasome activation, NLRP3 inflammasome activation has therefore a protective effect against bacterial infection. My main concern is that surprisingly, nlrp3 or il1b knockdown has no effect on bacterial burden in comparison to control embryos. Lane 256, as an explanation, the authors wrote "This may have been because we were using mosaic F0 CRISPR knockout, which is not a complete removal". The removal using mosaic F0 CRISPR knockout is nevertheless sufficient to observe a decrease in bacterial burden following OXSR1 knockdown. Would it be possible that OXSR1 also regulates immunity independently of NLRP3 inflammasome?

Other comments:

OXSR1 WB in extended Data 3 is really poor quality so that it is hard to see the increased expression of OXSR1 following infection.

Figure 2C. It is not shown but I guess that similar results should be obtain using M. tuberculosis.

Figures 5D and 5E. To confirm the involvement of NLRP3, in addition of using MCC950, NLRP3 knock down using siRNA should be also performed. NLRP3-deficient THP-1 cells are also commercially available if the siRNA-mediated knock down of NLRP3 is not convincing enough.

Minor comments:

How do the authors think that mycobacterium induces OXSR1 expression following infection? It has not been investigated and it is not discussed.

Significance

The observations reported in this manuscript are interesting since for the first time, it is described that virulent mycobacteria induce OXSR1 expression to reduce NLRP3 inflammasome activation by maintaining high intracellular K+. This is quite a significant advance in the field. To escape immune control, many successful intracellular pathogens have evolved methods to limit inflammasome activation. While it is known that potassium efflux is a trigger for inflammasome activation, the interaction between mycobacterial infection, potassium efflux and inflammasome activation was not explored.

My field of expertise is the regulation of inflammasome activation. As far as I remember, I've never reviewed a paper using zebrafish embryos but here, the explanations and data are clear so that it was easy to understand and to evaluate. Likewise, I did not know the WNK signaling pathway but the literature clearly shows that it is involved in intracellular ionic balance.

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Reply to the reviewers

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

In this project, authors develop a colorimetric and luminescence assay for the detection of SARS-CoV-2 RNA in vitro. They design an RNA based sensor that will be triggered by target RNA then release the ribosome binding site and a translation start site followed by a reporter gene. The released sequence will then trigger the production of reporter protein by transcription-translation coupled assay. Authors also introduce an RNA amplification step in order to increase the sensitivity of this assay.

**Strengths:**

This assay provides a simple, rapid way to detect SARS-CoV2 and it is an elegant way to incorporate transcription-translation coupled assay for SARS-CoV-2 RNA detection and identify SARS-CoV-2 patient samples. It is a nice assay and the performance is comparable with the existing method.

**Weaknesses:**

However, the positioning of this assay is not very clear. The readout of this assay could be recorded by camera whereas it includes several steps such as RNA extraction, amplification, transcription-translation coupled assay and reporter reaction. The limitations of the existing methods (RT-PCR, paper strip) and the advantages of this assay haven't been demonstrated by the experiments. The stability of RNA may also restrict the application of the proposed assay on site.

**Major comments:**

Authors are suggested to design an experiment to show the advantage of this assay compared with the existing method.

Response: We thank the reviewer for pointing this out. In Fig 5, we show a comparison of our assay with the bench mark in COVID-19 diagnostics, which is the RT-qPCR assay. We specifically correlate the Ct- values obtained for RT-qPCRs with the amount of color or luminescence obtained through our assay. From these experiments we note that the sensitivity of our assay is a lttle less than the RT-qPCRs where our assay does not detect Ct-values in the 36 to 38 range (very low viral loads). This comparative experiment highlights that our assay bears clear advantages over the RT-qPCR in terms of ease of assay set up, ease of color detection, amenability to cell-phone imaging and no requirement of sophisticated equipment or technical training to interpret results. The full details of these comparisons are discussed in the manuscript.

This is consistent with the literature on COVID-19 diagnostics where new assays are routinely bench-marked against the “gold-standard” RT-qPCR assay ((Corman et al., 2020; Pearson et al., 2021).

What is the limit of detection of this assay using LacZ and Luciferase reporter respectively?

Response: The limit of detection of the assay as shown in Fig 4B and Fig 4C-D, was found to be 100 copies of RNA, which translates to a concentration of 8 attomolar RNA. In this case, we find the limit of detection to be the same for both LacZ (Fig 4B) and Luciferase (Fig 4C-D) reporter.

The calculations of copy number and sensitivity were made using a commercial source of synthetic CoV-2 RNA (Twist Biosciences) that is used in several studies about COVID-19 diagnostics (Joung et al., 2020; Rabe & Cepko, 2020; Wu et al., 2021). The RNA copy numbers are taken from the product details provided by the manufacturer. These details are now clearly stated in the manuscript. The commercial RNA is provided at 106 copies per ul. From this we take as low as 100 copies per 20ul of NASBA reaction, which we are able to detect using our assay. Hence our sensitivity comes to 8 attoMolar. We have clarified this in the manuscript. We noticed a typo in the original submission where we refer to a sensitivity of 80 attomolar in the Discussion. This is corrected to 8 attomolar. With this sensitivity we are within the range to detect RNA in patient samples, as confirmed by our patient data.

Authors have not examined the selectivity of this assay. What is the specificity, selectivity for each of these variants? Does altering target RNA change the specificity?

Response: We thank the reviewer for raising this point. As recommended by the reviewer, we have now examined the selectivity of this assay through new data (See new Fig S3, new Fig S4 and new Fig S8, also shown below).

We have examined selectivity in 3 different ways.

1. Is our sensor selective to the said region of the SARS-CoV-2 genome? To address this, we generated 19 different Target (Trigger) RNAs spread across the SARS-CoV-2 genome. These were tested against Sensor 12 to examine for their ability to trigger the sensor. We find that our sensor is highly selective for its target RNA and does not show any detectable response to the other regions of SARS-CoV-2 (see new Fig S3).

Next, we asked if our assay is selective to SARS-CoV-2 versus other related human corona viruses. For this, we first examined the sequence of the target RNA (Amplicon RNA 12) that is sensed by Sensor 12. We selected equivalent regions of RNA from a different coronavirus, the HKU1 human coronavirus family. We generated these RNA sequences in vitro and performed IVTT. These new data are shown in new Fig S4 and below. We find that the human coronavirus (HKU1) RNAs are not able to turn on our sensor, whereas the cognate SARS-CoV-2 RNA is able to.

We then asked if our assay can detect a current prominent variant of SARS-CoV-2. A major cause of concern is the ability of SARS-CoV-2 to accumulate mutations in its genome, resulting in different variant strains of SARS-CoV-2. Of these variants, the Delta variant (B.1.617.2) is not only highly contagious but has been noted as a possible vaccine breakthrough mutant of SARS-CoV-2. For this, we obtained RNA from the patient nasopharyngeal swab samples from the NCBS-inStem Covid-19 testing Center, Bangalore, India. RNA was isolated in the BSL-3 facility at the testing center. RNA samples were sequenced and confirmed to be the Delta variant- B.1.617.2 (sequences deposited in GASIAD). RNA extracted from these patient samples were tested against Sensor 12 using NASBA followed by IVTT. We find that our assay can efficiently detect the Delta variant SARS-CoV-2 RNA from patient samples with a build up of color, but no color was observed from control samples. These new data are shown below and in new Fig 5F and new Fig S8. The ability to detect the Delta variant of SARS-CoV-2 is an important feature of our sensor since this variant is now of global concern and extensively found in the population, even becoming the dominant variant in several countries (Callaway, 2021; O’Dowd, 2021; Torjesen, 2021).

In Figure 2C-F, sensor 17 showed higher fold change and sensitivity. Why was sensor 12 selected for further study in Figure 3

Response: The reviewer rightly notes that sensor 17 responds to 1012 copies of RNA and hence appears to be inherently more sensitive than sensor 12, which responds to 1013 copies of RNA. However, neither of these sensitivities are good enough to detect the levels of viral RNA found in patient samples. Hence we coupled these sensors with a step of NASBA amplification. The screen to identify pairs of NASBA primers gave us great hits for sensor 12 right off the bat, where we could detect down to 100 copies of RNA. Hence we moved forward with sensor 12 for further experiments. This has now been clarified in the manuscript.

Authors should show the error bar in all plots. Authors should also indicate what the error bar means (SD, S.E.M. etc.) throughout the manuscript.

Response: This is an important point. We have added the error bars and statistical analyses to all relevant plots. We have included the description of these statistical parameters in the figure legends throughout the manuscript, where relevant. Alternatively, experimental replicates are indicated and shown in the revised manuscript. Specifically in Figures 2 and 3 and 4D we have performed statistical analysis to include p-values to show significance of the data. For the data in Figure 4 B-C we include the experimental replicates as a new Supplementary Figure (see new Fig S5). Data in Figure S5 is now updated to include the experimental replicates. For the patient data in Figure 5, we have included details of specificity and sensitivity analysis for clinical samples (see new Fig 5C).

**Minor comments:**

"This method is relatively faster but may generate false positives due to non-specific amplification and primer interactions." Reference is needed.

Response: We have now added the following references in support of this statement. (Gadkar, Goldfarb, Gantt, & Tilley, 2018; Sahoo, Sethy, Mohapatra, & Panda, 2016)

"using the softwares Primer 3 and NUPACK." Reference is needed.

Response: We have now added the following references (Untergasser et al., 2012; Zadeh et al., 2011)

Reference 15 belongs to CRISPR-CAS based assay but it was cited under RT-LAMP assay.

Response: This has now been corrected. We thank reviewer for this.

Reviewer #1 (Significance (Required)):

This paper will be of interest to scientists interested in developing diagnostic tools for the detection of SARS-CoV2 in viral and host pathogenic sequences; genetic disorders and development of precision medicine.

Reviewer works in the field of Chemical Biology and Nanotechnology including sensor development and the application in diagnosis, cell physiological studies.

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

In this manuscript, Charkravarthy et al. report a new method for detecting SARS-CoV-2 RNA in both in vitro and human saliva and nasal samples. The new detection method, PHANTOM, is capable of detecting as few as 100 copies of the SARS-CoV-2 genome. The method is demonstrated to reproducible over a large range of viral titers and results in a binary report on CoV-2 infection. From my perspective the results are strong and fairly convincing (please see comments below). There is clear, logical, flow to the experiments and engineering of the PHANTOM system. The collaborative work is well organized and logical. The work is clearly of high significance and certainly merits expedited review and publication. I would like to unambiguously state that support publication of this manuscript in its current form in the non-peer reviewed context of this journal, would be more than happy to provide further peer review of this manuscript upon submission to another journal, and would be more than happy to provide further comments if requested by the authors.

My personal background is broad in range, however, I have a long track record of research in RNA folding, structural biology, biosensor development, and bioinformatics. Given this knowledge base, I found the manuscript rather easy to read and digest. The manuscript is well written and clear. In order to expedite the process of review I will not give a detailed review which would include grammatical errors (there are are very few). Rather, I will touch on the most pressing issues I see.

**Major concerns:**

1) There a number of figures that do not show a statistical measure of significance (e.g. error bears, ANOVA, etc.). It is essential that these be included in the final peer reviewed publication. (See Figure 2A, Figure 3D, Figure 4B, Figure 4C, Figure 5A, Figure 5C, Figure 5D).

Response: This is an important point. We have added the error bars and statistical analyses to all relevant plots. We have included the description of these statistical parameters in the figure legends throughout the manuscript, where relevant. Alternately, experimental replicates are indicated.

Specifically in Figures 2 and 3 and 4D we have performed statistical analysis to include p-values to show significance of the data. For the data in Figure 4 B-C we include the experimental replicates as a new Supplementary Figure (see new Fig S5). Data in Figure S5 is now updated to include the experimental replicates. For the data in Figure 5, we have included details of specificity and sensitivity analysis for clinical samples (see new Fig 5C).

2) There are some important points that do not include references within the manuscript. I believe that the authors should reference Abdolahzadeh et al. RNA 2019 in the introduction. This manuscript describes another NASBA viral detection system using fluorescent RNA reporters (also see Trachman et al. Q. Rev. Biophys 2019, for reference on fluorescent aptamers). Also see the ROSALIND method (Jung et al. 2020 Nature Biotechnology) for detecting water contaminants using visual identification by fluorescent aptamers.

Response: We have added the above mentioned references to the manuscript as suggested by the reviewer.

3) The discussion states that "The overall sensitivity in the attomolar range ensures detection of infection in the majority of Covid-positive patients in a population". Please provide a reference to support this and explicitly state the concentration of viral RNA in patient samples. There are a number of times that the copy number of viral genomes and sensitivity of the measurement is stated throughout the manuscript. There should also be a reference and statement about concentration.

Response: The reviewer has raised multiple connected points here, which we address in the revised manuscript.

1. Concentration of RNA in patient samples: We have added the references (Pujadas et al., 2020; Wyllie et al., 2020) where the authors report that the typical concentration of viral RNA in patient nasopharyngeal swab samples lies in the range of 104 to 105 copies of RNA per ml. This translates to a concentration range of 10 to 100 attoMolar. This reference is now added to the manuscript. For the patient samples used on our study, we refer to the Ct- values obtained from the RT-PCR tests and correlate Ct values to the readout from our assay, consistent with other reports on COVID-19 diagnostics ((Joung et al., 2020; Vogels et al. 2020; Wu et al., 2021).

Copy number and sensitivity: As the reviewer notes, we refer to viral genome copy number and sensitivity of our assay in the manuscript. These calculations of copy number and sensitivity were made using a commercial source of synthetic CoV-2 RNA (Twist Biosciences) that is used in several studies about COVID-19 diagnostics (Joung et al., 2020; Rabe & Cepko, 2020; Wu et al., 2021). The RNA copy numbers are taken from the product details provided by the manufacturer. These details are now clearly stated in the manuscript. The commercial RNA is provided at 106 copies per ul. From this, we take as low as 100 copies per 20ul of NASBA reaction, which we are able to detect using our assay. Hence our sensitivity comes to 8 attoMolar. We have clarified this in the manuscript. We noticed a typo in the original submission where we refer to a sensitivity of 80 attomolar in the Discussion. This is corrected to 8 attomolar. With this sensitivity we are within the range to detect RNA in patient samples, as confirmed by our patient data.

Reviewer #3 (Significance (Required)):

I think this is a significant advancement in the field. The introduction of smartphone technology to this robust diagnostic is very attractive. The work is of high significance since the researchers demonstrated robust responses against SARS-CoV-2 variants. As well all now know these are on the rise and cheap robust detection methods are essential for containing this virus.

Response: We thank the reviewers for the positive comments.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Charkravarthy et al. report a new method for detecting SARS-CoV-2 RNA in both in vitro and human saliva and nasal samples. The new detection method, PHANTOM, is capable of detecting as few as 100 copies of the SARS-CoV-2 genome. The method is demonstrated to reproducible over a large range of viral titers and results in a binary report on CoV-2 infection. From my perspective the results are strong and fairly convincing (please see comments below). There is clear, logical, flow to the experiments and engineering of the PHANTOM system. The collaborative work is well organized and logical. The work is clearly of high significance and certainly merits expedited review and publication. I would like to unambiguously state that support publication of this manuscript in its current form in the non-peer reviewed context of this journal, would be more than happy to provide further peer review of this manuscript upon submission to another journal, and would be more than happy to provide further comments if requested by the authors.

My personal background is broad in range, however, I have a long track record of research in RNA folding, structural biology, biosensor development, and bioinformatics. Given this knowledge base, I found the manuscript rather easy to read and digest. The manuscript is well written and clear. In order to expedite the process of review I will not give a detailed review which would include grammatical errors (there are are very few). Rather, I will touch on the most pressing issues I see.

Major concerns:

1) There a number of figures that do not show a statistical measure of significance (e.g. error bears, ANOVA, etc.). It is essential that these be included in the final peer reviewed publication. (See Figure 2A, Figure 3D, Figure 4B, Figure 4C, Figure 5A, Figure 5C, Figure 5D).

2) There are some important points that do not include references within the manuscript. I believe that the authors should reference Abdolahzadeh et al. RNA 2019 in the introduction. This manuscript describes another NASBA viral detection system using fluorescent RNA reporters (also see Trachman et al. Q. Rev. Biophys 2019, for reference on fluorescent aptamers). Also see the ROSALIND method (Jung et al. 2020 Nature Biotechnology) for detecting water contaminants using visual identification by fluorescent aptamers.

3) The discussion states that "The overall sensitivity in the attomolar range ensures detection of infection in the majority of Covid-positive patients in a population". Please provide a reference to support this and explicitly state the concentration of viral RNA in patient samples. There are number of times that the copy number of viral genomes and sensitivity of the measurement is stated throughout the manuscript. There should also be a reference and statement about concentration.

Significance

I think this is a significant advancement in the field. The introduction of smart phone technology to this robust diagnostic is very attractive. The work is of high significance since the researchers demonstrated robust reposes against SARS-CoV-2 variants. As well all now know these are on the rise and cheap robust detection methods are essential for containing this virus.

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 project, authors develop a colorimetric and luminescence assay for the detection of SARS-CoV-2 RNA in vitro. They design an RNA based sensor that will be triggered by target RNA then release the ribosome binding site and a translation start site followed by a reporter gene. The released sequence will then trigger the production of reporter protein by transcription-translation coupled assay. Authors also introduce an RNA amplification step in order to increase the sensitivity of this assay.

Strengths:

This assay provides a simple, rapid way to detect SARS-CoV2 and it is an elegant way to incorporate transcription-translation coupled assay for SARS-CoV-2 RNA detection and identify SARS-CoV-2 patient samples. It is a nice assay and the performance is comparable with the existing method.

Weaknesses:

However, the positioning of this assay is not very clear. The readout of this assay could be recorded by camera whereas it includes several steps such as RNA extraction, amplification, transcription-translation coupled assay and reporter reaction. The limitations of the existing methods (RT-PCR, paper strip) and the advantages of this assay haven't been demonstrated by the experiments. The stability of RNA may also restrict the application of the proposed assay on site.

Major comments:

Authors are suggested to design an experiment to show the advantage of this assay compared with the existing method.

What is the limit of detection of this assay using LacZ and Luciferase reporter respectively?

Authors have not examined the selectivity of this assay. What is the specificity, selectivity for each of these variants? Do altering target RNA change the specificity?

In Figure 2C-F, sensor 17 showed higher fold change and sensitivity. Why was sensor 12 selected for further study in Figure 3?

Authors should show the error bar in all plots. Authors should also indicate what the error bar means (SD, S.E.M. etc.) throughout the manuscript.

Minor comments:

"This method is relatively faster but may generate false positives due to non-specific amplification and primer interactions." "using the softwares Primer 3 and NUPACK." Reference is needed.

Reference 15 belongs to CRISPR-CAS based assay but it was cited under RT-LAMP assay.

Significance

This paper will be of interest to scientists interested in developing diagnostic tools for the detection of SARS-CoV2 in viral and host pathogenic sequences; genetic disorders and development of precision medicine.

Reviewer works in the field of Chemical Biology and Nanotechnology including sensor development and the application in diagnosis, cell physiological studies.

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• authors' reply
• editorial decisions

</br>

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Reply to the reviewers

Responses to reviewers’ comments

We thank the reviewers for their encouraging comments and helpful suggestions.

Reviewer #1

(Evidence, reproducibility and clarity (Required)):

Sanchez et al report several new findings about the adhesive protrusions on Plasmodium falciparum infected erythrocytes. Using super resolution microscopy and correlation analysis, they tracked associations between the knob protein KAHRP and erythrocyte membrane cytoskeleton proteins. They have expanded on and improved previous work on the unusual spiral structure of the knobs, which appears to be a spiral ribbon or blade and have shown a developmental pathway for the association of KAHRP with the cytoskeleton. They have localised KAHRP close to the spiral and determined its abundance in the knobs. They have also used cryo electron tomography and subtomogram averaging to get an improved 3D view of the knob structure.

The work appears to be carefully and thoroughly done, and the paper is clearly written, though non specialists in the optical methods may find it challenging to navigate through the many super resolution images and correlation plots.

Comment 1: The writing needs minor editing to fix a variety of small linguistic errors and typos. For example, line 97 "sideway positions" (they presumably mean lateral location), line 980 typo overlay, line 366 "then could reorganizes", line 435, "a predict volume".

We apologize for the linguistic errors and typos. These have been corrected in the revised manuscript.

(Significance (Required)):

Comment 2: The study provides a distinct advance on the previous state of knowledge of the structure and biochemistry of the knobs. The knobs play a key role in virulence of P. falciparum and they are quite poorly understood. Although this paper does not represent a major breakthrough in determining the molecular structure or mechanistic role of the knobs, e.g. the biochemical identity of the spiral remains unknown, the new information is valuable and likely to be important in understanding the pathogenic actions of P falciparum.

We thank the reviewer for appreciating the importance of our study. We believe that our first-time observations on the dynamics of KAHRP are a very important advance in the field and that revealing the mechanistic basis is a great challenge that at the current stage has to be left to future work.

Comment 3: The interpretation shown in Figure 7 seems fine, except for the proposal that the actin cytoskeleton is reorganised. There is no evidence for that. The cryo tomograms of the cytoskeleton in Watermeyer et al addressed this point and did not find any evidence for reorganisation of the cytoskeleton other than the insertion of the knobs.

In two previous studies we could show that actin is indeed reorganized by the parasite. It is mined from the protofilaments to generate long actin filaments that connect the knobs with the Maurer’s clefts and which are used for trafficking of cargo vesicles from the Maurer’s clefts to the erythrocyte plasma membrane (Cyklaff et al. Hemoglobins S and C interfere with actin remodeling in Plasmodium falciparum-infected erythrocytes. Science. 2011 334:1283-1286; Cyrklaff et al. Oxidative insult can induce malaria-protective trait of sickle and fetal erythrocytes. Nat Commun. 2016 7:13401). Moreover, a life-cycle resolved AFM-study of the cytoplasmic side of iRBCs by the group of CT Lim has demonstrated dramatic coarsening of the spectrin network, which must be accompanied by changes to the actin component of the skeleton (Shi, Hui, et al. "Life cycle-dependent cytoskeletal modifications in Plasmodium falciparum infected erythrocytes." PLoS One 8.4 (2013): e61170). Coarsening of the actin-spectrin network would imply a decrease of the amount of actin in the network, which is consistent with its use in the parasite-derived long actin filaments.

\*Referee Cross-commenting***

I also agree with the other 2.

Reviewer #2

(Evidence, reproducibility and clarity (Required)):

Malaria parasites replicate within circulating red blood cells (RBC). During parasite maturation, the parasite coordinates extensive modification of the host cell, including structural modifications of the RBC cytoskeleton and surface membrane. These host cell alterations play crucial roles in the pathology of malaria, including vascular adhesion by parasitised cells and avoidance of splenic clearance, and so are of great interest. This interesting manuscript describes a detailed examination of the role in these RBC modifications of a well-described parasite protein called KAHRP. Using a combination of cutting-edge super-resolution microscopy, cryo-electron tomography, immuno-EM, SEM and parasite mutagenesis, the authors provide evidence that KHARP localisation alters during parasite maturation but eventually becomes closely associated with the previously-described spiral structures that underlie infected RBC surface membrane protrusions called knobs. The authors provide improved resolution of the spiral formations, generate a quantitative estimate of the number of KAHRP molecules per knob, and provide a model for the role of KAHRP in attaching other proteins to the spirals based on their observations.

In general, this study is thorough and well-performed, and the conclusions drawn are well-supported by the data. Although the work does not advance understanding of knob function or the parasite components that form the bulk of the spirals, it provides an interesting and useful contribution to understanding of the manner in which this important pathogen manipulates its host cell.

We thank the reviewer for appreciating the importance of our study and in acknowledging that it is an important intermediate step towards a complete understanding of skeleton remodelling by the parasite.

I have just a few minor suggestions that should improve the manuscript.

Comment 1: Line 91 (Page 2 paragraph 2). It would be greatly helpful here if the authors could provide a more detailed background on the makeup of the RBC cytoskeleton, and in particular the interactions between beta-spectrin and the actin protofilaments of the junctional complexes. The authors should make it clear that the actin-binding domain of beta-spectrin comprises 2 calponin like domains, and that these are attached to the end of the tandem spectrin repeat domains that make up the bulk of the molecule.

We thank the reviewer for this helpful suggestion and have added a new paragraph to the results section providing detailed background information on the makeup of the RBC membrane skeleton. The new text reads as follows:

“Major components of the red blood cell membrane skeleton are spectrin and actin filaments (Fig. 1B). The spectrin filaments consist of α- and ß-spectrin, which form α2ß2 heterotetramers by head-to-head association of two αß dimers (Lux, 2016; Machnicka et al., 2014). The N-termini of the ß-spectrin subunits are positioned at the tail ends of the heterotetramer and contain two calponin homology (CH) domains for binding to actin protofilaments consisting of 6 to 8 actin monomers in each of the two strands (Lux, 2016; Machnicka et al., 2014). Protein 4.1R strengthens the spectrin actin interaction (Lux, 2016; Machnicka et al., 2014). Groups of up to six spectrin heterotetramers can attach to an actin protofilaments, resulting in a pseudohexagonal meshwork (Lux, 2016). Ankyrin binds to the C-terminal domain of ß-spectrin and connects integral membrane proteins with the actin spectrin network in an ankyrin complex (Lux, 2016; Machnicka et al., 2014).”

Comment 2: Line 97 "These values are slightly larger than the reported physical dimension of the protofilament...". Please provide these reported dimensions here, as well as relevant references.

The requested information is now provided. The sentence now reads as follows:

“These values are slightly larger than the reported physical dimension of the protofilaments of ~37 nm (Lux, 2016) and might be explained by the lateral localization of the spectrin binding sites and the additional sizes of the primary and secondary antibody trees used to detect the two targets.”

Comment 3: Line 366 "reorganize"

The spelling mistake has been corrected.

(Significance (Required)):

Comment 4: This is a useful technical advance in understanding of the structure of the P. falciparum-infected red blood cell, and builds on the work of Watermeyer et al. (2016). The study should certainly be of interest to most malaria researchers, particularly those interested in the pathobiology of the organism.

We thank the reviewer for supporting our study.

\*Referee Cross-commenting***

I fully agree with and endorse the comments of the other 2 reviewers.

Reviewer #3

(Evidence, reproducibility and clarity (Required)):

The binding of P. falciparum infected erythrocyte (iRBCs) to the endothelium is mediated by protuberances (knobs). These knobs are assembled by a multi-protein complex at the iRBC surface. It acts as a scaffold for the presentation of the major virulence antigen, P. falciparum Erythrocyte Membrane Protein-1 (PfEMP1). The knob-associated histidine-rich protein (KAHRP) is an essential component of the knobs and therefore essential for the binding of iRBC to the endothelium under physiological conditions. This manuscript focusses on the knob architecture and KAHRP localization.

Comment 1: It is, at least for this reviewer - hard to assess how the "preparation of exposed membranes by hypotonic shock" and the analysis of the "inverted erythrocyte membrane ghosts" is i) reflective of the physiological architecture within the iRBC and ii) how the authors exclude remnants from Maurers clefts (MCs) in their preparation. The latter appears especially important for the interpretation of dynamic KAHRP repositioning, as MCs are mobile in early stages and non-mobile later on (e.g. McMilian et al. 2013, Grüring et al. 2011) and the authors observed at least some MAHRP1 signal (Figure S8), which is hard to interpret by the single representative image provided.

We understand the reviewer’s concerns, but are convinced that we have done the necessary controls to evaluate our approaches. For example, we evaluated the exposed membrane approach by investigating uninfected erythrocytes and comparing the findings with literature reports (see Figure 1). A high degree of agreement was observed. We further would like to point out that the exposed membrane approach has been successfully used by several other studies referenced in the manuscript (Dearnley et al., 2016; Looker et al., 2019; Shi et al., 2013). Please also allow us to explain why we have used exposed membranes instead of whole cells. The reason is that the hemozoin produced by the parasite interferes with STED microscopy, resulting in a quick and strong build-up of resonance energy in the specimen and, eventually, in the disruption of the cell.

With regard to the question of whether remnants of Maurer’s clefts are present in our preparations, we do not think so, at least we never observed membrane profiles reminiscent of Maurer’s clefts in SEM images of exposed membranes (see figure at the end of the response letter). Irrespectively, we will double check this result using STED imaging of exposed membranes treated with an antibody against the established Maurer’s clefts marker SBP1. These data could be added to a revised manuscript.

Comment 2: line 173: Please provide a detailed description about parasite synchronization (also absent in the methods section).

A detailed description including references are now added to the methods section:

“For synchronization of cultures, schizont-infected erythrocytes were sterile purified using a strong magnet (VarioMACS, Miltenyi Biotec) (Staalsoe et al., 1999) and mixed with fresh erythrocytes to high parasitaemia. 5000 heparin units (Heparin-sodium 25000, Ratiopharm) were added and the cells were returned to culture for 4 hrs (Boyle et al., 2010). Following the treatment with heparin, cells were washed with pre-warmed supplemented RMPI 1640 medium and then returned to culture for 2 hrs to allow for re-invasion of erythrocytes. Subsequently, cells were treated with 5% sorbitol to remove late parasite stages (Lambros and Vanderberg, 1979).”

Comment 3: line 136: Please re-check nomenclature of "PHIS1605w" (mixed nomenclature used throughout the manuscript). I suggest to use either LyMP or the up-to-date ID PF3D7_0532400.

We apologize for the oversight and now consistently use the ID PF3D7_0532400.

Comment 4: Please provide source and references for PfEMP1, MAHRP1 and "PHIS1605w" antibodies that are used. I cannot find them in the methods section or in Table S1.

We apologize for the oversight and now provide the requested information in the amended Table S1.

Comment 5: line 165: Warncke et al. (2016) appears to be misplaced as an appropriate MAHRP1 reference.

We now cite the original MAHRP1 publication by Spycher et al. 2003.

Comment 6: line 159: the sentence "The strong cross-correlation between KAHRP and actin is consistent with previous cryo-electron tomographic analysis showing long actin filaments connecting the knobs with Maurer's clefts in trophozoites (Cyrklaff et al., 2012; Cyrklaff et al., 2011; Cyrklaff et al., 2016)" could be moved to the discussion section.

The sentence was indeed redundant with a section in the discussion and was removed.

Comment 7: line 199: The text refers to Fig. 9AB - but should refer to 4AB or suppl. 11.

We are sorry for this mistake and now refer to the correct figures in the revised manuscript.

Comment 8: Fig. 4: A solid average for the number of subtomograms, but please provide information about what the arrowheads (4E) indicate.

Thank you for this comment. The arrowheads indicate peripheral crown-like densities. We have updated the figure legend to clarify this issue.

Comment 9: The "flexible periphery" is likely a combination of flexibility and occupancy as the average was made from subtomograms with varying number of turns in the spiral. As occupancy is likely a significant contributing factor to the average that should be discussed or at least mentioned.

Thank you for this important comment. Indeed, a significant variation was observed between the individual knobs. The spirals have variable diameter, and the number of peripheral proteins also varied. We added measurements to the supplementary figure 11D. In addition, we update the text and extended the discussion.

Comment 10. On that note, did the authors try and classify based on number of turns prior to averaging and if so did the authors see any differences in structures between few turn and many turn spirals?

We attempted several classifications on the full knobs with variable masks. However due to a limited number of particles in the dataset we could not converge to stable solutions. Instead, we decided to adopt the subboxing strategy where locally ordered segments at the periphery could be analyzed. This showed several structural snapshot at the periphery of the knobs.

Comment 11. What size mask was used? Was it a soft sphere around the core or big enough for the knobs with multiple spiral turns?

While we attempted several alignments and classifications with variable masks, the final refinement and measurement of FSC was performed with a soft contour mask mask. We overlaid it with the structure in Figure S11F and uploaded it as a part of the EMDB deposition. We further show the masks used in this study in a new Figure S14.

Comment 12. It might be useful for readers who are not familiar with Dynamo to provide a little bit more information about how the initial reference was produced. Additionally more information about the sub-boxing strategy ie: spacing etc. would helpful.

Thank you very much for the suggestion. For the initial reference we manually aligned all the particles, summed them up and low-pass filtered them. We now describe it in the methods section.

For the subboxing procedure we added more description to the main text:

“40 segments were extracted at the radius of the 2nd and 3rd spirals followed by their classification into structural classes.”

We further extended and simplified the description in the results section (line ~221).

Comment 13: Fig. 5 Additional (earlier) maturation stages of the iRBC with Ni2+NAT-gold-labelling would be a nice add on - this could help confirm the model and would itself be a control for the later stage labelling.

We thank the reviewer for this insightful suggestion. We are currently performing the proposed experiment and will include it in a revised version of the manuscript.

Comment 14: line 637: DMSI typo and please provide the supplier for DMSI (DSM1).

We corrected the typographic error and now provide the name of the supplier.

Comment 15: Figure 7: Please provide what the purple arrows indicate.

The figure legend has been updated.

Comment 16: Fig S11D: The labels X, Y and Z are confusing, describing the slicing axis as "XZ, YZ and XY" view is more intuitive.

Done as suggested by the reviewer.

Comment 17: Figure S13 B: WBs are cropped. Please provide un-cropped WB.

Uncropped Western blots will be provided in the revised manuscript.

(Significance (Required)):

In general, I highly appreciated the solid data and its thorough analysis of the microscopy data. The authors investigate the structural organization of knobs in iRBCs using high-resolution imaging techniques including STED and PALM super-resolution microscopy-based approaches and electron tomography. The beauty of this paper is that it does nicely re-investigate knob architecture in iRBC (e.g. Watermeyer et al., 2016, Cutts et al., 2017, Looker et al., 2019, McHugh et al., 2020) and provides some intriguing KHARP co-localization with cytoskeleton components. The downside of it is that - by nature - it is descriptive (and the data rather confirmative) and as it stands does not provide us with a deeper molecular dissection of the knob associated structure and its cellular function.

We thank the reviewer for appreciating our study and would like to emphasize the following novelties in our study:

• We show that the association of KAHRP with membrane skeletal components is highly dynamic and changes as the parasite matures. Our results on the dynamics of KAHRP organization reconciles conflicting reports in the literature, and establish for the first time a dynamical model for KAHRP organization.
• We further show that KAHRP finally assembles at remnant actin-junctional complexes devoid of the actin-capping factors adducin and tropomodulin.
• We further quantified the number of KAHRP molecules per knob and show that KAHRP is present as 60 copies per knob, a number one order of magnitude greater than previously thought.
• Last but not least, we provide a 35 Å map of the spiral scaffold underlaying knobs and show that KAHRP associates with the spiral scaffold.

• We conclude by providing a novel model on the biological function of KAHRP by proposing that KAHRP acts as a glue that connects spectrin and parasite-remodeled actin filaments with the knob spiral.

  \*Referee Cross-commenting***

Fully agreed.

Boyle, M.J., Wilson, D.W., Richards, J.S., Riglar, D.T., Tetteh, K.K., Conway, D.J., Ralph, S.A., Baum, J., and Beeson, J.G. (2010). Isolation of viable Plasmodium falciparum merozoites to define erythrocyte invasion events and advance vaccine and drug development. Proc Natl Acad Sci U S A 107, 14378-14383.

Lambros, C., and Vanderberg, J.P. (1979). Synchronization of Plasmodium falciparum erythrocytic stages in culture. J Parasitol 65, 418-420.

Lux, S.E.t. (2016). Anatomy of the red cell membrane skeleton: unanswered questions. Blood 127, 187-199.

Staalsoe, T., Giha, H.A., Dodoo, D., Theander, T.G., and Hviid, L. (1999). Detection of antibodies to variant antigens on Plasmodium falciparum-infected erythrocytes by flow cytometry. Cytometry 35, 329-336.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The binding of P. falciparum infected erythrocyte (iRBCs) to the endothelium is mediated by protuberances (knobs). These knobs are assembled by a multi-protein complex at the iRBC surface. It acts as a scaffold for the presentation of the major virulence antigen, P. falciparum Erythrocyte Membrane Protein-1 (PfEMP1). The knob-associated histidine-rich protein (KAHRP) is an essential component of the knobs and therefore essential for the binding of iRBC to the endothelium under physiological conditions. This manuscript focusses on the knob architecture and KAHRP localization.

General point:

It is, at least for this reviewer - hard to assess how the "preparation of exposed membranes by hypotonic shock" and the analysis of the "inverted erythrocyte membrane ghosts" is i) reflective of the physiological architecture within the iRBC and ii) how the authors exclude remnants from Maurers clefts (MCs) in their preparation. The latter appears especially important for the interpretation of dynamic KAHRP repositioning, as MCs are mobile in early stages and non-mobile later on (e.g. McMilian et al. 2013, Grüring et al. 2011) and the authors observed at least some MAHRP1 signal (Figure S8), which is hard to interpret by the single representative image provided.

Specific points:

• line 173: Please provide a detailed description about parasite synchronization (also absent in the methods section)
• line 136: Please re-check nomenclature of "PHIS1605w" (mixed nomenclature used throughout the manuscript). I suggest to use either LyMP or the up-to-date ID PF3D7_0532400.
• Please provide source and references for PfEMP1, MAHRP1 and "PHIS1605w" antibodies that are used. I cannot find them in the methods section or in Table S1 -line 165: Warncke et al. (2016) appears to be misplaced as an appropriate MAHRP1 reference.
• line 159: the sentence "The strong cross-correlation between KAHRP and actin is consistent with previous cryo-electron tomographic analysis showing long actin filaments connecting the knobs with Maurer's clefts in trophozoites (Cyrklaff et al., 2012; Cyrklaff et al., 2011; Cyrklaff et al., 2016)" could be moved to the discussion section
• line 199: The text refers to Fig. 9AB - but should refer to 4AB or suppl. 11.
• Fig. 4: A solid average for the number of subtomograms, but please provide information about what the arrowheads (4E) indicate. A few additional comments on this section:

1: The "flexible periphery" is likely a combination of flexibility and occupancy as the average was made from subtomograms with varying number of turns in the spiral. As occupancy is likely a significant contributing factor to the average that should be discussed or at least mentioned.

1. On that note, did the authors try and classify based on number of turns prior to averaging and if so did the authors see any differences in structures between few turn and many turn spirals?
2. What size mask was used? Was it a soft sphere around the core or big enough for the knobs with multiple spiral turns?
3. It might be useful for readers who are not familiar with Dynamo to provide a little bit more information about how the initial reference was produced. Additionally more information about the sub-boxing strategy ie: spacing etc. would helpful.

• Fig. 5 Additional (earlier) maturation stages of the iRBC with Ni2+NAT-gold-labelling would be a nice add on - this could help confirm the model and would itself be a control for the later stage labelling.
• line 637: DMSI typo and please provide the supplier for DMSI (DSM1).
• Figure 7: Please provide what the purple arrows indicate.
• Fig S11D: The labels X, Y and Z are confusing, describing the slicing axis as "XZ, YZ and XY" view is more intuitive.
• Figure S13 B: WBs are cropped. Please provide un-cropped WB.

Significance

In general, I highly appreciated the solid data and its thorough analysis of the microscopy data. The authors investigate the structural organization of knobs in iRBCs using high-resolution imaging techniques including STED and PALM super-resolution microscopy-based approaches and electron tomography. The beauty of this paper is that it does nicely re-investigate knob architecture in iRBC (e.g. Watermeyer et al., 2016, Cutts et al., 2017, Looker et al., 2019, McHugh et al., 2020) and provides some intriguing KHARP co-localization with cytoskeleton components. The downside of it is that - by nature - it is descriptive (and the data rather confirmative) and as it stands does not provide us with a deeper molecular dissection of the knob associated structure and its cellular function.

Referee Cross-commenting

Fully agreed.

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Referee #2

Evidence, reproducibility and clarity

Malaria parasites replicate within circulating red blood cells (RBC). During parasite maturation, the parasite coordinates extensive modification of the host cell, including structural modifications of the RBC cytoskeleton and surface membrane. These host cell alterations play crucial roles in the pathology of malaria, including vascular adhesion by parasitised cells and avoidance of splenic clearance, and so are of great interest. This interesting manuscript describes a detailed examination of the role in these RBC modifications of a well-described parasite protein called KAHRP. Using a combination of cutting-edge super-resolution microscopy, cryo-electron tomography, immuno-EM, SEM and parasite mutagenesis, the authors provide evidence that KHARP localisation alters during parasite maturation but eventually becomes closely associated with the previously-described spiral structures that underlie infected RBC surface membrane protrusions called knobs. The authors provide improved resolution of the spiral formations, generate a quantitative estimate of the number of KAHRP molecules per knob, and provide a model for the role of KAHRP in attaching other proteins to the spirals based on their observations. In general, this study is thorough and well-performed, and the conclusions drawn are well-supported by the data. Although the work does not advance understanding of knob function or the parasite components that form the bulk of the spirals, it provides an interesting and useful contribution to understanding of the manner in which this important pathogen manipulates its host cell.

I have just a few minor suggestions that should improve the manuscript.

Line 91 (Page 2 paragraph 2). It would be greatly helpful here if the authors could provide a more detailed background on the makeup of the RBC cytoskeleton, and in particular the interactions between beta-spectrin and the actin protofilaments of the junctional complexes. The authors should make it clear that the actin-binding domain of beta-spectrin comprises 2 calponin like domains, and that these are attached to the end of the tandem spectrin repeat domains that make up the bulk of the molecule.

Line 97 "These values are slightly larger than the reported physical dimension of the protofilament...". Please provide these reported dimensions here, as well as relevant references.

Line 366 "reorganize"

Significance

This is a useful technical advance in understanding of the structure of the P. falciparum-infected red blood cell, and builds on the work of Watermeyer et al. (2016). The study should certainly be of interest to most malaria researchers, particularly those interested in the pathobiology of the organism.

Referee Cross-commenting

I fully agree with and endorse the comments of the other 2 reviewers.

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Referee #1

Evidence, reproducibility and clarity

Sanchez et al report several new findings about the adhesive protrusions on Plasmodium falciparum infected erythrocytes. Using super resolution microscopy and correlation analysis, they tracked associations between the knob protein KAHRP and erythrocyte membrane cytoskeleton proteins. They have expanded on and improved previous work on the unusual spiral structure of the knobs, which appears to be a spiral ribbon or blade) and have shown a developmental pathway for the association of KAHRP with the cytoskeleton. They have localised KAHRP close to the spiral and determined its abundance in the knobs.

They have also used cryo electron tomography and subtomogram averaging to get an improved 3D view of the knob structure.

The work appears to be carefully and thoroughly done, and the paper is clearly written, though non specialists in the optical methods may find it challenging to navigate through the many super resolution images and correlation plots. The writing needs minor editing to fix a variety of small linguistic errors and typos. For example, line 97 "sideway positions" (they presumably mean lateral location), line 980 typo overlay, line 366 "then could reorganizes", line 435, "a predict volume".

Significance

The study provides a distinct advance on the previous state of knowledge of the structure and biochemistry of the knobs. The knobs play a key role in virulence of P. falciparum and they are quite poorly understood. Although this paper does not represent a major breakthrough in determining the molecular structure or mechanistic role of the knobs, e.g. the biochemical identity of the spiral remains unknown, the new information is valuable and likely to be important in understanding the pathogenic actions of P falciparum.

The interpretation shown in Figure 7 seems fine, except for the proposal that the actin cytoskeleton is reorganised. There is no evidence for that. The cryo tomograms of the cytoskeleton in Watermeyer et al addressed this point and did not find any evidence for reorganisation of the cytoskeleton other than the insertion of the knobs.

I am generally familiar with the area of this work, but not expert in the details of the optical methods and localisation analysis.

Referee Cross-commenting

I also agree with the other 2.

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Reply to the reviewers

Dear Editor,

We appreciate the critical and constructive comments that Reviewers made on our paper entitled “The structure and flexibility analysis of the Arabidopsis Synaptotagmin 1 reveal the basis of its regulation at membrane contact sites” by Benavente et al.. We are very pleased that three reviewers from Review commons appreciated the work, found it interesting and suggested constructive modifications to the paper. We have now responded to their suggestions and enclose a modified manuscript.

As suggested by the reviewers we now provide additional biochemical evidence about the role of calcium on C2 activation, more controls in the biochemical assays, an improved protocol for the lipid binding assays as well as details in the molecular dynamics. In addition, following reviewers’ recommendations, we have rephrased some of the headings and statements in the discussion section, to adjust them better to our experimental results. Altogether, we believe that the manuscript is more solid and interesting than the previous version for the general readers of eLife.

Specifically, we have made the following changes in response to the particular comments of the referees:

Reviewer 1

Major points

The conclusion that SYT1C2A determines protein behavior by binding calcium and likely switching its function from a pure tether to a lipid transporter is accurately and convincingly portrayed. However, there are some problematic statements in the way this information is interpreted and used to propose a model.

• • p7: "This means that site I will be occupied depending on the physiological Ca2+ concentration to activate the protein and trigger Ca2+-dependent SYT1C2A lipid binding." Please exchange "means" by "suggests"* We agree with the reviewer and we have exchanged “means” by “suggests”
• • There is not enough data to determine whether SYT1C2A interacts with the SYT1SMP domain, much less to propose that it is the SYTC2A that loads the SMP with DAG. They may also operate independently by means of the unstructured hinge sequence between them. *
• • It is implied that SYTC2A would have to release its calcium atom for it to leave the PM and go to the ER to complete a single transport cycle. It is unclear whether SYT1C2A could bind and release calcium repeatedly and fast enough to cycle between membranes efficiently. It appears more plausible for it to remain at the PM until intracellular calcium concentrations decrease. **

  These statements should be marked as speculative. *

We understand that the reviewer comments are related to steps 3 and 4 of our model for the function of SYT1 (figure7; pages 17 and 18). We have now included these scenarios suggested by the reviewer (page 17 and 18). In addition, we have discussed the work from Vennekate et al, PNAS, 2012, related to the cis and trans membrane interactions of the two C2 domains of human synaptotagmin (Syt1). The authors demonstrated that they are driven by the balance in the concentration of anionic lipids between target membranes and by Ca2+ and protein concentration. Likewise, the changes in the local composition of PIP and/or Ca2+ may drive the transfer of SYT1C2A from the PM to de ER and vice versa while the C2B remains at the PM.

Most of the graphs shown (except Fig. 4A) appear to show only one experiment. Please include results from at least three independent experiments in all graphs, and analyze them statistically. Please describe only differences between samples that are statistically significant (for all graphs and tables).

Following reviewed recommendation, we have assured that all the biochemical data arises from three independent measurements. Indeed, as indicated in the figure legends and methods section, this was the case for the Ca2+ binding experiments at figure 2C and for the lipid binding data at figure 4. We have now repeated the ITC experiments to provide three independent measurements of the dissociation constant of SYT1C2A for Ca2+.

Minor comments

Please include the PDB codes for the available structures used. It is not clear where the C2C domain structure comes from. We guess it may correspond to PDB entry 2DMG. A word of caution, this 2006 structure has been released but not published and its quality is suboptimal. After its appearance in Idevall-Hagren et al. 2015 supplementary images it has been re-cited in other publications. I would advise against making topology claims based on this structure (Figure S1), and only use it as an example for polybasic patches in C2 domains.

We have included the PDB codes for the available structures used at the corresponding figure captions 1, 3 and S1.

We agree that the stereochemistry of the refined structure of the E-Syt2 C2C domains (2DMG) is suboptimal. However, we have sought for the advice of an NMR expert (M.A. Jimenez, https://scholar.google.es/citations?hl=es&user=iAF0ymYAAAAJ) to evaluate the NMR restrains available alongside the entry at PDB. She concluded that the Halpha-Halpha distance restrains indicate that the connectivity of the beta strands is correct. The confusion may arise from the fact that the PDB entry has been updated twice since 2006, the last one in 2011.

• • p4: Schauder et al. 2014. Only the "shuttle" model is mentioned in the text. Although this may be the most plausible scenario, the "tunnel" model cannot be completely ruled out*. We have now stated that both shuttle or tunnel modes are possible for lipid transfer at page 4.
• • p5: Fernandez-Busnadiego et al. 2015 does not make a reference to the claim in the text.* Fernandez-Busnadiego et al. 2015 has been replaced by Collado et. al 2019
• • p18: Collado et. al 2019 don't assign the peak-forming function to the N-terminal hairpin domain of tricalbins. As the reviewer indicates, Collado et. al 2019 just suggests that the peak forming function could be due to the N-terminal hairpin domain of tricalbins: “This phenomenon may rely on the hairpin sequence that anchors Tcbs to the ER membrane. Tcb hairpin sequences could sense and/or generate membrane curvature as in reticulons and other ER morphogenetic proteins (Hu et al., 2011).” (Taken from Collado et al. 2019).*

Accordingly, we have indicated that “It has been suggested that the insertion of the N-terminal hydrophobic end of Tcbs may induce the formation of peaks of strong curvature at the ER region facing the PM. These structures shorten the distance between the ER and the PM by ~7 nm and facilitate lipid transport (Collado et al., 2019)”

Fig. 1A: the notation for the domains C2C-C2E of E-Syt1 is confusing and not described in the legend. Also, please mark which beta sheet is which more clearly in Fig 1B, it is very difficult to understand the labelling** Fig. 1C: several elements (e.g. types of boxes, "T" on the top) used in the figure are not described in the legend. Both beta sheets and mutations are described as "arrows" in the legend, please differentiate between vertical and horizontal.

We have modified the Fig. 1A legend to explain the notation of C2 domains of human E-Syts “Human E-Syt1 displays five C2 domains while E-Syt2 and E-Syt3 display three”.

Labeling of beta strands has been modified to make the panel clearer.

We have rewritten the caption of figure 1C to describe the types of boxes and the “T” and to distinguish between vertical and horizontal arrows.

Fig. 2A: indicate Lys 286, which is mentioned in the text

The reference to Lys 286 in the text was not correct. We have modified the text to indicate that Lys275 replaces the Ca I as it is shown in figure 2.

Fig. 2B: Inset too small to read.

Labels for inset at Fig 2B have been enlarged.

Fig. 3: please show the scale and explain the blue-red color code. Please mark the polybasic patch.

We have explained the meaning of the blue and red code, marked the polybasic patch of SYT1C2A and E-Syt1C2C and indicated that all of them are scaled to the same value.

Fig. 4A should show both mutants for both types of liposomes.

We have included new liposome binding data including both mutants for both types of liposomes.

Table 1: what is "control"?

We have indicated that the unbound wild-type protein is taken as a control

Fig. S5: Difficult to read, increase font size. The text talks about experiments with calcium and EGTA that are not shown in the figure.

We have increased figure size to facilitate reading. We have also indicated that C2AB-Ca and C2A stand for the experiments carried out in presence of Ca and EGTA, respectively.

Reviewer 2

Minor comments

Typos: please re-read carefully through the manuscript to remove them. We advise the authors to have the manuscript corrected by a native english-speaker.

We have done a thorough revision of the manuscript to correct typos and to improve the English style of the manuscript

Reviewer 2 considers that “The authors discuss their findings within the frame of experimental observations that are already published but these remain speculative”

We are glad that the reviewer appreciates our work in “decrypting the roles of C2 individual operating modes” as it is a “central issue for providing functional specificity but also plasticity in response to developmental /environmental clues”. The reviewer also considers our work “important and identifies a number of very interesting features”. As already mentioned to the editor, the present version of the manuscript includes new biochemical data and analysis to support further the functions of C2A-C2B tandem. In addition, we have included new references and rephrased some of the headings and statements in the discussion section, to adjust them better to our experimental results.

Reviewer 3

Major points

1)The authors investigated SYT1C2A calcium-binding sites using two different methods, ITC and differential scanning fluorimetry. By using ITC, they described the first binding site coordinating calcium ions in the nanomolar range. The second calcium-binding site was then characterized by differential scanning fluorimetry. The second calcium-binding site binds calcium with Kd of 277 µM. The authors then mutated SYT1C2A at two positions and performed again differential scanning fluorimetry. In this case, they did not observe any blue shift in intrinsic fluorescence concluding that "calcium-binding is mediated by the calcium-binding site". It is not clear which binding site the authors mean. In the structure of SYT1C2A, the mutated residues (D276 and D282) are shared by both calcium-binding sites. It is, therefore, difficult to interpret the data. The authors should generate a unique mutation for each site and perform both ITC and differential scanning fluorimetry

The SYT1C2A-DADA double mutant was prepared to abolish Ca2+ binding to both site I and site II and to discard an unspecific effect of Ca2+ on intrinsic fluorescence that accounts for the low affinity Kd. Our data showed that the addition of Ca2+ to SYT1C2A-DADA does not produce a shift in intrinsic fluorescence of the protein; indicating that the observed Ca2+-binding activity is specifically mediated by the Ca2+ dependent lipid binding site. We clarify this point in the present version of the manuscript.

In addition, following reviewer’s recommendation, we have prepared two additional point mutant proteins, SYT1C2A D276A and SYT1C2A E340A, to investigate the Ca2+ binding properties at site II and I, respectively. As expected, the reduction of one carboxylate ligand at the structural site II produces a drastic decrease in the Ca2+ binding affinity (Kd = 1.8± 0.5 mM) which is coupled with a decrease in thermal stability of the protein (Ti = 55°C) and a red-shift in fluorescence emission with respect to the wild type protein that resembles those effects observed for the SYT1C2A-DADA mutant (Figure S2A). Differentially, SYT1C2A Glu334Ala doubled the Kd (534 ± 60 mM) while reducing slightly its thermal stability (page 7 figure S2A)

2)The authors described an increase in the inflexion point temperature with increasing calcium concentration. They noted that the effect was measurable from 30 µM to 300 µM. Looking at the plot with the first derivative ratio (Figure 2C), there is also an apparent change in the inflexion point temperature from 300 µM to 3 mM. Does this mean that the SYT1C2A domain binds more than two calcium ions?

The ligand induced stabilization of proteins results in changes of the thermally induced melting curves for the ligand complexed relative to the uncomplexed proteins. This effect is used to unequivocally identify ligand hits for a particular protein from large libraries of compounds and to provide an initial estimation of the binding affinity. However, a deeper analysis of the ligand binding affinities using this technique is discouraged as the increase of melting temperature with the ligand concentration does not saturate to a particular value. This is why the effect of Ca2+ addition to SYT1C2A was also measurable from 300 µM to 3 mM, and it does not necessarily imply the binding of Ca2+ to another site. Consequently, we used other techniques such as ITC or the analysis of the change of intrinsic fluorescence upon Ca2+ addition to precisely characterize the Ca2+ binding affinities of SYT1C2A. In the present version of the manuscript, we have indicated that the change in Ti vs Ca2+ concentration is measurable when moving from 30 mM to 300 mM, thus demonstrating a Ca2+-binding event “is initiated” in this concentration range (page 7)

3)To address lipid-binding properties of the SYT1 C2 domains, the authors used two independent methods, lipid co-sedimentation assay and BLI. In the Material and Methods section, the authors wrote that a solution of liposomes was sonicated for seven minutes to achieve homogeneity. How was homogeneity checked? Standard protocols for the liposome co-sedimentation assay use the extruder to achieve a homogeneous population of the liposomes. Also, the authors noted that the liposomes were resuspended in the buffer containing 50 mM Tris/HCl, 80 mM KCl, and 5 mM NaCl. The liposomes are usually loaded with sugar molecules, like raffinose at this step to allow subsequent co-sedimentation using centrifugation.

Following the reviewer recommendation, we have used an extruder to achieve a homogeneous population of the liposomes (see the Methods section). This has produced an improvement of the data from the statistical point of view. However, we did not employ any sugar to facilitate lipid sedimentation as we found that 1 hour centrifugation at 58,000 rpm using a TLA100 rotor (Beckman) was enough to separate adequately soluble and precipitated fractions.

The authors wrote that the samples were centrifuged at 58,000 rpm. The information does not allow reproducibility without rotor specification.

We have now included the rotor specification in the methods section.

The bound protein was estimated by subtracting the supernatant from the total amount of protein used in the assay. Direct estimation of the protein amounts in the bound fraction via e.g. SDS-PAGE would be more suitable.

We respectfully disagree with the reviewer in this issue. The reviewer may note that the differences in the fraction of bound protein to the liposomes are at maximum around 25%. Such values are statistically significant using spectrophotometric techniques but there will be less accurately determined by the analysis of an SDS-PAGE. In addition, the later would require several washing steps of the insoluble fraction that may induce additional errors. This is well documented in a previous work from our group (Diaz et al, PNAS 2015). There, the lipid binding properties of WT and mutant C2 domain are compared using both approaches; in this work it is shown that the spectrophotometric techniques showed significant differences with the SDS-PAGE, which resulted just indicative.

Nevertheless, we have prepared the requested SDS-PAGE for reviewer evaluation (see below) and if required we will include it as a new panel in figure 4 or include it as supplementary material. The SDS-PAGE shows the amount of soluble protein after the incubation with liposomes. It is clearly shown a reduction in the amount of WT and DADA soluble protein upon incubation with PCPSPI liposomes with respect to the sample incubated with PCPS liposomes. Differentially, no effect is observed for the PolyB and WT in presence of EGTA. Sample migrates abnormally producing a double band in presence of EGTA, probably due to the effect of removing the structural Ca site.

Critical controls for the liposome co-sedimentation assay are missing:

Do the SYT1 C2 domains bind liposomes without negatively charged lipids (i.e. PC-only liposomes)?

Does the SYT1C2A-DADA mutant domain bind the PC/PS/PI liposomes?

Does the SYT1C2A-PolyB mutant interact with the PC/PS liposomes?

We have included all the controls suggested by the referee in the present version of the manuscript, in the results section and in figure 4A.

The authors wrote both in the main text and the figure 4 legend that they used a lipid monolayer in the BLI method. However, in the Material and Methods section, they wrote that they used small unilamellar vesicles.

The starting material for lipid monolayer immobilization at the biosensor tip is a solution of small unilamellar vesicles. We have clarified this issue in the methods section.

4)The authors beneficially used all-atom MD simulations to address mechanistic details of the SYT1 C2 domains with two different lipid bilayers. However, several issues need to be addressed.

Is there a particular reason to include sitosterol in the MD simulations? Does sitosterol contribute to protein binding?

We clarify this issue in the present version of the manuscript. The use of sitosterol or stigmasterol in research involving plant membranes and membrane-associated proteins is recommended (DOI: 10.1063/1.4983655 PMID: 28595398) to recapitulate the fluidity and thermotropic properties of model membranes (DOI: 10.1016/j.colsurfb.2019.110422 PMID: 31437609). Sitosterol, as is the case for cholesterol in mammal membranes, contributes to packing the lipid bilayer more tightly into a liquid ordered phase (DOI: 10.1016/j.chemphyslip.2017.01.003 PMID: 28088325) and this aspect is important in molecular dynamics simulations to attain equilibration more effectively (DOI: 10.1016/j.jcis.2011.02.048 PMID: 21429500).

We observed one hydrogen bond contact between Asn 338 at loop L3 and sitosterol in PSPI-M. We clarify this point in the results section.

Why was not the simulation ran for a longer time? What was a criterion to determine that the system reached a stable state? Results of the MD simulations are presented as static snapshots. The manuscript would benefit from a more detailed analysis, e.g. the number of hydrogen bonds between the protein and phospholipid molecules over time, development of the tilt angle over time, etc.

Following the reviewer’s recommendations, we now provide data showing the dynamic features of our MD calculations. In particular, we have compared the overlay of the different structures along the simulation of the SYT1C2A domain attached to the PS-Membrane and to the PSPIP-Membrane highlighting those amino acids hydrogen bonded to phospholipids (Figure S4A and S4B). This picture illustrates well that the pattern of interactions is conserved along the simulation. In addition, it also shows that the orientation of the domain with respect to the plane of the membrane is conserved. In this respect, as the reviewer requested, we have also included, a picture illustrating the change in the tilt angle of the C2A with respect to the plane of the membrane along the simulation. This analysis reveals that the tilt angle with respect to the membrane is 20 degrees larger for the PSPIP-Membrane than for the PS membrane due to the interaction of PIP molecules with the polybasic site (Figure S4E).

In addition, we now present time traces illustrating the course of the simulations. In particular, those corresponding to the RMSD of the individual SYT1C2A, SYT1C2B and the linker between them. They clearly show that the simulations reached equilibrium within the time sampled (Figure S5H).

The authors performed the MD simulations for both SYT1 C2 domains. It would be informative to include an electrostatic potential mapped on the surface of the SYT1C2B domain similarly to figure 3. The experimental results showed that SYT1C2B binds liposomes containing PC/PS. How does SYT1C2B interact with the PC/PS membrane? The authors noted that SYT1C2 inserts loop L3 into the lipid bilayer and that this loop adopts a β-hairpin structure. This is the case for the simulation with the SYT1C2AB fragment, but not for the SYT1C2B domain alone. Is the β-hairpin formed during the MD simulation? Or is it a result of the template-based modelling?

To clarify reviewers’ concerns, we have included a supplementary figure illustrating the RMSD per residue along the MD simulation for the SYT1C2AB protein fragment in solution, and attached to PSPI-M. The representation illustrates an overall reduction of the RMSD as a result of the protein stabilization at the membrane, which is more significant at the membrane binding loops. In particular, the highly flexible SYT1C2B L3 loop in solution becomes highly stabilized upon membrane interaction and it folds as a beta hairpin.

We have calculated the electrostatic potential mapped on the surface of the SYT1C2B. As it does not come from an experimental structure, we decided not to include in figure 3. The map, which is depicted below in the orientation shown in figure 3, shows that SYT1C2B might not display a polybasic site in accordance with our experimental results.

How is the proposed binding model of the SYT1C2AB affected by the data obtained using SAXS?

SAXS data showed that SYT1C2AB fragment may adopt a V-shaped compact structure and an extended conformation in which there is no interaction between the C2A and C2B domains. Interestingly, the V-shaped structure in solution resembles the proposed binding mode for SYT1C2AB to the membrane. We clarify this point in page 15.

Minor comments

1) SYT1CB construct is not listed in figure 1A along with the other constructs used in the study.

We have modified Figure 1B to include SYT1C2B

2) Phospholipids contain a phosphate group rather than a phosphoryl group.

We have modified the text to correct this.

3) In the text, the authors sometimes used the ratio 350 nm/330 nm and sometimes 330 nm/350 nm.

This has been corrected in Figure 2C

4) Figure S2, displayed curves look strikingly similar, different line representation does not allow a proper comparison. There are no units for y-axes.

The figure has been corrected according to the reviewer’s recommendation for proper comparison.

5) Figure 4B, y-axes do not have scales.

The Y-axis from the BlitZ system represents the thickening of the layer of proteins attached to the biosensor tip and it is given in nm. However, this parameter could be meaningless when comparing different membranes and/or proteins. Hence, we scaled the plots to the maximum thickness for comparison purposes.

6) Figure 5B, IP3 or I3P?

We have corrected the labels corresponding to inositol triphosphate IP3 at figure 5B

7) The authors noted that based on their SAXS experiments, the SYT1-SMPC2A has a maximum size of 176 Å and they wrote that this value is in accordance with the size of the previously characterized E-Syt2-SMPC2AB protein. However, as the authors reported, E-Syt2-SMPC2AB is two times smaller.

We agree with the reviewer, the size of the SMP tunnel of E-Syt2-SMPC2AB is two times smaller than the Dmax size of SYT1 SMPC2A. We clarify this point in the text.

Yours sincerely

Armando Albert

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Referee #3

Evidence, reproducibility and clarity

The focus of this manuscript is the structural characterization of Arabidopsis synaptotagmin 1 (SYT1), which is a plant ortholog of the mammalian extended synaptotagmins (E-Syts). E-Syts play a principal role in the non-vesicular lipid transfer at the endoplasmic reticulum - plasma membrane contact sites. The function of the extended synaptotagmins is given by a unique combination of the evolutionarily conserved domains. The authors combined both experimental and computational methods to characterize different domains of Arabidopsis SYT1.

The authors solved the structure of one of the SYT1 C2 domains (SYT1C2A) using X-ray crystallography. The obtained structure is highly similar to the previously characterized C2A domain of mammalian E-Syt2. In contrast to the orthologous C2A domain of E-Syt2, only two calcium ions are coordinated by the SYT1C2A domain. Next, the authors aimed to characterize the identified calcium-binding sites by two different experimental techniques, namely isothermal titration calorimetry (ITC) and differential scanning fluorimetry. To study lipid interactions of SYT1, the authors used a combination of the experimental approach (liposome-binding assays and biolayer interferometry, BLI) and computational methods (ligand-protein docking and molecular dynamics simulations). The authors found that both SYT1 C2 domains can interact with the lipid bilayer containing anionic phospholipids. Intriguingly, the authors described two lipid-interacting sites in the SYT1C2A domain. One site is involved in the coordination of phosphatidylserine (PS) in a calcium-dependent manner, and the second one coordinates molecules of phosphatidylinositol 4,5-bisphosphate (PIP2) through mostly electrostatic interactions. Last, the authors study the flexibility of SYT1 using partially overlapping protein fragments via small-angle X-ray scattering. Three hinge points are suggested to be responsible for the high flexibility of SYT1.

The notion that SYT1C2A domain confers two independent lipid-binding sites, one unique for PIP2 molecules, and the second one regulated by calcium ions, is very compelling. In addition, the results describing the potential SYT1 flexibility provide novel insight into the function of extended synaptotagmins. However, my enthusiasm is mitigated by several points listed below:

1)The authors investigated SYT1C2A calcium-binding sites using two different methods, ITC and differential scanning fluorimetry. By using ITC, they described the first binding site coordinating calcium ions in the nanomolar range. The second calcium-binding site was then characterized by differential scanning fluorimetry. The second calcium-binding site binds calcium with Kd of 277 µM. The authors then mutated SYT1C2A at two positions and performed again differential scanning fluorimetry. In this case, they did not observe any blue shift in intrinsic fluorescence concluding that "calcium-binding is mediated by the calcium-binding site". It is not clear which binding site the authors mean. In the structure of SYT1C2A, the mutated residues (D276 and D282) are shared by both calcium-binding sites. It is, therefore, difficult to interpret the data. The authors should generate a unique mutation for each site and perform both ITC and differential scanning fluorimetry.

2)The authors described an increase in the inflexion point temperature with increasing calcium concentration. They noted that the effect was measurable from 30 µM to 300 µM. Looking at the plot with the first derivative ratio (Figure 2C), there is also an apparent change in the inflexion point temperature from 300 µM to 3 mM. Does this mean that the SYT1C2A domain binds more than two calcium ions?

3)To address lipid-binding properties of the SYT1 C2 domains, the authors used two independent methods, lipid co-sedimentation assay and BLI. In the Material and Methods section, the authors wrote that a solution of liposomes was sonicated for seven minutes to achieve homogeneity. How was homogeneity checked? Standard protocols for the liposome co-sedimentation assay use the extruder to achieve a homogeneous population of the liposomes. Also, the authors noted that the liposomes were resuspended in the buffer containing 50 mM Tris/HCl, 80 mM KCl, and 5 mM NaCl. The liposomes are usually loaded with sugar molecules, like raffinose at this step to allow subsequent co-sedimentation using centrifugation. The authors wrote that the samples were centrifuged at 58,000 rpm. The information does not allow reproducibility without rotor specification. The bound protein was estimated by subtracting the supernatant from the total amount of protein used in the assay. Direct estimation of the protein amounts in the bound fraction via e.g. SDS-PAGE would be more suitable. Critical controls for the liposome co-sedimentation assay are missing. Do the SYT1 C2 domains bind liposomes without negatively charged lipids (i.e. PC-only liposomes)? Does the SYT1C2A-DADA mutant domain bind the PC/PS/PI liposomes? Does the SYT1C2A-PolyB mutant interact with the PC/PS liposomes? The authors wrote both in the main text and the figure 4 legend that they used a lipid monolayer in the BLI method. However, in the Material and Methods section, they wrote that they used small unilamellar vesicles.

4)The authors beneficially used all-atom MD simulations to address mechanistic details of the SYT1 C2 domains with two different lipid bilayers. However, several issues need to be addressed. Is there a particular reason to include sitosterol in the MD simulations? Does sitosterol contribute to protein binding? Why was not the simulation ran for a longer time? What was a criterion to determine that the system reached a stable state? Results of the MD simulations are presented as static snapshots. The manuscript would benefit from a more detailed analysis, e.g. the number of hydrogen bonds between the protein and phospholipid molecules over time, development of the tilt angle over time, etc. The authors performed the MD simulations for both SYT1 C2 domains. It would be informative to include an electrostatic potential mapped on the surface of the SYT1C2B domain similarly to figure 3. The experimental results showed that SYT1C2B binds liposomes containing PC/PS. How does SYT1C2B interact with the PC/PS membrane? The authors noted that SYT1C2 inserts loop L3 into the lipid bilayer and that this loop adopts a β-hairpin structure. This is the case for the simulation with the SYT1C2AB fragment, but not for the SYT1C2B domain alone. Is the β-hairpin formed during the MD simulation? Or is it a result of the template-based modelling? How is the proposed binding model of the SYT1C2AB affected by the data obtained using SAXS?

Minor comments:

1) SYT1CB construct is not listed in figure 1A along with the other constructs used in the study.

2) Phospholipids contain a phosphate group rather than a phosphoryl group.

3) In the text, the authors sometimes used the ratio 350 nm/330 nm and sometimes 330 nm/350 nm.

4) Figure S2, displayed curves look strikingly similar, different line representation does not allow a proper comparison. There are no units for y-axes.

5) Figure 4B, y-axes do not have scales.

6) Figure 5B, IP3 or I3P?

7) The authors noted that based on their SAXS experiments, the SYT1-SMPC2A has a maximum size of 176 Å and they wrote that this value is in accordance with the size of the previously characterized E-Syt2-SMPC2AB protein. However, as the authors reported, E-Syt2-SMPC2AB is two times smaller.

Significance

Nature and significance of the advance:

By a combination of experimental and computational methods, the manuscript provides novel insight into the structure-function relationship of plant SYT1.

Work in the context of the existing literature:

The submitted manuscript deals with Arabidopsis SYT1 protein, which belongs to an evolutionarily conserved family of proteins functioning at the ER-PM contact sites. Several recent reports described a principal role of Arabidopsis SYT1 in the regulation of lipid homeostasis, plasmodesmata functions and the response to various stresses (Lee et al. 2019. Ionic stress enhances ER-PM connectivity via phosphoinositide-associated SYT1 contact site expansion in Arabidopsis. PNAS 116, 1420-1429. https://doi.org/10.1073/pnas.1818099116; Ishikawa et al. 2020. Structural and functional relationships between plasmodesmata and plant endoplasmic reticulum-plasma membrane contact sites consisting of three synaptotagmins. New Phytologist 226, 798-808. https://doi.org/10.1111/nph.16391; Ruiz-Lopez et al. 2021. Synaptotagmins at the endoplasmic reticulum-plasma membrane contact sites maintain diacylglycerol homeostasis during abiotic stress. The Plant Cell. https://doi.org/10.1093/plcell/koab122). However, in contrast to mammalian orthologs, mechanistic details of the plant SYT1 function are largely missing.

Audience:

The manuscript might be of interest to the community of plant molecular biologists, structural biologists dealing with peripheral membrane proteins and computational biologists.

Reviewer's expertise:

Reviewer's field of expertise is plant molecular biology, plant biochemistry, protein-protein, protein-membrane and ion-membrane interactions, molecular dynamics simulations, integrative structural biology, structural bioinformatics.

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Referee #2

Evidence, reproducibility and clarity

This work focuses on Synaptotagmin1 (SYT1), a regulatory element of plant membrane contact site, that act as a tether and physically and functionally connects the endoplasmic reticulum (ER) to the plasma membrane (PM). Like many membrane contact site proteins, SYT1 harbours lipid transfer activity through its SMP domain. Plant SYTs proteins are orthologous to the Extended Synaptotagmin and Tricalbin ER-PM tethers from animal and yeast. SYT1 presents two C2 (C2A and C2B) lipid-binding domains at their C-terminus that are determinant for PM binding, presumably regulating SYT1 function at ER-PM membrane contact sites.

In this paper, Benavente et al. aimed at investigating the molecular mechanisms of SYT1 binding to the PM and specificity of function of C2A (previous work has shown that SYT1 C2A, but not SYT1 C2B, binds membrane lipids in a Ca2+ dependant manner). The authors combined a wide range of approaches from X-ray crystallography to biophysics and in silico molecular modelling to understand the mechanisms of SYT1 C2A interaction with lipids, at the molecular level. From their study, Benavente et al. shows that C2A display dual lipid binding activity interacting with PS in a Ca2+-dependant manner and with phosphoinositide in a Ca2+-independent manner. These interactions involve two distinct sites; a polybasic amino acid site for phosphoinositides binding and a Ca2+-dependant lipid binding site for PS. They propose that this two-steps binding mechanism confers plasticity in membrane docking under low and high intracellular calcium concentration. They also show that SYT1 full length protein displays three flexible hinges, which they propose confers SYT1 a high degree of conformational freedom

Minor comments

• Typos: please re-read carefully through the manuscript to remove them.
• We advise the authors to have the manuscript corrected by a native english-speaker.

Significance

C2- domains are central functional elements of SYT/E-SYT/Tricalbin ER-PM tethers. They regulate PM docking through their lipids binding activity, which can be calcium-dependant or calcium-independent, but also presents lipid specificity (PS, phosphoinositides...). Beside their lipid-binding activity, C2 domains have also been shown to be involved in protein-protein interaction, including intramolecular interaction to inhibit lipid-transfer activity (E-SYT). Multiple C2s are present in SYT/E-SYT/Tricalbin tethers and their diversity of function is likely central for providing functional specificity but also plasticity in response to developmental /environmental clues (together with changes membrane lipid composition and intracellular calcium levels). Decrypting C2 individual operating mode is therefore central. This work is important as it investigates SYT1A docking mechanisms at the molecular level and identifies a number of very interesting features. However, as it stands, the paper does not make the link with SYT1 functionality. The authors discuss their findings within the frame of experimental observations that are already published but these remain speculative.

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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). The authors obtain a high-resolution structure of SYT1C2A and characterize its calcium and lipid-binding capabilities and those of SYT1C2B. They also study the influence of these interactions on domain topology and the overall architecture of SYT1. They uncover a calcium-dependent lipid binding mechanism that allows them to propose an interesting model in which SYT1C2A binds to the PM to help shuttle DAG to the ER upon abiotic stress.

Major comments:

• Are the key conclusions convincing? - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? The conclusion that SYT1C2A determines protein behavior by binding calcium and likely switching its function from a pure tether to a lipid transporter is accurately and convincingly portrayed. However, there are some problematic statements in the way this information is interpreted and used to propose a model.

• p7: "This means that site I will be occupied depending on the physiological Ca2+ concentration to activate the protein and trigger Ca2+-dependent SYT1C2A lipid binding." Please exchange "means" by "suggests".

• There is not enough data to determine whether SYT1C2A interacts with the SYT1SMP domain, much less to propose that it is the SYTC2A that loads the SMP with DAG. They may also operate independently by means of the unstructured hinge sequence between them.

• It is implied that SYTC2A would have to release its calcium atom for it to leave the PM and go to the ER to complete a single transport cycle. It is unclear whether SYT1C2A could bind and release calcium repeatedly and fast enough to cycle between membranes efficiently. It appears more plausible for it to remain at the PM until intracellular calcium concentrations decrease. These statements should be marked as speculative.

• 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 new experiments suggested.
• Are the data and the methods presented in such a way that they can be reproduced? Yes, to the best of my knowledge.
• Are the experiments adequately replicated and statistical analysis adequate? No. Most of the graphs shown (except Fig. 4A) appear to show only one experiment. Please include results from at least three independent experiments in all graphs, and analyze them statistically. Please describe only differences between samples that are statistically significant (for all graphs and tables).

Minor comments:

• Specific experimental issues that are easily addressable. No issues with experiments.
• Are prior studies referenced appropriately? Generally yes, but there are a few things to change:

• Please include the PDB codes for the available structures used. It is not clear where the C2C domain structure comes from. We guess it may correspond to PDB entry 2DMG. A word of caution, this 2006 structure has been released but not published and its quality is suboptimal. After its appearance in Idevall-Hagren et al. 2015 supplementary images it has been re-cited in other publications. I would advise against making topology claims based on this structure (Figure S1), and only use it as an example for polybasic patches in C2 domains. • p4: Schauder et al. 2014. Only the "shuttle" model is mentioned in the text. Although this may be the most plausible scenario, the "tunnel" model cannot be completely ruled out. • p5: Fernandez-Busnadiego et al. 2015 does not make a reference to the claim in the text. • p18: Collado et. al 2019 don't assign the peak-forming function to the N-terminal hairpin domain of tricalbins.

• Are the text and figures clear and accurate? Generally yes, although the figures and legends should contain more information. For example:
• Fig. 1A: the notation for the domains C2C-C2E of E-Syt1 is confusing and not described in the legend. Also, please mark which beta sheet is which more clearly in Fig 1B, it is very difficult to understand the labelling.
• Fig. 1C: several elements (e.g. types of boxes, "T" on the top) used in the figure are not described in the legend. Both beta sheets and mutations are described as "arrows" in the legend, please differentiate between vertical and horizontal.
• Fig. 2A: indicate Lys 286, which is mentioned in the text.
• Fig. 2B: Inset too small to read.
• Fig. 3: please show the scale and explain the blue-red color code. Please mark the polybasic patch.
• Fig. 4A should show both mutants for both types of liposomes.
• Table 1: what is "control"?
• Fig. S5: Difficult to read, increase font size. The text talks about experiments with calcium and EGTA that are not shown in the figure.

Text:

• p5, first Results paragraph: reference the loop numbers marked in the figure to facilitate the description. The description of the loop between b6 and b7 is not clear: the text implies it is not present in SYT1C2A, although it should say it is unstructured.
• Please indicate more prominently throughout the text and methods the plant species from which the C2 domains were studied, rather than just saying "plant". For example, are all the other SYTs shown in Fig 1C from Arabidopsis as well? To generalize the findings reported here as "plants", the conservation in other species need to be shown. Alternatively, please rephrase the relevant statements.
• "Data" is used both in singular and plural.
• There are several typos (it would be much easier to point to them having line numbers in the manuscript!), e.g. p6 title says "C2+" and the next paragraph "SYTCA2", Fig. 4D is mentioned in the text but it doesn't appear in the figures, p16: "DAG form the PM" -> from, p17 "overexpression of Syt1" -> E-Syt1.
• Do you have suggestions that would help the authors improve the presentation of their data and conclusions? References to abiotic stress leading to DAG accumulation can be found throughout the paper, but little is explained about how this correlates with the increase in calcium concentration suggested for SYT1 activation. It would be an improvement to explain how this happens.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. Multi-C2 domain proteins perform multiple different functions through mechanisms not yet fully understood. One important reason for this lack of knowledge is the presence of multiple C2 domains and their similarity to each another. The key to understanding how a C2 domain operates can hinge on a single calcium-binding site, which often escape accurate prediction by homology modelling and other computational methods. This is also the case for lipid binding affinity and stereophysical properties of any protein. This work highlights the importance of obtaining reliable, high-resolution structures of these domains as well as characterizing their binding partners and the dynamics of their interactions. Through the identification of the properties of each C2 domain and adjacent sequences the authors provide a coherent mechanistic model for SYTC2AB and a reproducible workflow for the study of other C2 domains.
  • Place the work in the context of the existing literature (provide references, where appropriate). This work is an important step in the study of plant synaptotagmins, in which previously reported SYT1 biochemical properties (Schapire 2018, Perez-Sancho 2015, among others) and the study of its orthologs in other organisms are brought together with novel structural and biophysical data to create a compelling mechanistic model. It also has important implications for the mechanisms of functions of this family of proteins in other organisms.
  • State what audience might be interested in and influenced by the reported findings. Researchers in the broad membrane traffic community will enjoy this work, and particularly those working with orthologs of SYT1 might find insights that apply to their research. In a broader sense, this work will be appealing to researchers working in plant cellular stress response.
  • 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. Structure of ER-PM contact sites. I have no expertise in titration calorimetry or SAXS and cannot properly evaluate those results.

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Reply to the reviewers

We are grateful to the reviewers for their thoughtful comments and propose the following experiments or clarifications listed below (blue) in a revised manuscript.

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

The authors use a combination of Dsn1-Flag kinetochore purification from yeast extracts and laser trapping experiments (as in a number of previous studies), to study the effect of Mps1-dependent phosphorylation on reconstituted kinetochore-microtubule attachments in vitro. They complement this analysis with genetic experiments characterizing the effects of non-Mps1 phosphorylatable mutants on checkpoint activity and chromosome segregation in yeast.

The authors had previously shown that Mps1 is the major kinase activity that copurifies with Dsn1-Flag in their purification scheme. They now investigate the effect of adding ATP and thereby allowing Mps1 phosphorylation in the reconstituted system. They show that addition of ATP decreases the rupture force of kinetochore-microtubule attachments, meaning it weakens the strength of the attachment. This effect can be negated either by inhibiting Mps1 with reversine, or by providing kinetochores in which the Mps1 phosphorylation sites on Ndc80 (most of them in the N-terminal tail) have been mutated to alanine. Thus, like the activity of Ipl1, Mps1 phosphorylation of the Ndc80 N-tail (which is known to be important for full MT affinity) weakens kinetochore-microtubule attachments.

Cellular experiments demonstrate that non-Mps1 phosphorylatable Ndc80 14-A mutants have a functional mitotic checkpoint (contrary to previous claims by Kemmler et al., 2009), but show synthetic sickness with stu2 alleles that are involved in error correction.

**Major points:**

Within the framework of this experimental setting, the study as presented is logical and clear. The conclusions regarding the effect of Mps1 in this reconstituted system are overall well supported by the data. I have a couple of major and some minor points that can further improve data interpretation and should therefore be considered:

1. In previous publications (e.g. Gutierrez et al., Current Biology 2020), the authors have reported that the Dam1 complex, an established Mps1 substrate, is required for full attachment strength in this system. Are the effects of Mps1-dependent Ndc80 phosphorylation and Dam1 independent from one another? For example would dad1-1 or non Cdk1 phosphorylatable Dam1 complex further reduce the rupture force in ATP? Or does Mps1 phosphorylation affect, for example, Dam1 binding to Ndc80?

Response: To better understand the effects of ATP treatment, we analyzed the levels of Dam1 on the kinetochores after ATP treatment and did not see any change. We will add this data to a supplemental figure. Dam1 clearly makes a major contribution to the strength of the kinetochores because their strength even after ATP-treatment is higher than the rupture force of kinetochores purified from a dad1-1 mutant strain. However, as we report in the paper, blocking the eight Mps1 target sites in the tail of Ndc80 was sufficient to block the effect of ATP, so it is unlikely that phosphorylation of the Dam1 complex by Mps1 makes a major contribution to the ATP-dependent kinetochore weakening in vitro. We think Dam1 phosphorylation by Aurora B probably contributes independently to error correction, because the dam1-3D mutant, carrying phospho-mimetic substitutions in three Aurora B sites, is synthetically lethal when combined with the ndc80-8D phospho-mimetic mutant in eight Mps1 sites. We will add this genetic interaction data to the revised manuscript to provide additional information about the pathways.

What is the effect of ATP on initial binding events? Are there differences in the fraction of beads that spontaneously attach laterally at the start of the experiment? This may allow to draw conclusions whether any kind of binding or specifically force-generating end-on attachments are affected by ATP.

Response: We did measure a reduction in the fraction of free kinetochore-decorated beads capable of binding microtubules upon exposure to ATP (from 20% binding in the absence of adenosine to 11% in the presence of ATP). This observation suggests that the microtubule-binding activity of the kinetochores, like their rupture strength, is reduced upon exposure to ATP, as reported in the methods, in the "rupture force measurements" section. However, because we worked with a low density of kinetochores on the beads, the initial numbers of beads that spontaneously attached was quite low and free beads capable of binding to microtubules were relatively rare. In addition, when we find a bead already attached to the lattice, we cannot distinguish whether it bound initially to the lattice or instead bound to a tip that then grew beyond the bead. For these reasons, we feel it would be very difficult using our current approach to draw statistically significant conclusions about whether there were ATP-dependent changes in the relative affinities of the kinetochores for lateral versus tip attachments.

Ndc80-8D has low attachment strength, consistent with lowered MT affinity of the phospho-mimetic Ndc80 tail. Interestingly, Supplementary Figure S4B shows that the amount of Cse4 in the pull-down western appears substantially reduced in 8D vs 8A or wt. Is the amount of co-purified inner kinetochore affected in this mutant? This may be an alternative explanation for decreased attachment strength, for example if the fraction of "full" or "complete" kinetochores may be reduced. Could this also happen upon inclusion of ATP?

Response: The reviewer is correct that the level of Cse4 and other inner kinetochore components is slightly reduced in the Ndc80-8D kinetochores, for reasons that are not clear to us. However, the incubation of wild type kinetochores with ATP does not affect the levels of these proteins, suggesting that the weakened rupture strength is not due to reduced levels of these inner kinetochore proteins. We will add the data showing that ATP does not affect levels of inner kinetochore proteins into a supplemental figure to clarify this point.

**Minor points:**

page 13 (heading): "Weakening occurs via phosphorylation...". Probably good to mention what is weakened ("Weakening of kinetochore-microtubule attachments occurs via phosphorylation...".

Response: We will alter the heading as suggested.

page 14/Figure5C: Median Rupture Force for Ndc80-8D is 4.8 pN according to the text. In the graph it looks like >5 pN.

Response: We thank the reviewer for noticing this mistake and will correct the median rupture force to 5.6 pN.

page 23: comma missing between T21 S37 and T47 (should be T21, S37 and T47)

Response: We thank the reviewer for noticing this omission and will correct it.

page 24/25: different spelling of G1 (sometimes with subscript)

Response: We thank the reviewer for noticing this inconsistency and will correct all to be G1.

page 24/25: ug instead of µg

Response: Thanks. We will fix this mistake.

page 28: Figure 5B instead of Figure 5A

Response: Thanks for noticing this mistake. We will correct this.

Figure 6A: Lambda-Phosphatase treatment for 20 minutes according to figure legend and 30 minutes according to Material and Methods section.

Response: The material and methods section specified a 20-minute incubation with phosphatase, in agreement with the figure legend. We believe the reviewer might have accidentally confused the time value with the temperature, which was 30 degrees.

Figure 6E: One should not draw any conclusions from the anti-phospho T47 blot here, the quality is simply too poor to allow a statement regarding an mps1-1 effect

Response: While the immunoblots with the T74 phospho-specific antibody are not as clean as many standard antibodies, we have reproduced the results multiple times and therefore feel comfortable concluding that there is a decrease in signal that is Mps1-dependent.

Figure 6: Labelling T47P misleading (Proline substitution?, use pT47 instead)

Response: We will change the labeling on this figure, as suggested, from T74P to pT74. To be consistent, we will also change this nomenclature in the text.

Figure 6F: Make clear in the labelling that a stu2-AID background is used here, makes it easier to understand why Auxin is used here.

Response: We will change the labeling, as suggested, to include the genotype of stu2-AID in the figure.

how specific is reversine for yeast Mps1? I have not seen any data on this in previous publications.

Response: Reversine is not necessarily specific for Mps1. However, the only kinase activity that co-purifies with the isolated kinetochores is from Mps1, so reversine should inhibit only Mps1 in our in vitro experiments. Nevertheless, to further address this concern, we will include optical trapping results using mps1-1 mutant kinetochores in the revised manuscript. We have already performed these additional experiments and found that mps1-1 kinetochores do not undergo ATP-dependent weakening, strongly reinforcing our conclusion that Mps1 is the major kinase involved.

additional genetic interactions might be informative, if Ndc80-8D has weakened attachments, it may have synthetic effects with other mutants (dam1?), conversely, ndc80-8A may show genetic interactions with ipl1 alleles, for example.

Response: We agree that the ndc80 phospho-mutant alleles might have genetic interactions with other mutants. Consistent with this prediction, we have found that ndc80-8D is synthetically lethal when combined with the dam1-3D mutant in three Ipl1 sites. As mentioned above, we will add this data into the revised text. We will also perform additional genetic interaction experiments with ipl1 and mps1 alleles and add any additional interactions we discover into the revised text.

Reviewer #1 (Significance (Required)):

The study adds to the characterization of the effects of Mps1 kinase on kinetochore-microtubule attachments and characterizes the cellular phenotypes of non-Mps1 phosphorylatable Ndc80 mutants. The major conceptual point that Mps1 phosphorylation can weaken kinetochore-microtubule interactions and thereby contributes to error correction in a manner similar to Ipl1 has previously been made in the literature. Maure et al., (Tanaka lab, 2007, Current Biology) have characterized the effects of mps1 mutant alleles on biorientation of authentic chromosomes and on replicated/unreplicated mini-chromosomes. In particular the experiments with unreplicated mini-chromosomes have revealed less frequent detachment in mps1 mutants, demonstrating that Mps1 activity is required to release attachments that are not under tension.

Another benefit of this study is that it puts the Kemmler 2009 EMBO J. paper into perspective and corrects some of it claims. In particular the notion of sustained checkpoint activation in the Mps1 phospho-mimetic Ndc80-14D mutant, whose lethality was claimed to be rescued by checkpoint deletion. It is confirmed here that the allele is lethal but cannot be alleviated by simultaneous checkpoint deletion. Conversely, the Ndc80-14A mutant is shown to have a functional checkpoint. One could argue that since the publication of the Kemmler paper, the idea of requirement of Mps1 phosphorylation on Ndc80 for checkpoint activity has not gained any traction in the field, but it's still useful for the field to put some of these earlier claims into perspective. The paper will therefore be interesting to researchers working on mechanisms of chromosome segregation and error correction.

From my background I cannot comment on technical details of the biophysical force spectroscopy experiments (laser trapping), but I have no reason to doubt that the authors accurately report their findings.

Response: We sincerely thank the reviewer for their careful reading, helpful comments, and enthusiasm for our manuscript.

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

This paper focusses on the mechanisms underlying chromosome biorientation in mitosis, an essential process that warrants equal chromosome segregation to the dividing cells. Correction of improper kinetochore-microtubule attachments relies on two conserved protein kinases, Aurora B and Mps1, that detach kinetochores that are not under tension in order to provide them with a second opportunity to establish bipolar connections. In vivo, Aurora B and Mps1 have intertwined functions and share some common targets. For this reason, despite the large body of literature on the subject, their precise roles in chromosome biorientation have been difficult to tease apart.

The authors take advantage of an in vitro reconstitution assay that they previously published (Akyioshi et al., 2010) to identify the critical target(s) of Mps1 in weakening kinetochore-microtubule connections. The assay uses kinetochore particles purified from budding yeast cells that bear Mps1 but are notably deprived of Aurora B. Upon addition of ATP to activate the co-purified kinases (e.g. Mps1), kinetochores are added to coverslip-anchored microtubules to which they attach laterally. Through a laser trap, kinetochores are brought to the microtubule plus-end and pulled with increasing force until the kinetochore detaches, which allows measurements of the average rupture forces that reflect the strength of the attachments. The approach is straightforward and potentially very powerful, first because it provides a simplified experimental set-up in comparison to the cellular context, and second because it directly measures the impact of protein phosphorylation on the strength of attachments.

The authors convincingly show that Mps1-dependent phosphorylation of the N-terminal part of Ndc80 significantly weakens the strength of kinetochore-microtubule attachments in vitro, while phosphorylation of other known Mps1 targets, such as Spc105, does not seem to have an effect. Eight phosphorylation sites in Ndc80, which were previously identified as Mps1-dependent phosphorylation sites (Kemmler et al., 2009), are shown to be critical to destabilise kinetochore-microtubule attachments in the in vitro reconstitution assays. The authors also present evidence for a moderate involvement of Ndc80 phosphorylation by Mps1 in correcting improper attachments in vivo, suggesting that additional mechanisms are physiologically relevant for error correction.

The experiments are mostly well designed, the data are solid and support the main conclusions. However, to my opinion additional experiments could be performed, as outlined below, to strengthen the physiological relevance of the main findings and corroborate some of the conclusions.

**Major points:**

1. Given the partially overlapping function of Mps1 and Ipl1 (Aurora B) in error correction, the ndc80-8A mutant should display synthetic growth and chromosome mis-segregation defects with ipl1 temperature-sensitive alleles. Conversely, the ndc80-8D mutant should suppress the lethality at high temperatures of mps1-3 mutant cells, which were recently shown to be defective in chromosome biorientation (Benzi et al., 2020). Finally, chromosome mono-orientation could become apparent in ndc80-8A cells upon a transient treatment with microtubule-depolymerising drugs, which should amplify the cellular need for error correction.

Response: We agree that further exploration of the possible genetic interactions might help to reinforce the physiological relevance of our main findings. Toward this goal, we will obtain the mps1-3 mutant to determine whether ndc80-8D can suppress its lethality and will add this to the revised manuscript if there is a positive result. As mentioned in response to Reviewer 1, we will add a synthetic lethal interaction between ndc80-8D and a dam1-3D mutant where the Aurora B sites are altered to the revised text. We will also perform additional genetic interactions with ipl1 and mps1 mutants and add any we find into the revision. As requested, we will perform a nocodazole wash out experiment, to determine if ndc80-8A cells show a defect in error correction and add this data to the revision if there is a defect.

The authors show that Mps1-dependent phosphorylation of Ndc80 is not involved in the spindle assembly checkpoint, a conclusion that contradicts a previous report (Kemmler et al., 2009). They also find, in contrast with the same report, that the lethal phenotype of the ndc80-14D phospho-mimetic mutant cannot be rescued by disabling the spindle checkpoint. In my opinion, Kemmler et al. convincingly showed, through a number of different experimental approaches, that ndc80-14D cells die because of spindle checkpoint hyperactivation. Not only deletion of checkpoint genes was shown to rescue the lethality, but re-introduction of a wild type copy of the deleted checkpoint gene reinstated lethality. Thus, the explanation invoked here that spontaneous suppressing mutations could underlie the viability of ndc80-14D SAC-deficient mutants is not consistent with the published observations. A thorough examination by the authors of the phenotype of ndc80-14D cells in their hands should be carried out to support these conflicting conclusions. If authors find that ndc80-14D cells actually die because of chromosome mono-orientation, then this would highlight an important function for some or all the six additional phosphorylation sites, relative to the ndc80-8D mutant, for chromosome biorientation in vivo.

Response: We were unable to reproduce the data that deletion of the spindle checkpoint suppresses lethality of the ndc80-14Dmutant, so it remains unclear why our results differ from those of the Kemmler paper. However, we note that re-introducing a wild-type checkpoint gene via transformation and restoring lethality to the ndc80-14D cells does not necessarily mean there were no suppressors. While that is one possible interpretation, another possibility is that there was a suppressor mutation in the viable ndc80-14D cells that also required the lack of the checkpoint to live. Kemmler and co-workers selected for viability on FOA media and never backcrossed those viable strains to show that they could regenerate the double mutant through a cross with the expected segregation pattern of two mutations, which would have been a more rigorous demonstration that the viability was specifically due to ndc80-14D and the checkpoint mutation. Instead, they transformed a wild-type copy of the checkpoint gene back into the strain that was selected for growth on FOA and showed that it reverted the phenotype. This approach cannot rule out a suppressor mutation that fails to suppress in the presence of an active checkpoint. Therefore, in our opinion, the Kemmler paper does not make an entirely convincing case that the ndc80-14D cells die because of spindle checkpoint hyperactivation.

To further analyze the phenotype of ndc80-14D cells, we have constructed an Ndc80-AID ndc80-14D strain and added auxin, to deplete the wild-type copy of Ndc80. In agreement with the findings of Kemmler et al., this did trigger the spindle assembly checkpoint. However, when we made an Ndc80-AID ndc80-14D mad2 strain and analyzed segregation, we found that chromosome 8 missegregated in 28% of the cells compared to 2% of control cells. This observation suggests that there is a kinetochore defect in these cells that may have triggered the checkpoint and is inconsistent with the mutant solely activating the checkpoint in the absence of any other kinetochore defect. In addition, the levels of Ndc80-14D as well as Mps1 were altered on the mutant kinetochores. The combination of these defects strongly suggests that the ndc80-14D mutant alters kinetochore function in addition to leading to constitutive checkpoint signaling. Because our manuscript is mainly focused on phosphorylation of the Mps1 target sites within the N-terminal tail, we do not plan to add this data involving many additional sites, including Ipl1 target sites and sites on the CH domains of Ndc80, into the current manuscript. We will further pursue the other phosphorylation sites in the future.

The conclusion that Spc105 phosphorylation by Mps1 is not required for the Mps1-mediated weakening of kinetochore attachments in vitro is based on the comparison between kinetochore particles bearing wild type, untagged Spc105 and particles bearing non-phosphorylatable Spc105-6A tagged at the C-terminus with twelve myc epitopes. Thus, the presence of the tag could obliterate the effects of the mutations in the phosphorylation sites by destabilising kinetochore-microtubule attachments in the presence of ATP. Consistent with this conclusion, Spc105-6A-12myc-bearing kinetochores withstand lower rupture forces than Spc105-bearing kinetochores upon ATP addition. Furthermore, Spc105-6A-12myc kinetochore particles show an interacting protein at MW above 150 KD that is not present in wild type particles (Fig. S2A), suggesting that either the tag or the mutations might affect kinetochore composition. Thus, this set of experiments should be repeated using Spc105-6A kinetochore particles lacking the tag.

Response: If we understand correctly, the reviewer is suggesting that the myc tag on Spc105-6A could cause an ATP-dependent effect on kinetochore strength. While this is formally possible, it seems highly unlikely to us, for two reasons: First, a myc tag is not expected to bind nucleotides, and while it can sometimes have a general effect on protein stability or interfere with protein-protein interactions, we are not aware of any evidence for a myc tag directly causing an ATP-dependent effect in vitro. Second, when we measured Spc105-6A kinetochores in control experiments, without adenosine or with ADP, their rupture strengths were high like wild-type kinetochores. The strength of ADP-treated Spc105-6A kinetochores (8.7 pN), for example, was statistically indistinguishable from that of ADP-treated wild-type kinetochores (8.7 pN, p = 0.27 based on a log-rank test). The wild-type-like behavior of untreated and mock-treated Spc105-6A kinetochores indicates that their composition is not affected in a manner that significantly impacts kinetochore-microtubule strength.

In general, it would have been informative to complement the data presented here with a mass spec analysis of the composition of kinetochore particles, at least for the experiments that are most relevant to the conclusions. For instance, the composition of the Ndc80-8A kinetochore particles is assumed to be similar to that of wild type kinetochores based on gel silver staining (Fig. S4A; note also that ndc80-8A particles are compared to ndc80-8D particles and not to wild type particles). However, the authors previously showed that kinetochore particles purified from dad1-1 mutant cells (affecting the Dam1 complex) have an apparently identical composition to particles purified from wild type cells by silver staining, yet they display significantly lower resistance to the rupture strength in vitro (Akyioshi et al., 2010). What is the status of the Dam1 complex (or other kinetochore subunits) in kinetochores purified from ndc80-8A/-8D or spc105-6A cells relative to wild type kinetochore particles?

Response: We agree that further characterization of the kinetochore particle composition would be valuable and propose to further analyze the composition by purifying wild-type, Ndc80-8A, Ndc80-8D and Spc105-6A kinetochores and performing immunoblotting against the Dam1 complex. In addition, we will analyze the Ndc80-8A and Ndc80-8D kinetochores by mass spectrometry and report a qualitative analysis of the relative amounts of each kinetochore subcomplex in the revised manuscript supplementary data.

**Minor comment:**

I believe that the right reference for the sentence in the Discussion "If Aurora B is defective, for example, the opposing phosphatase PP1 prematurely localizes to kinetochores" is Liu et al. 2010.

Response: We had cited the reference showing this effect in yeast, since our work was performed in yeast. We will also add the Liu et al paper, which showed the same result in human cells.

Reviewer #2 (Significance (Required)):

Although the experiments are well designed and the conclusions are mainly supported by the data, the question arises as to what extent the in vitro assays recapitulate, at least partly, what happens in vivo. An emblematic example is the involvement of Spc105 in the error correction pathway. The Biggins lab previously showed that Spc105 phosphorylation by Mps1 and subsequent Bub1 recruitment is not only essential for the spindle assembly checkpoint, but is also crucial for chromosome segregation in vivo, as shown by slow-growth phenotype and aneuploidy of the spc105-6A non-phosphorylatable mutant (London et al., 2012). Additionally, a recent paper showed that Spc105 is a crucial Mps1 target in chromosome biorientation (Benzi et al., 2020).

In sharp contrast, the ndc80-8A mutant, which in vitro completely erases the ability of Mps1 to destabilise kinetochore-microtubule attachments, displays no growth defects in otherwise wild type cells and only modestly enhances chromosome mis-segregation in a mutant affecting an intrinsic correction pathway (stu2ccΔ). The N-terminal part of Ndc80 (aa 1-116) containing the aforementioned eight phosphorylation sites can even be deleted altogether without any consequence on cell viability (Kemmler et al., 2009). Thus, although the in vitro assays presented here produced clear-cut and reproducible results, their physiological relevance in vivo remains unclear.

Left apart this criticism, the manuscript has several merits outlined above and will be of interest for people working in the fields of chromosome segregation, kinetochore assembly, spindle assembly checkpoint, etc.

Expertise of this reviewer: mitosis and related checkpoints

Response: We are grateful to the reviewer for carefully reading our manuscript and detailing their concerns. We agree that it can be challenging to establish the physiological relevance of experiments performed in vitro. However, our in vitro approach allowed the effects of Mps1 specifically on kinetochore-microtubule attachment strength to be disentangled from its numerous other effects in vivo. In our view, the relatively mild phenotypes associated with mutants in the Mps1 phosphorylation sites on the Ndc80 tail are consistent with similarly mild phenotypes of mutants in the Aurora B phosphorylation sites on the Ndc80 tail. In both cases, this appears to be due to additional error correction pathways that compensate in vivo.

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

Sarangapani, Koch, Nelson et al. applied a combination of in vitro biophysical assays with purified kinetochore particles and in vivo analyses to investigate the contribution of Mps1 kinase to kinetochore-microtubule (KT-MT) attachment stability and error correction.

The manuscript is well written and the authors nicely highlight the facts that 1) the focus of the field has long been on the contribution of Aurora kinases (Ipl1 in budding yeast) to attachment stability and error correction, and 2) it has been difficult to assess the relative contributions of Aurora versus Mps1 kinases in cell-based experiments. The authors note that their KT particle assay is uniquely positioned to address this gap in our understanding and to specifically isolate the contribution of Mps1 to attachment stability in vitro. The findings are well-presented and quite convincing although I have several comments that should be addressed to strengthen the central conclusion that this work has isolated the contribution of Mps1 in their assays.

**Major points:**

1) I think it is important to note that reversine is not specific for Mps1 kinase - although it is typically presented as such in the field. It was initially identified as an Aurora kinase inhibitor (IC50: ~25nM (Aurora B) - 900nM (Aurora A)) that turned out be an even more potent Mps1 inhibitor (IC50 ~6nM). I have concerns that the in vitro assays were done with 5 uM reversine - a concentration so high that it could certainly inhibit any Ipl1 that is present (see comment 3 below) and possibly even inhibit Bub1 activity as Santaguida et al. (JCB, 2010) measured an IC50 >1uM for Bub1 inhibition. It is important to complement/confirm the chemical inhibitor experiment by repeating the rupture assays +/- ATP in KT particles purified from the mps1-1 strain (shown in Figure 6).

Response: We agree that reversine is not necessarily specific for Mps1 and this concern was also brought up by Reviewer 1. Because Mps1 is the only kinase activity that co-purifies with the isolated kinetochore particles, we expect reversine to inhibit only Mps1 in our in vitro assays. However, to further address this point, we will add rupture force assays using kinetochores purified from mps1-1 mutant cells to the revised manuscript. We have already performed these experiments and they confirm that kinetochores lacking Mps1 do not undergo ATP-dependent weakening. We did not put this data into the original submission because the experiment needs to be performed differently due to altered Dam1 levels. But we will clarify the changes in the materials and methods and add the data to a supplementary figure.

2) If the ATP-mediated reduction on rupture force is lost in the mps1-1 KT particles, which will also lack Bub1 kinase, then preserving the ATP-dependent reduction in rupture force from KT particles purified from the Bub1delta mutant strain would be strong evidence that the contribution of Mps1 kinase has been disentangled from other kinases in this assay.

Response: Although Mps1 recruits Bub1, we think it is unlikely that we are assaying Bub1 kinase activity in our in vitroexperiments. We cannot detect Bub1 activity on the purified kinetochores using a sensitive radioactive kinase assay (London et al, Curr Bio 2011), and the levels of Bub1 in our kinetochore purifications are very low (for example, see Akiyoshi et al, Nature, 2010). However, we agree with the reviewer that this caveat should be mentioned and will add this point to the revised text for clarity.

3) Recent work has shown that Sli15-Ipl1 interacts with and is recruited to KTs by the COMA complex (Rodriguez et al., Curr Biol, 2019 and Fischbock-Halwachs et al., eLife 2019) and that this population of Ipl1 is important for accurate chromosome segregation as also shown 10 years prior by Knockleby and Vogel (Cell Cycle, 2009). I realize that this group previously showed (London et al., Curr Biol, 2012) that phosphorylation of KT particles was not affected when purified from the ipl1-321 mutants, but in light of the recent findings how sure are the authors that there is not any Sli15-Ipl1 in the preparations? I think commenting on this would be worthwhile.

Response: We have not detected Ipl1 or Sli15 in the numerous mass spectrometry experiments we have performed on the kinetochore purifications. In addition, we have been separately assaying the effects of Ipl1 phosphorylation on kinetochores for another project (de Regt, https://doi.org/10.1101/415992), which independently confirmed that the only detectable kinase activity in our kinetochore purifications is Mps1. We will add this additional reference to the manuscript.

4) Since the interplay between Mps1 and Aurora B are central to this story, the authors should expand upon the sentence on page 5 reading "While there is some evidence that Mps1 regulates Aurora B activity (Jelluma et al., 2010; Saurin et al., 2011; Tighe et al., 2008), significant data suggests it has an independent role in error correction and acts downstream of Aurora B (Hewitt et al., 2010; Maciejowski et al., 2010; Maure et al., 2007; Meyer et al., 2013; Santaguida et al., 2010)." I am not entirely convinced that the in vivo experiments presented here differentiate as to whether Mps1 is upstream from Ipl1 or whether they are acting independently? For example, phosphorylation of T74 looks to be completely lost in figure 6E (although it's difficult to tell since the blot for T74P is very smeary). If they are acting independently in error correction then Ipl1 should still be able to phosphorylate T74 in this condition. However, if the P-T74 really is lost completely in the mcd1-1 cells then this suggests to me that Ipl1 is downstream of Mps1 in this live cell error correction assay.

Response: We thank the reviewer for bringing this to our attention. We did not mean to imply that Mps1 is downstream from Aurora B in budding yeast and were intending only to summarize findings from the literature regarding other organisms. We will revise this section of the text to make that point clearer, and we agree that the order of events remains unresolved. In addition, we will note that Mps1 does not eliminate the phosphorylation detected by the T74 antibody in the revision, to avoid misconceptions about the order of events.

**Other points:**

1) On p.8 "a median strength of 7.5 pN, similar to untreated and ADP-treated kinetochores". Similar is vague so I'm curious as to whether there a statistically significant difference between this and the 9.8 pN and 8.7 pN measured in the other conditions. If so this could be explained by partial dephosphorylation with the phosphatase.

Response: The quoted phrase refers to the 7.5-pN strength measured when λ-phosphatase was included together with ATP (data from Fig. 1D and Supp. Fig. S1B). P-values computed from comparisons of survival plots using the log-rank test show that this strength was not significantly different from the ADP-treated wild-type (8.7 pN, p = 0.06), nor was it significantly different from the ADP- and MnCl2-treated wild-type (8.1 pN, p = 0.35). However, it was barely significantly different from MnCl2-treated wild-type (8.6 pN, p = 0.03), and it was more significantly different from untreated wild-type (9.8 pN, p = 0.0007). With the revised manuscript, we will include a supplemental table with p-values computed from log-rank tests for all the key statistical comparisons, including those mentioned here.

2) On p.19 the authors note that Aurora A phosphorylates Ndc80 tail during mitosis. Ye et al. (Curr Biol, 2015) also showed that Aurora A can phosphorylate Aurora B sites and that this activity "converges" at the tail to weaken attachments during error correction.

Response: We will add the reference and thank the reviewer for pointing out this omission.

3) Optional: I am curious as to whether the addition of ATP to the Ndc80-8D particles further reduces the rupture force. If so then other sites may also be in play.

Response: We agree this is an interesting question but we have not yet performed those assays and agree it might be worthwhile for a future study.

4) Please comment on why MnCl2 is used in the rupture assays in Figure S1. I saw no mention of this in the main text.

Response: We include MnCl2 in the assay because it is required for phosphatase activity and will add this point to the legend of supplementary Figure S1.

5) Consider moving S2 A and B to Figure 3 C and D. This is an interesting result and would go well in the main figure next to the significantly reduced rupture force measurements for the 6A mutant so the reader doesn't have to dig into the supplemental for the data providing this reasonable explanation for the rupture force result.

Response: We thank the reviewer for this suggestion and will move S2A and S2B into Figure 3.

Reviewer #3 (Significance (Required)):

The significance of this relates to focusing on an important phenomenon - error correction - and in looking beyond the traditional focus of the field on Aurora kinases to Mps1 kinase, which is largely implicated in checkpoint signaling. Disentangling the contributions of these two players is an important advance.

The work will be of interest to audiences interested in: kinases, cell division, checkpoints, kinetochore biology, biophysics

The above areas of interest overlap with my expertise.

Response: We thank the reviewer for their enthusiasm for our experiments that help distinguish kinase activities and thus contribute to understanding the process of error correction.

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Referee #3

Evidence, reproducibility and clarity

Sarangapani, Koch, Nelson et al. applied a combination of in vitro biophysical assays with purified kinetochore particles and in vivo analyses to investigate the contribution of Mps1 kinase to kinetochore-microtubule (KT-MT) attachment stability and error correction. The manuscript is well written and the authors nicely highlight the facts that 1) the focus of the field has long been on the contribution of Aurora kinases (Ipl1 in budding yeast) to attachment stability and error correction, and 2) it has been difficult to assess the relative contributions of Aurora versus Mps1 kinases in cell-based experiments. The authors note that their KT particle assay is uniquely positioned to address this gap in our understanding and to specifically isolate the contribution of Mps1 to attachment stability in vitro. The findings are well-presented and quite convincing although I have several comments that should be addressed to strengthen the central conclusion that this work has isolated the contribution of Mps1 in their assays.

Major points:

1) I think it is important to note that reversine is not specific for Mps1 kinase - although it is typically presented as such in the field. It was initially identified as an Aurora kinase inhibitor (IC50: ~25nM (Aurora B) - 900nM (Aurora A)) that turned out be an even more potent Mps1 inhibitor (IC50 ~6nM). I have concerns that the in vitro assays were done with 5 uM reversine - a concentration so high that it could certainly inhibit any Ipl1 that is present (see comment 3 below) and possibly even inhibit Bub1 activity as Santaguida et al. (JCB, 2010) measured an IC50 >1uM for Bub1 inhibition. It is important to complement/confirm the chemical inhibitor experiment by repeating the rupture assays +/- ATP in KT particles purified from the mps1-1 strain (shown in Figure 6).

2) If the ATP-mediated reduction on rupture force is lost in the mps1-1 KT particles, which will also lack Bub1 kinase, then preserving the ATP-dependent reduction in rupture force from KT particles purified from the Bub1delta mutant strain would be strong evidence that the contribution of Mps1 kinase has been disentangled from other kinases in this assay.

3) Recent work has shown that Sli15-Ipl1 interacts with and is recruited to KTs by the COMA complex (Rodriguez et al., Curr Biol, 2019 and Fischbock-Halwachs et al., eLife 2019) and that this population of Ipl1 is important for accurate chromosome segregation as also shown 10 years prior by Knockleby and Vogel (Cell Cycle, 2009). I realize that this group previously showed (London et al., Curr Biol, 2012) that phosphorylation of KT particles was not affected when purified from the ipl1-321 mutants, but in light of the recent findings how sure are the authors that there is not any Sli15-Ipl1 in the preparations? I think commenting on this would be worthwhile.

4) Since the interplay between Mps1 and Aurora B are central to this story, the authors should expand upon the sentence on page 5 reading "While there is some evidence that Mps1 regulates Aurora B activity (Jelluma et al., 2010; Saurin et al., 2011; Tighe et al., 2008), significant data suggests it has an independent role in error correction and acts downstream of Aurora B (Hewitt et al., 2010; Maciejowski et al., 2010; Maure et al., 2007; Meyer et al., 2013; Santaguida et al., 2010)." I am not entirely convinced that the in vivo experiments presented here differentiate as to whether Mps1 is upstream from Ipl1 or whether they are acting independently? For example, phosphorylation of T74 looks to be completely lost in figure 6E (although it's difficult to tell since the blot for T74P is very smeary). If they are acting independently in error correction then Ipl1 should still be able to phosphorylate T74 in this condition. However, if the P-T74 really is lost completely in the mcd1-1 cells then this suggests to me that Ipl1 is downstream of Mps1 in this live cell error correction assay.

Other points:

1) On p.8 "a median strength of 7.5 pN, similar to untreated and ADP-treated kinetochores". Similar is vague so I'm curious as to whether there a statistically significant difference between this and the 9.8 pN and 8.7 pN measured in the other conditions. If so this could be explained by partial dephosphorylation with the phosphatase.

2) On p.19 the authors note that Aurora A phosphorylates Ndc80 tail during mitosis. Ye et al. (Curr Biol, 2015) also showed that Aurora A can phosphorylate Aurora B sites and that this activity "converges" at the tail to weaken attachments during error correction.

3) Optional: I am curious as to whether the addition of ATP to the Ndc80-8D particles further reduces the rupture force. If so then other sites may also be in play.

4) Please comment on why MnCl2 is used in the rupture assays in Figure S1. I saw no mention of this in the main text.

5) Consider moving S2 A and B to Figure 3 C and D. This is an interesting result and would go well in the main figure next to the significantly reduced rupture force measurements for the 6A mutant so the reader doesn't have to dig into the supplemental for the data providing this reasonable explanation for the rupture force result.

Significance

The significance of this relates to focusing on an important phenomenon - error correction - and in looking beyond the traditional focus of the field on Aurora kinases to Mps1 kinase, which is largely implicated in checkpoint signaling. Disentangling the contributions of these two players is an important advance.

The work will be of interest to audiences interested in: kinases, cell division, checkpoints, kinetochore biology, biophysics

The above areas of interest overlap with my expertise.

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Referee #2

Evidence, reproducibility and clarity

This paper focusses on the mechanisms underlying chromosome biorientation in mitosis, an essential process that warrants equal chromosome segregation to the dividing cells. Correction of improper kinetochore-microtubule attachments relies on two conserved protein kinases, Aurora B and Mps1, that detach kinetochores that are not under tension in order to provide them with a second opportunity to establish bipolar connections. In vivo, Aurora B and Mps1 have intertwined functions and share some common targets. For this reason, despite the large body of literature on the subject, their precise roles in chromosome biorientation have been difficult to tease apart.

The authors take advantage of an in vitro reconstitution assay that they previously published (Akyioshi et al., 2010) to identify the critical target(s) of Mps1 in weakening kinetochore-microtubule connections. The assay uses kinetochore particles purified from budding yeast cells that bear Mps1 but are notably deprived of Aurora B. Upon addition of ATP to activate the co-purified kinases (e.g. Mps1), kinetochores are added to coverslip-anchored microtubules to which they attach laterally. Through a laser trap, kinetochores are brought to the microtubule plus-end and pulled with increasing force until the kinetochore detaches, which allows measurements of the average rupture forces that reflect the strength of the attachments. The approach is straightforward and potentially very powerful, first because it provides a simplified experimental set-up in comparison to the cellular context, and second because it directly measures the impact of protein phosphorylation on the strength of attachments.

The authors convincingly show that Mps1-dependent phosphorylation of the N-terminal part of Ndc80 significantly weakens the strength of kinetochore-microtubule attachments in vitro, while phosphorylation of other known Mps1 targets, such as Spc105, does not seem to have an effect. Eight phosphorylation sites in Ndc80, which were previously identified as Mps1-dependent phosphorylation sites (Kemmler et al., 2009), are shown to be critical to destabilise kinetochore-microtubule attachments in the in vitro reconstitution assays. The authors also present evidence for a moderate involvement of Ndc80 phosphorylation by Mps1 in correcting improper attachments in vivo, suggesting that additional mechanisms are physiologically relevant for error correction.

The experiments are mostly well designed, the data are solid and support the main conclusions. However, to my opinion additional experiments could be performed, as outlined below, to strengthen the physiological relevance of the main findings and corroborate some of the conclusions.

Major points:

1. Given the partially overlapping function of Mps1 and Ipl1 (Aurora B) in error correction, the ndc80-8A mutant should display synthetic growth and chromosome mis-segregation defects with ipl1 temperature-sensitive alleles. Conversely, the ndc80-8D mutant should suppress the lethality at high temperatures of mps1-3 mutant cells, which were recently shown to be defective in chromosome biorientation (Benzi et al., 2020). Finally, chromosome mono-orientation could become apparent in ndc80-8A cells upon a transient treatment with microtubule-depolymerising drugs, which should amplify the cellular need for error correction.
2. The authors show that Mps1-dependent phosphorylation of Ndc80 is not involved in the spindle assembly checkpoint, a conclusion that contradicts a previous report (Kemmler et al., 2009). They also find, in contrast with the same report, that the lethal phenotype of the ndc80-14D phospho-mimetic mutant cannot be rescued by disabling the spindle checkpoint. In my opinion, Kemmler et al. convincingly showed, through a number of different experimental approaches, that ndc80-14D cells die because of spindle checkpoint hyperactivation. Not only deletion of checkpoint genes was shown to rescue the lethality, but re-introduction of a wild type copy of the deleted checkpoint gene reinstated lethality. Thus, the explanation invoked here that spontaneous suppressing mutations could underlie the viability of ndc80-14D SAC-deficient mutants is not consistent with the published observations. A thorough examination by the authors of the phenotype of ndc80-14D cells in their hands should be carried out to support these conflicting conclusions. If authors find that ndc80-14D cells actually die because of chromosome mono-orientation, then this would highlight an important function for some or all the six additional phosphorylation sites, relative to the ndc80-8D mutant, for chromosome biorientation in vivo.
3. The conclusion that Spc105 phosphorylation by Mps1 is not required for the Mps1-mediated weakening of kinetochore attachments in vitro is based on the comparison between kinetochore particles bearing wild type, untagged Spc105 and particles bearing non-phosphorylatable Spc105-6A tagged at the C-terminus with twelve myc epitopes. Thus, the presence of the tag could obliterate the effects of the mutations in the phosphorylation sites by destabilising kinetochore-microtubule attachments in the presence of ATP. Consistent with this conclusion, Spc105-6A-12myc-bearing kinetochores withstand lower rupture forces than Spc105-bearing kinetochores upon ATP addition. Furthermore, Spc105-6A-12myc kinetochore particles show an interacting protein at MW above 150 KD that is not present in wild type particles (Fig. S2A), suggesting that either the tag or the mutations might affect kinetochore composition. Thus, this set of experiments should be repeated using Spc105-6A kinetochore particles lacking the tag.
4. In general, it would have been informative to complement the data presented here with a mass spec analysis of the composition of kinetochore particles, at least for the experiments that are most relevant to the conclusions. For instance, the composition of the Ndc80-8A kinetochore particles is assumed to be similar to that of wild type kinetochores based on gel silver staining (Fig. S4A; note also that ndc80-8A particles are compared to ndc80-8D particles and not to wild type particles). However, the authors previously showed that kinetochore particles purified from dad1-1 mutant cells (affecting the Dam1 complex) have an apparently identical composition to particles purified from wild type cells by silver staining, yet they display significantly lower resistance to the rupture strength in vitro (Akyioshi et al., 2010). What is the status of the Dam1 complex (or other kinetochore subunits) in kinetochores purified from ndc80-8A/-8D or spc105-6A cells relative to wild type kinetochore particles?

Minor comment:

I believe that the right reference for the sentence in the Discussion "If Aurora B is defective, for example, the opposing phosphatase PP1 prematurely localizes to kinetochores" is Liu et al. 2010.

Significance

Although the experiments are well designed and the conclusions are mainly supported by the data, the question arises as to what extent the in vitro assays recapitulate, at least partly, what happens in vivo. An emblematic example is the involvement of Spc105 in the error correction pathway. The Biggins lab previously showed that Spc105 phosphorylation by Mps1 and subsequent Bub1 recruitment is not only essential for the spindle assembly checkpoint, but is also crucial for chromosome segregation in vivo, as shown by slow-growth phenotype and aneuploidy of the spc105-6A non-phosphorylatable mutant (London et al., 2012). Additionally, a recent paper showed that Spc105 is a crucial Mps1 target in chromosome biorientation (Benzi et al., 2020).

In sharp contrast, the ndc80-8A mutant, which in vitro completely erases the ability of Mps1 to destabilise kinetochore-microtubule attachments, displays no growth defects in otherwise wild type cells and only modestly enhances chromosome mis-segregation in a mutant affecting an intrinsic correction pathway (stu2ccΔ). The N-terminal part of Ndc80 (aa 1-116) containing the aforementioned eight phosphorylation sites can even be deleted altogether without any consequence on cell viability (Kemmler et al., 2009). Thus, although the in vitro assays presented here produced clear-cut and reproducible results, their physiological relevance in vivo remains unclear.

Left apart this criticism, the manuscript has several merits outlined above and will be of interest for people working in the fields of chromosome segregation, kinetochore assembly, spindle assembly checkpoint, etc.

Expertise of this reviewer: mitosis and related checkpoints

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Referee #1

Evidence, reproducibility and clarity

The authors use a combination of Dsn1-Flag kinetochore purification from yeast extracts and laser trapping experiments (as in a number of previous studies), to study the effect of Mps1-dependent phosphorylation on reconstituted kinetochore-microtubule attachments in vitro. They complement this analysis with genetic experiments characterizing the effects of non-Mps1 phosphorylatable mutants on checkpoint activity and chromosome segregation in yeast. The authors had previously shown that Mps1 is the major kinase activity that copurifies with Dsn1-Flag in their purification scheme. They now investigate the effect of adding ATP and thereby allowing Mps1 phosphorylation in the reconstituted system. They show that addition of ATP decreases the rupture force of kinetochore-microtubule attachments, meaning it weakens the strength of the attachment. This effect can be negated either by inhibiting Mps1 with reversine, or by providing kinetochores in which the Mps1 phosphorylation sites on Ndc80 (most of them in the N-terminal tail) have been mutated to alanine. Thus, similar to the activity of Ipl1, Mps1 phosphorylation of the Ndc80 N-tail (which is known to be important for for full MT affinity) weakens kinetochore-microtubule attachments.

Cellular experiments demonstrate that non-Mps1 phosphorylatable Ndc80 14-A mutants have a functional mitotic checkpoint (contrary to previous claims by Kemmler et al., 2009), but show synthetic sickness with stu2 alleles that are involved in error correction.

Major points:

Within the framework of this experimental setting, the study as presented is logical and clear. The conclusions regarding the effect of Mps1 in this reconstituted system are overall well supported by the data. I have a couple of major and some minor points that can further improve data interpretation and should therefore be considered:

1. In previous publications (e.g. Gutierrez et al., Current Biology 2020), the authors have reported that the Dam1 complex, an established Mps1 substrate, is required for full attachment strength in this system. Are the effects of Mps1-dependent Ndc80 phosphorylation and Dam1 independent from one another? For example would dad1-1 or non Cdk1 phosphorylatable Dam1 complex further reduce the rupture force in ATP? Or does Mps1 phosphorylation affect, for example, Dam1 binding to Ndc80?
2. What is the effect of ATP on initial binding events? Are there differences in the fraction of beads that spontaneously attach laterally at the start of the experiment? This may allow to draw conclusions whether any kind of binding or specifically force-generating end-on attachments are affected by ATP.
3. Ndc80-8D has low attachment strength, consistent with lowered MT affinity of the phospho-mimetic Ndc80 tail. Interestingly, Supplementary Figure S4B shows that the amount of Cse4 in the pull-down western appears substantially reduced in 8D vs 8A or wt. Is the amount of co-purified inner kinetochore affected in this mutant? This may be an alternative explanation for decreased attachment strength, for example if the fraction of "full" or "complete" kinetochores may be reduced. Could this also happen upon inclusion of ATP?

Minor points:

page 13 (heading): "Weakening occurs via phosphorylation...". Probably good to mention what is weakened ("Weakening of kinetochore-microtubule attachments occurs via phosphorylation...".

page 14/Figure5C: Median Rupture Force for Ndc80-8D is 4.8 pN according to the text. In the graph it looks like >5 pN.

page 23: comma missing between T21 S37 and T47 (should be T21, S37 and T47)

page 24/25: different spelling of G1 (sometimes with subscript)

page 24/25: ug instead of µg

page 28: Figure 5B instead of Figure 5A

Figure 6A: Lambda-Phosphatase treatment for 20 minutes according to figure legend and 30 minutes according to Material and Methods section.

Figure 6E: One should not draw any conclusions from the anti-phospho T47 blot here, the quality is simply too poor to allow a statement regarding an mps1-1 effect

Figure 6: Labelling T47P misleading (Proline substitution?, use pT47 instead)

Figure 6F: Make clear in the labelling that a stu2-AID background is used here, makes it easier to understand why Auxin is used here.

how specific is reversine for yeast Mps1? I have not seen any data on this in previous publications.

additional genetic interactions might be informative, if Ndc80-8D has weakenend attachments, it may have synthetic effects with other mutants (dam1?), conversely, ndc80-8A may show genetic interactions with ipl1 alleles, for example.

Significance

The study adds to the characterization of the effects of Mps1 kinase on kinetochore-microtubule attachments and characterizes the cellular phenotypes of non-Mps1 phosphorylatable Ndc80 mutants. The major conceptual point that Mps1 phosphorylation can weaken kinetochore-microtubule interactions and thereby contributes to error correction in a manner similar to Ipl1 has previously been made in the literature. Maure et al., (Tanaka lab, 2007, Current Biology) have characterized the effects of mps1 mutant alleles on biorientation of authentic chromosomes and on replicated/unreplicated mini-chromosomes. In particular the experiments with unreplicated mini-chromosomes have revealed less frequent detachment in mps1 mutants, demonstrating that Mps1 activity is required to release attachments that are not under tension.

Another benefit of this study is that it puts the Kemmler 2009 EMBO J. paper into perspective and corrects some of it claims. In particular the notion of sustained checkpoint activation in the Mps1 phospho-mimetic Ndc80-14D mutant, whose lethality was claimed to be rescued by checkpoint deletion. It is confirmed here that the allele is lethal, but cannot be alleviated by simultaneous checkpoint deletion. Conversely, the Ndc80-14A mutant is shown to have a functional checkpoint. One could argue that since the publication of the Kemmler paper, the idea of requirement of Mps1 phosphorylation on Ndc80 for checkpoint activity has not gained any traction in the field, but it's still useful for the field to put some of these earlier claims into perspective. The paper will therefore be interesting to researchers working on mechanisms of chromosome segregation and error correction.

From my background I cannot comment on technical details of the biophysical force spectroscopy experiments (laser trapping), but I have no reason to doubt that the authors accurately report their findings.

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Reply to the reviewers

General comments:

We thank the reviewers for their constructive critique and are pleased they see the results as interesting and of general relevance. We also acknowledge their concerns on the issue of whether all claims are supported by sufficiently strong data. Our careful reading and analysis of the points that are raised suggest there are different reasons for the different cases that are brought up:

1. Misunderstandings, due to lack of clarity on our side. Example: When talking about ‘reduced actin’, our wording focussed on the endosome-associated actin (partly out of consideration for the fact the actual measurements we show come from the area around the endosomes, so we did not want to make any stronger claims), even though we should have made it clear that other areas of the cell tip are also affected. This will be addressed by clearer explanations.

Ill-advised wording we chose that is or can be seen as overinterpretation.

Example: ‘anchoring’ of actin at endosomes. We had not intended to infer anything about specific anchoring sites or mechanisms. We should have used a more neutral term, such as ‘associate with’ or accumulate around’ for the description. This and other cases can also be resolved by rewriting and better wording.

Anecdotal evidence or insufficient data.

Example: Images of phalloidin stainings depicting how actin is organized around late endosomes in control embryos. These and other cases will be addressed by adding further examples and additional quantification.

Finally, one suggestion was made for obtaining additional experimental data, which would involve laser ablation. While the experiment would provide an interesting extension of our findings, we will sadly not be in a position to carry it out in the foreseeable future, as explained below. We hope the referees will agree that our now extended discussion addresses the point in question sufficiently to support the conclusions from the experiments we do present.

These and all other points are addressed individually below. We highlighted the corresponding text changes in the manuscript file for the reviewers to identify them more easily.

Detailed responses:

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

**Summary**

Rios-Barrera and Leptin investigate the formation and guidance of the subcellular tube that forms in the terminal cell of the dorsal branches of the Drosophila tracheal system. In previous work the authors documented the presence of late endosomes at the tip of the growing terminal cell, ahead of the forming subcellular tube, which are involved in membrane recycling {Mathew, 2020 #1407}. In this present work they analyze the organization of the actin cytoskeleton in the tip terminal cell, in relation with the late endosomes, and assess the guidance of the subcellular tube. They find that the presence and localization of late endosomes play a role in tube guidance. They also find that late endosomes recruit actin around them, mediated by the activity of the actin polymerization regulator Wash, which is recruited to maturing late endosomes. When Wash activity is decreased, actin around late endosomes is decreased and tube guidance is compromised. Based on this observation, laser ablation experiments of actin ahead of the tube and actin staining at the tip of the terminal cell, the authors propose an exciting model: late endosomes recruit actin, which connects the actin pool of the basal membrane and the actin pool of the apical (subcellular tube) membrane thereby directing tube growth and guidance.

The manuscript is well-written and well-presented, the images and movies are of high quality and the experimental data, which is technically challenging, is very good and sufficiently replicated.

**Major comments:**

1. A critical point in the model that the authors put forward (which is also contained in the title and abstract) is that actin organized at late endosomes anchors apical and basal actin cortices. However, there is no clear and conclusive evidence for this. Clear evidence in this direction should be provided to propose it as a mechanism (as it is in the text, particularly in the first sentences of the discussion) and imply it in the title. The authors show endogenous actin around late endosomes and actin fibers at the tip of the terminal branch. However, at the level of resolution presented (Fig 3A,B), it is not possible to determine whether the different actin populations are actually "anchored". I suggest to present stronger data supporting this important conclusion.

In the same direction, it would be critical to show that this anchoring of actin fibers is disturbed when actin enrichment at the late endosome is perturbed (see also point 5).

Actually, the authors show that when Vha or Wash activity are downregulated actin accumulation around the CD4 vesicles decrease. However, this experiment has a few inconveniences. First, it is difficult to determine levels of a construct that is overexpressed (UAS-utr::GFP). Could the authors use phalloidin or an actin antibody to confirm the result?

Second, I find the result difficult to interpret. In the images provided I see a general decrease of actin (UtrGFP) at the tip, not only around the CD4 vesicles (Fig 6D,F) . Are these mutant conditions also affecting the rest of actin pools? If this is the case, can the authors attribute the defects exclusively to the abnormal recruitment of actin to the late endosomes?

Most importantly, the authors should analyze the pattern of actin distribution (labelling endogenous actin) and determine a possible loss of "anchoring" of fibers when late endosome maturation is perturbed.

We understand the referee addresses three issues here, to which we will respond in turn below:

• As already mentioned above, the referee interprets the term ‘anchoring’ in a more specific meaning than we had intended it to have. We obviously have to rephrase.
• A technical critique of the use of an overexpressed construct to visualize actin, which in turn has two sub-points: potential physiological effects on actin, and potentially inaccurate localisation. Both are valid points, but in our view do not undermine our conclusions. We will raise and discuss these concerns in our revised text.
• The specificity of the effects of reducing Vha and Wash of function on actin associated with endosomes versus throughout the growth cone of the cell – a very good point, about which we should have been much clearer and now will be. (a) Considering the use of the term ‘anchoring’, and the referee’s concern over whether we provide the appropriate evidence gave us with a good starting point to re-think what we actually show and how it can be interpreted.

Put in neutral terms, what [we felt] we had shown was an accumulation or enrichment of actin around endosomes that was dependent on proper functioning of Vha and Wash.

We agree that the term ‘anchoring’ cannot be justified by the description of actin localisation alone. The term implies a physical (and perhaps strong or long term) interaction between the endosome and the surrounding actin.

We see a strong enrichment of actin around endosomes, including in experiments in which we use phalloidin to visualize actin (Fig. 3B). The resolution of our images is approximately 200nm so they are able to reveal the very close association. The question is what the mechanistic basis for this closeness is. It is unlikely to be random, as shown by a quantification we have now included (Figure S3C). It is difficult to imagine how it could persist without at least transient physical interaction between the two components. The association is indeed highly dynamic and is constantly being re-established. This must mean that something ‘attracts’ actin to endosomes, most likely a molecule that is itself associated with endosomes. The presence or accessibility of such a molecule depends on the proper maturation of endosomes, as shown by the results of reducing Vha activity. And the ability of actin to associate depends on Wash. Together these findings suggest to us the existence of a (dynamic) molecular link between the endosomes and the actin network.

In order not to give the impression that we are claiming a permanent ‘anchor’, we now use more general terms such as ‘associates’ or ‘accumulates’, but also include the clarification on our thinking in the text. Furthermore, to illustrate a representative range of cases, we will add more examples of late endosomes and the actin meshwork surrounding them (Figure S3A, B). These images should give a broader reflection of the actin populations and their dynamism during tube growth.

(b) A major reason why we use live imaging with actin reporters is that the distribution of actin around late endosomes and the tip compartment in general is very dynamic, so capturing cells at the right time point can be challenging from fixed samples. This problem is exacerbated by a technical limitation: For the actin cytoskeleton to be well preserved during fixation, embryos have to be manually dechorionated which limits the throughput of the experiment. We therefore found that analysing cells over time is more informative than analysing cells fixed at a given time point.

As the reviewer points out, using an overexpressed reporter can have drawbacks. With regard to the problem of not representing the endogenous distribution faithfully, this can be the case when making statements about the absolute distribution. However, what we are looking at here is not absolute quantities of actin but relative changes in the area of interest with respect to other, unaffected regions of the cells, and then comparing these between mutant conditions and the control. We do this by normalizing the signal to the levels seen in the subcellular tube, using it as an internal control that allows us to adjust for variation in expression levels.

There is on case where such a normalization could be problematic, and that is when comparing actin levels in cells expressing bitesize RNAi, because Bitesize is itself involved in organizing the actin cytoskeleton in the tube membrane (JayaNandanan et al., 2014). However, in this experiment, the analysis still shows that actin levels at late endosomes do not correlate with the tube misguidance phenotype.

With regard to potential physiological effects of an over-expressed construct, some of the commonly used actin reporters have subtle effects on actin physiology, whereas Utr-ABD has negligible or no effects on the actin cytoskeleton, and it also reproduces actin dynamics faithfully (Spracklen et al., 2014). It is therefore generally considered the most reliable tool for live imaging of actin in Drosophila.

We have adapted the text and commented on these issues and hoped we have achieved more clarity.

(c) We agree that when Vha or Wash are downregulated, actin levels are overall reduced in the growth cone of the cells, while this is not the case in other regions, for example at the base of the cell. Although we had not explicitly stated this (but now will), this is a further indication that the different actin populations in the growing tip interact with each other.

For the downregulation of Wash, this could potentially have been due to a direct effect of Wash on the apical and basal actin, but then we would have expected a similar result in other parts of the cell, including the cell body and the proximal part of the branch, but we do not see that. Even more importantly, the expression of Vha100-DN has the same effect and this cannot be easily explained by a direction action on actin. Together, these findings therefore indicate that depletion of actin around endosomes has a knock-on effect on the basal and apical actin cortex in the vicinity. We have included this reasoning in the paper now.

Another critical point in the model put forward by the authors is that late endosomes drive tube guidance. To test this point the authors use an elegant system to mislocalize Rab7 late endosomes.

However, the effects are not strong (1G), and only a proportion of branches show misguided tubes. Do the cases with a ventrally-guided tube in the experiment Rab7:YFP+/+ (Fig. 1G) have a CD4 endosome (with Rab7YFP) at the tip? This would help to explain the weak effect.

This is an excellent point, and it is indeed what we observe: all cells with ventrally guided tubes have a late endosome that is positive for the YRab7-nanobody-membrane complex at the tip of the cell (n=42), whereas only 2/3 of misguided tubes do (n = 12), and those always have the additional endosome at the tip of the misguide tube. As the reviewer suggests, this provides an obvious explanation for why these cells do not have a tube misguidance phenotype. We have added a representative image of this condition (Rab7::YFP+/+, ventrally-guided tube) in Figure 2 to illustrate the phenotype.

What is the cause that preventing proper endosome maturation and acidification leads to misguided tubes (rather than missing ones)?

A complete loss of late endosome activity would indeed result in the absence of the subcellular tube. However, we and others have shown that partial loss of function (as caused by RNAi) can have more subtle effects. For instance, fully blocking endocytosis using the shibire**ts line completely prevents proper tube extension (Mathew et al., 2020), but expression of a shibire RNAi still allows tube formation to proceed, albeit in a defective manner (Schottenfeld-Roames et al., 2014). Similarly, the misguidance phenotypes resulting from Vha downregulation likely reflect weaker loss of late endosome function. These perturbations would allow initial tube growth to proceed, but later on they would uncover this later function of the endocytic pathway in regulating tube guidance.

We believe that what we see as this weaker defect is an uncoupling of direction from growth per se. The cells still receive their growth-inducing signals from the FGF-receptor, and this leads to directed cell growth in the direction of the chemotactic signal. The normal trafficking of membrane material from the apical to the basal domain is also not disrupted. Thus, membrane keeps being added to both domains and both the tube and the basal domain continue to growth. However, the growing tube has been disconnected from its guiding structure at the tip of the cell (our speculation: because failed endosome maturation no longer allows proper actin coordination) and therefore follows a random path. We had not been sufficiently clear about this but have now hopefully remedied this in the text.

The authors indicate that downregulating Vha activity leads to defects in acidification, but late endosome-MVB normally form. It is intriguing to see extra CD4 vesicles (like in 1C or 6C).

Wouldn't we expect to see "normal" tip accumulation of CD4 vesicles only, and not extra ones? How relevant are these extra CD4 vesicles?

Wouldn't we expect to see "non functional" CD4 vesicles, unable to recruit actin and lead intracellular tube formation (i.e. no tube) rather than missguidances? (1D shows higher proportion of misguided tubes than no tubes)

Similarly, is Wash-RNAi producing extra CD4 vesicles (as observed in movie 5, fig 6E)?

We do not postulate that the late endosomes are morphologically normal – there are vesicles carrying the CD4 marker (which is only a membrane marker, not specific for endosomes), but the literature indicates that the endosomes do not undergo their normal maturations, and we would have no reason to claim otherwise. So we agree that the ones we see in the Vha-downregulated cells are not fully functional, and this is indeed confirmed by their inability to recruit actin.

With regard to the number of large CD4 vesicles at the tip, terminal cells can normally have from 1 to 3 in the growth cone, and the fact that the experimental cells we showed were at the upper range whereas the control at the lower end was pure chance. We have now quantified the number of vesicles in the abnormal conditions and see that there is no increase (Figure S5F).

Actin recruitment to late endosomes was already documented, where it plays a role in cargo trafficking.

The authors propose that Wash is recruited to late endosomes upon acidification where it would prime actin nucleation around the endosome. The authors indicate a decrease in Wash accumulation upon expression of Vha dominant negative. However, this decrease is not quantified. In addition, it is difficult to determine levels of a construct when this is overexpressed (UAS-Wash::GFP). It would be desirable to use antibodies against the endogenous protein (Wash in this case) to claim differences in accumulation in mutant conditions.

We have quantified the amount of Wash::GFP in CD4 vesicles. As mentioned, the vesicles are very dynamic, and so is their recruitment of Wash::GFP, and doing the analysis in the live cells is therefore more meaningful than extracting information from fixed samples, but we will also try to obtain the antibody for confirmation in fixed material. We appreciate that as discussed above for actin, results using overexpressed constructs have to be interpreted with care, but here again, we mitigate against this by assessing relative changes rather than absolute amounts and mitigate against misinterpretation by normalizing the signal to the one seen in the cytoplasm.

The results presented do not rule out a requirement of Wash in terminal branching which is not associated with the enrichment in the late endosomes. The genetic interaction observed with Shrub is also compatible with both proteins acting on terminal branching but in different/parallel mechanisms.

While the fact that downregulation of Vha has the same effect cannot be explained in this manner, we agree with the reviewer and will rephrase this section in the paper.

Laser ablation experiments

The laser ablation experiments are difficult to interpret.

First, it is unclear to me what the results exactly indicate. What does the recoil observed suggest? Does it fit with the expected tension exerted by a link of the actin cytoskeleton relayed by late endosomes?.

The observed recoil suggests that there was tension across the ablated area. The laser ablation experiments were one way to evaluate whether the actin cytoskeleton within the tip of the cell was continuous between the subcellular tube and the leading edge of the cell. Tension along this axis would support such a model. We assumed that if the actin cytoskeleton at the tip is continuous with both membrane compartments it was likely to be under tension, and our laser ablation experiments showed that is indeed the case. We have rewritten this section to make it clearer.

From the text and figure I don't understand how is the recoil calculated: retraction of the subcellular tube backwards? "enlargement" of the bleached area?

Briefly, we had used three measuring points: the backward displacement of (i) the subcellular tube and (ii) of the plasma membrane adjacent to the ablated area, which both retract towards the cell body, and we also measured (iii) the forward displacement of plasma membrane on the other side of the ablated area. We then calculated the average of these for each experiment.

However, we have now redone the evaluations of these experiments using PIV, an established method that is commonly used to calculate initial recoil after ablation and have explained this in the text.

Second, it is unclear to me what laser ablation actually ablates. Does it only affect actin? Or are also CD4-late endosomes and other tip structures affected?

The laser ablations with the conditions we use have in the past been shown to temporarily disrupt the actin cytoskeleton without otherwise damaging the cell (Rauzzi et al., 2015).

The ablations were done in cells that express the actin reporter Utr::GFP together with the membrane marker CD4::mIFP but we have no reason to believe that CD4 containing structures were damaged. For example, upon ablation, the CD4 vesicles in the ablated area are bleached, but in the recovery phase, we observe actin puncta in the positions where CD4 vesicles were originally located, suggesting that the vesicles themselves persist. Our interpretation of these observations is that the bleached CD4 vesicles do not recover their fluorescence (CD4::mIFP is an integral membrane protein and cannot simply be re-inserted within short periods), but they are still capable of recruiting actin. We have added a representative image of this to better describe the experiment (Fig. S4).

Third, is the recovery observed after ablation correlated with new actin recruitment around old or new late endosomes?

Actin rapidly reappears in the bleached area and the region that recoiled, where it is first seen in the basal cortex and filopodia. The tube re-extends towards the ablated area, and actin reassembles around the tube within seconds. During further recovery, actin reappears in puncta ahead of the tube and we assume that this is partly de novo assembly around the existing vesicles (Fig. S4A, B). At the same time, we also see new CD4 vesicles reaching the tip, so it is likely that both populations (old and new vesicles) mediate the recovery phase. We have added images of additional examples that illustrate these points.

Forth, I find the experiments in cells with secondary subcellular tubes very confusing and the explanations very speculative

The data on cuts in cells with tube duplications are indeed difficult to interpret, and because the emergence of secondary branches is unpredictable, it is not easy to obtain large numbers of observations. Figure S4 is another example of the response of these cells to the laser cut, and we will make clear that our interpretations are merely speculative.

Finally, and most importantly. I think that performing laser ablation experiments in mutant conditions that affect actin recruitment (VhaDN and Wash RNAi,....) would be very informative. One would expect to find a decrease in recoil. If this was the case, it would validate, on the one hand, that in control conditions there is a tension that depends (at least in part) on actin organization, and on the other hand it would show that when actin recruitment is affected tension decreases, supporting the "anchoring" model. I understand that laser ablation experiments are not easy to perform, but I think this would be a useful experiment.

To my understanding, as it stands, the laser ablation experiments "....support the notion that adequate cytoskeletal organization at the tip is required for tube guidance and stability" as the authors acknowledge, but they do not convincingly support their "anchoring" model

Laser cuts on cells that express Vha100-DN or wash-RNAi would be a nice addition that would take the work to the next level. But sadly, these are among the experiments that right now are impossible to carry out because of all the logistical and other problems resulting from the Covid pandemic, as explained in the cover letter.

**Other comments:**

• From the images presented, it is often difficult to figure out where the subcellular tube forms, the presence of vesicles, the cell morphologies,... and to determine the correlation between the CD4 vesicles and tube guidance.

This is the result of a frustrating technical limitation. In experiments in the past we have used markers for the outline of the cell, as we do here, too. Thus, where CD4 is expressed under the btl-gal4 driver it marks the entire outline of the cell against a completely negative background. Even for other markers, if expressed under btl-gal4, the outline of the cell is visible against the dark background. However, for endogenously marked proteins that are expressed ubiquitously, this is no longer true, and as we add more markers to follow different structures, we run out of fluorescent colours for everything we would like to highlight (and genetically, out of chromosomes to accommodate the necessary transgenic or endogenously modified constructs). We will provide tracings of the outlines of the cells to make the images clearer.

For instance, in Fig 1H and 1J, is there a "lateral" CD4 vesicle? Why it does not generate a missguided tube?

Yes, there are also CD4 vesicles closer to the proximal part of the cell. They are enriched at but not restricted to the tip of the cell. As we have shown previously (Mathew et al., 2020), they emerge along the subcellular tube, and most are transported towards the tip (also seen in Fig. 1A, for example). Why the remaining ones do not affect the guidance of the tube is unclear, but it is almost certain that the growth of the tip of the cells towards the chemotactic FGF signal plays a role: the basal membrane is constantly moving away from the tip of the tube at this location, but not at the sides further down the branch.

Fig 1I, are there 2 subcellular tubes? Can the authors mark them? I cannot really visualize them with the CD4 marker, they seem stalled or short or missing.

In Fig 1I, the tube is curled up inside of the cell, a phenotype often seen in larval terminal cells with excessive FGF signaling (for instance see Ukken et al., 2014). We added diagrams that explain the morphology of the tubes in this figure.

Fig 1L: what do the authors mean by "corrected" tube sprouts?

This is not well phrased, and we will also improve the figure to make the point clearer.

Panels 1K-M (now 1H-J) show snapshots from a movie of a cell that originally had only a misguided tube (at the top left) and is here in the process of forming its ‘correct’ tube growing in the ventral direction. In 1L (now 1I) this second tube is showing first signs of emerging, in 1M (now 1J) it is clearly visible. We have changed the wording in the figure and add an explanation in the legend, and we added a second example of this process in Figure S1.

It is difficult to identify the cell in Fig 2D-F

We added a dotted line in one of the channels showing the general morphology of the cell.

• Movie S3: I find it difficult to spot the association of CD4 and utrGFP that the authors point. Can the authors label in the movie the vesicles and the association?

We added pauses in the movie and arrows to the frames where actin is seen surrounding late endosomes.

• The results with the Rab7 downregulation and upregulation are not very clear.

Does the downregulation of Rab 7 (Rab7 DN construct) have any effect on tube guidance?

Does it decrease or eliminate actin association with CD4 vesicles in the embryo? The authors show that in the larvae expression of Rab7 DN leads to loss of actin enrichment in Rab7 vesicles. Does this have an effect on terminal branching?

Rab7DN is not visible in the embryo so we did not pursue further experiments in those stages and we previously showed that loss of Rab7 does not affect branching in larvae (Best and Leptin 2019). However, as the reviewer rightfully pointed out, expression of Rab7DN prevents actin nucleation at late endosomes in larval stages, so having the phenotypic consequence of this experiment would be informative and we are grateful for the observation. We had done the experiment, and we found no difference in the number of branches compared to controls. This suggests either that at larval stages actin recruitment at late endosomes is no longer required for branching or that there are redundant mechanisms that can balance the lack of actin nucleation. We favour the second model, because it has been shown that microtubules also play a role in tube branching and in coordinating the actin cytoskeleton (Araujo lab, 2021), so it is possible that actin nucleation can be bypassed. This is also consistent the fact that the phenotypes we describe are not all fully penetrant, again pointing to redundant mechanisms ensuring consistent directed growth.

We added the data regarding Rab7DN to the manuscript (Figure S2).

The Rab7 active construct produce effects at larval stages but not in the embryo. Is terminal cell branching in the larvae also dependent on late endosomes? Can the authors show "excess" of late endosomes in the larvae that lead to extra terminal branches? Even that the authors indicate that they cannot detect Rab7Q67L, can they find any effect at embryonic stages (e.g. presence and position of CD4 vesicles, other unrelated effects,...)?

Expression of Rab7CA in the embryo generates similar defects as nanobody-mediated mislocalisation of Rab7. We include below an example for the reviewer, but we did not feel comfortable including these data in the paper because some technical complications made them impossible to document and interpret with the certainty that we would wish. Most importantly, the YFP fusion protein is not detectable at embryonic stages, even with the most sensitive microscopes and detectors available to us. This means that we cannot correlate the observed phenotypes with the presence or absence of Rab7CA, which in our view makes them too weak for publication. At face value, these results suggest that Rab7CA begins to trigger branching during embryonic development, which eventually leads to the excess number of branches we see in the larva, but alas, we think this is too speculative to include in the paper.

• In some examples in the movies there seem to be a correlation between CD4 vesicles presence/positioning and basal lamellipodia/filopodia or actin enrichment, and also in -btl experiments. Have the authors explored this? They may want to comment on this in the discussion section.

That is a very pertinent point, and we should indeed have commented on it. If we assume the reviewer is looking at examples such as the one in Fig. 1I (currently S1C), then the explanation is the following. The terminal cells in the embryo often form transient side-branches, presumably in response to a low level FGF signals from the environment. In those cases, the basal actin cytoskeleton rearranges in the branching area to form the filopodia that lead the outgrowth of the branch, and what the reviewer observed is that this transient branch also forms the late endosome structure that we see in the main or proper growth cone. Thus, the guiding FGF-signal leads to a reorganisation of the entire actin cytoskeleton in the growth cone, and the formation of the actin-covered endosome is part of that process. We have included this in the discussion.

Reviewer #2 (Significance (Required)):

This work is relevant for the morphogenesis field and deals with the important issue of how the cytoskeleton regulates shape and cellular events. The work represents a deep analysis of a specific issue in the specialized field of tracheal development, but the results may be relevant for other types of cells forming subcellular tubes. Describing a function of trafficking vesicles (late endosome in this case) in cell morphogenesis (in addition to cargo trafficking) in an in vivo system is also relevant to advance in the cell biology field.

**Referees cross-commenting**

I agree with the comments of reviewer #1. I find relevant the points raised in "major comments number 2 and 4".

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

**Summary:**

The authors investigate the role of late endosomes in

the context of actin organization during cell morphogenesis. They use as experimental model the polarized terminal cells in the Drosophila tracheal system that forms a sub-cellular projection containing a tube. The authors show that disruption of the sub-cellular localization or maturation of late endosomes leads to increased proportion of terminal cells with mis-guided tubes. Their analysis indicated that endosomal F-actin recruitment is crucial for the directionality of the tube growth. The authors propose a model where, late endosomes control a coordinated crosstalk between endosomal and cortical actin pools to drive subcellular tube-guidance.

**Major comments:**

1. The conclusion about how WASH functions in the tube-guidance, is not clearly shown and it should be better explained and documented. It is known that loss of function of the WASH leads to dysregulation of endosomal tubulation inducing enlarged endosomes, which in turn affects the endosome-to-plasma-membrane recycling of various cargos (including luminal cargos like Serp) (Gomez, et al., Mol. Biol. Cell, 2012; Dong et al, Nat. Comm. 2013). The authors should clarify if there is a defect in the integrity of endosomes located close to the cell tip in the btl>WASHIR knock down. In the cartoon panel C' (Figure 7), the endosomes in the cell tip are shown intact (Including their relative position to the tip) but no experimental data support this conclusion.

Given the fact that Wash contributes to proper late endosome morphology we do not necessarily expect the endosomes to look normal. We had not shown this in the diagram because our own data do not directly address this point, but the literature is of course clear enough about this, so we have modified our diagrams so that they better reflect the expected phenotypes and included a reference to the relevant literature.

We and others have shown the important role of late endosomes in plasma membrane and luminal cargo delivery, and as elaborated in the response to referee 2’s point 3, complete loss of endosomal function blocks these processes. Here, at reduced but not abolished function plasma membrane delivery is clearly still functional.

-The functional analysis of WASH was based on RNAi knock down. The authors express a single RNAi construct against WASH. The expression of this RNAi line gave a low penetrance phenotype. A well-known caveat of RNAi is off-targeting. Hence, phenotypic analysis needs to include a verification by a second independent RNAi construct or a rescue of the RNAi phenotype with an overexpressed cDNA of WASH. Ideally, the null wash mutant (Nagel et al. 2017) can be used to confirm the phenotype.

Analysing wash mutants would provide a welcome additional confirmation of the knockdown results, and it is true in general that poorly characterised RNAi lines can have off target effects. However, this is a well validated line: Nagel et al. (2017) showed that the same RNAi line that we used fully recapitulates the phenotype seen in wash mutants: In both cases, actin fails to localize to late endosomes, and this is what we also found in terminal cells.

Whereas we believe therefore that the experiment is not essential to support our conclusions, we agree it is desirable and have ordered these flies. However, progress is being hampered by import restrictions at the first author’s lab: the necessary paperwork for flies to be imported for his work is still under revision by officials. The experiment thus cannot be done at the moment.

The authors claim a role of the late endosomes in subcellular tube growth and guidance. But show no data on lumen formation to prove tube presence in the tracheal terminal cells of V100R755A, btl>WASHIR, shrb mutants or in GrabFP-Bint treated terminal cells. The interpretation and quantification of the phenotypic classes "miss-tube-guided" and "ventrally-tube-guided" are based on membrane markers and not on luminal markers. The presented data with the provided resolution does not prove if the mCD4-mIFP or PH-GFP markers define apical membrane protrusions/extensions or tubular structures. Therefore, the classifications of the tube-guidance phenotype and the quantification of "distance from tube to tip" may be suggestive. The authors need to provide additional confocal data of co.stainings of the endosomal compartments with luminal antigens (i.e. GASP or Serp or Verm).

We are very unsure as to what this would add and in what context it would be necessary. Membrane and actin markers have been widely used to follow the formation of the subcellular tube by all groups working in this field. There is ample documentation in the literature that the subcellular tube, as defined by luminal content (Serp, Verm, Gasp, CBP-GFP, ANF-GFP) is surrounded by apical plasma membrane which carries apical transmembrane proteins (Crb, Uif) and their associated apical cytoplasmic complexes (Par3, Par6, aPKC, pMoesin), and apical phospholipids which can be visualized by specific PIP-binding markers, e. g. The PLC-d PH-domain that binds to PIP2 (see, e.g., Kato et al., 2004; Oshima et al., 2006; Okenve-Ramos & Llimargas, 2014 (here they use both luminal and actin reporters); Ochoa-Espinosa et al., 2017; and from our lab: JayaNandanan et al., 2014; Mathew et al., 2020. Therefore, all labs in this field have used these markers interchangeably to visualize the subcellular tube and we are not aware of a single case where luminal shape and apical membrane shape were not exactly congruent.

We have in fact used luminal markers in some experiments here, but we believe there is no reason to assume that luminal markers would have a different distribution compared to membrane, apical or actin reporters in any the experiments described here. Finally, the focus of the paper is on the behaviour of the early out-growing membrane rather than the mature tube, and on how membrane is remodelled in this process by modifications in the actin cytoskeleton. Including confirmation of the presence of luminal material would not add to the paper.

page 8 line 248, the authors interpret that reducing the dose of Shrb by half strongly enhances the wash-RNAi phenotype and suggest that WASH and Shrb act in the same pathway. Shrub is a subunit of the ESCRT-III complex involved in inward membrane budding of endosomes and WASH functions in outward endosomal membrane budding.

The Shrb and WASH form discrete molecular complexes in endosomes. The authors should consider that Shrb and WASH may well act in parallel to control directional tube growth.

This is a good point and we will rephrase our conclusions from this experiment.

The authors use nanobody-based GFP trap construct to investigate the effect of Rab7YFP localization. This is an excellent way to provide novel information for protein miss-localization in vivo. Using this method the authors concluded that ... "the correct distribution of late endosomes is required for proper tube guidance" (page 5, lines 157-158). The authors obviously consider that GrabFP-B-Int construct affected the distribution of late endosomes. However, this is unclear and additional control experiments are needed to support the author's claims. For instance, did expression of GrabFP-B-Int, target the Rab7-YFP protein or the Rab7-associated endosomes? With the presented data, it is not clear if the Rab7-YFP positive vesicles are endosomes? or aggregates formed by the trapped Rab7-YFP protein? Co-stainings using GFP in Rab7-YFP terminal cells with another endosomal markers i.e. Avl, or hrs, should be provided. It is also not clear if endocytosis of apical/basal membrane or luminal cargos was affected in GrabFP-B-Int treated terminal cells. The loss of endocytic components has been associated with defects in subcellular tube shape and morphology (Schottenfeld-Roames et al, Cur Biol. 2014). The authors should clarify these issues.

The nanobody would of course bind both to free Rab7::YFP (if there is any available) and to endosome-associated Rab7::YFP. However, in addition to Rab7::YFP we also assayed the distribution of CD4::mIFP, a membrane-associated protein that is seen at very low levels in all membranes (Mathew et al., 2020), but highly enriched in cytoplasmic vesicles, which we showed by co-expressed markers to correspond to endosomes (Mathew et al., 2020). If the nanobody sequestered free Rab7::YFP, we would expect little overlap between Rab7::YFP and CD4::mIFP puncta. Instead, we see that the large Rab7::YFP/nanobody puncta have membrane associated with them (63% of vesicles are triple positive, vs 8% of Rab7::YFP-GrabFP vesicles) indicating that they are not merely Rab7 aggregates. We will include a quantification of the degree of overlap between these components.

Regarding the question of whether endocytosis is affected, we believe this is unlikely, or if it is at all, only to a minimal extent, since growth of the outer membrane, which crucially depends on endocytosis, continues in these cells. We have added a comment to this effect in the text. The cells look very different from cells in which endocytosis has been inhibited.

In the legends of Figure 7 (C'), the authors stated that.... "lack of actin regulators at the basal cortex prevents the connection of the actin meshwork at the tip to the basal plasma membrane".... by depicting the singed mutant phenotype. singed mutant analysis is not shown in the manuscript.

Singed/Fascin has previously been shown to be required for actin organization in fillopodia (Okenve-Ramos & Llimargas, 2014). We have now included new data that show that cells expressing singed RNAi also have reducedamounts of actin at late endosomes, and that reduced actin correlates strongly with tube misguidance. This shows that an actin bundling protein that has previously been shown to be needed for actin bundles in filopodia again affects actin around endosomes, providing another illustration that these compartments interact with each other.

Our quantifications on actin around late endosomes show that interfering with endosome maturation, actin nucleation via Wash and basal/filopodial actin all lead to loss of actin around endosomes, and the misguidance phenotype correlates with actin loss (Figure 6J). By contrast, disruption of the apical actin cortex does not affect endosomal actin but does lead to misguidance. This establishes a hierarchy of actin organisation in the tip of the cell: basal actin affects endosomal actin, loss endosomal actin affects both apical and basal actin, but apical actin does not feed back on endosomal. All three pools are nevertheless required for tube guidance.

The authors consider the late endosomes nucleate actin ahead of the tube (i.e. page3, line 87-88, page 9, line 285). This is not very convincing from the presented data. The authors should provide some quantitative data showing that lack of WASH (and endosomal F-actin network) effects the apical and basal F-actin pools in the tip of the cell.

If we understand the reviewer correctly, there are two comments included in this point: (i) whether actin is nucleated at late endosomes, and (ii), whether reducing endosomal F-actin affects apical-basal actin pools in the tip of the cell.

(i) As stated above in the response to reviewer #2, we have added quantitative data illustrating actin recruitment at late endosomes with phalloidin stainings. Actin association with endosomes is also confirmed by the Rab7 stainings in larval terminal cells in Fig. 3G-H that show actin puncta associated with endosomes.

(ii) Again, as mentioned in the response to reviewer #2, we do think that all actin pools in the growth cone are affected. We are glad that the reviewers encouraged us to make this more explicit and will now discuss more clearlyhow endosomal F-actin could affect apical and basal F-actin pools.

**Minor concerns:**

1. The authors concluded (page 9, line 285) that "endosomes serve as actin nucleating centres that propagate forces within the cell by physically linking different subcellular compartments".

We agree with the reviewer, this is a good way of phrasing it, and we will rewrite this conclusion accordingly.

The authors should depict in the panels the Ventral/Dorsal axis.

All images are positioned in the same orientation, but we will ensure that the D/V axis orientation is stated in the manuscript.

Numerous omissions need to be corrected. Labeling is missing in the panels J-M' (Figure 1). The statistical significance and the p values levels are not indicated in Figure 2 (G). The panel figure 5 (D) is miss-labelled. The panels C-C' in f igure 7 are not very informative. They do not reflect the general model of the study. How the prevention of actin nucleation at late endosomes, or apical or basal cortex affects tube directionality is not graphically shown.

We thank the reviewer for noticing these omissions, we will fix them for resubmission. Having added more discussion about the general organization of actin at the tip of the cell, we think the relevance of panels 7C is justified.

In the section "Crosstalk between cytoskeletal compartments" (Lines 359- 400, discussion) the argument about the involvement of microtubules in tube-guidance is a likely scenario. But I found this argument over-extended. WASH interacts with tubulin Derivery et al. Dev Cell (2009) and WASH activity balances the endosomal and cortical F-actin networks during epithelial tube maturation in multicellular tracheal tubes (Tsarouhas et al., Nat. Comm 2019). These results should be considered in the discussion section.

We will incorporate these references to the discussion, they will for sure enrich it.

Reviewer #1 (Significance (Required)):

The important role of actin cytoskeleton in the initiation of endocytosis is well established. Actin structures in the plasma membrane are dynamically organized to assist the remodeling of the cell surface and to facilitate the inward movement of vesicles. Similarly actin networks in endosomes are critical for endosomal fusion and fission. In this work, the authors identified an opposing but interesting scenario. They propose a role for the late endocytic pathway in organizing actin networks for proper cell morphogenesis and point out an intracellular crosstalk and coordination between distinct cytoskeletal pools within a cell.

Although the mechanism about how the separate F-actin pools communicate is not shown, the paper is interesting and shows an original contribution in the area of cell morphogenesis. In addition it represents a conceptual advance as it proposes a mechanism through which actin cytoskeleton is coordinated to regulate tube morphogenesis. The proposed mechanism may be relevant for tracheal terminal cells, but could represent a general mechanism in the field of cell biology. The methodology is appropriate and the text flow is well organized. However, as explained, there are few inconsistencies in the manuscript. I believe the above additions would strengthen the conclusion of the paper.

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Referee #2

Evidence, reproducibility and clarity

Summary

Rios-Barrera and Leptin investigate the formation and guidance of the subcellular tube that forms in the terminal cell of the dorsal branches of the Drosophila tracheal system. In previous work the authors documented the presence of late endosomes at the tip of the growing terminal cell, ahead of the forming subcellular tube, which are involved in membrane recycling {Mathew, 2020 #1407}. In this present work they analyze the organization of the actin cytoskeleton in the tip terminal cell, in relation with the late endosomes, and assess the guidance of the subcellular tube. They find that the presence and localization of late endosomes play a role in tube guidance. They also find that late endosomes recruit actin around them, mediated by the activity of the actin polymerization regulator Wash, which is recruited to maturing late endosomes. When Wash activity is decreased, actin around late endosomes is decreased and tube guidance is compromised. Based on this observation, laser ablation experiments of actin ahead of the tube and actin staining at the tip of the terminal cell, the authors propose an exciting model: late endosomes recruit actin, which connects the actin pool of the basal membrane and the actin pool of the apical (subcellular tube) membrane thereby directing tube growth and guidance. The manuscript is well-written and well-presented, the images and movies are of high quality and the experimental data, which is technically challenging, is very good and sufficiently replicated.

Major comments:

1. A critical point in the model that the authors put forward (which is also contained in the title and abstract) is that actin organized at late endosomes anchors apical and basal actin cortices. However, there is no clear and conclusive evidence for this. Clear evidence in this direction should be provided to propose it as a mechanism (as it is in the text, particularly in the first sentences of the discussion) and imply it in the title.

The authors show endogenous actin around late endosomes and actin fibers at the tip of the terminal branch. However, at the level of resolution presented (Fig 3A,B), it is not possible to determine whether the different actin populations are actually "anchored". I suggest to present stronger data supporting this important conclusion.

In the same direction, it would be critical to show that this anchoring of actin fibers is disturbed when actin enrichment at the late endosome is perturbed (see also point 5). Actually, the authors show that when Vha or Wash activity are downregulated actin accumulation around the CD4 vesicles decrease. However, this experiment has a few inconveniences. First, it is difficult to determine levels of a construct that is overexpressed (UAS-utr::GFP). Could the authors use phalloidin or an actin antibody to confirm the result? Second, I find the result difficult to interpret. In the images provided I see a general decrease of actin (UtrGFP) at the tip, not only around the CD4 vesicles (Fig 6D,F) . Are these mutant conditions also affecting the rest of actin pools? If this is the case, can the authors attribute the defects exclusively to the abnormal recruitment of actin to the late endosomes? Most importantly, the authors should analyze the pattern of actin distribution (labelling endogenous actin) and determine a possible loss of "anchoring" of fibers when late endosome maturation is perturbed.

1. Another critical point in the model put forward by the authors is that late endosomes drive tube guidance. To test this point the authors use an elegant system to mislocalize Rab7 late endosomes. However, the effects are not strong (1G), and only a proportion of branches show misguided tubes. Do the cases with a ventrally-guided tube in the experiment Rab7:YFP+/+ (Fig. 1G) have a CD4 endosome (with Rab7YFP) at the tip? This would help to explain the weak effect.
2. What is the cause that preventing proper endosome maturation and acidification leads to misguided tubes (rather than missing ones)? The authors indicate that downregulating Vha activity leads to defects in acidification, but late endosome-MVB normally form. It is intriguing to see extra CD4 vesicles (like in 1C or 6C). Wouldn't we expect to see "normal" tip accumulation of CD4 vesicles only, and not extra ones? How relevant are these extra CD4 vesicles? Wouldn't we expect to see "non functional" CD4 vesicles, unable to recruit actin and lead intracellular tube formation (i.e. no tube) rather than missguidances? (1D shows higher proportion of misguided tubes than no tubes) Similarly, is Wash-RNAi producing extra CD4 vesicles (as observed in movie 5, fig 6E)?
3. Actin recruitment to late endosomes was already documented, where it plays a role in cargo trafficking. The authors propose that Wash is recruited to late endosomes upon acidification where it would prime actin nucleation around the endosome. The authors indicate a decrease in Wash accumulation upon expression of Vha dominant negative. However, this decrease is not quantified. In addition, it is difficult to determine levels of a construct when this is overexpressed (UAS-Wash::GFP). It would be desirable to use antibodies against the endogenous protein (Wash in this case) to claim differences in accumulation in mutant conditions.

The results presented do not rule out a requirement of Wash in terminal branching which is not associated with the enrichment in the late endosomes. The genetic interaction observed with Shrub is also compatible with both proteins acting on terminal branching but in different/parallel mechanisms.

1. Laser ablation experiments The laser ablation experiments are difficult to interpret. First, it is unclear to me what the results exactly indicate. What does the recoil observed suggest? Does it fit with the expected tension exerted by a link of the actin cytoskeleton relayed by late endosomes?. From the text and figure I don't understand how is the recoil calculated: retraction of the subcellular tube backwards? "enlargement" of the bleached area? Second, it is unclear to me what laser ablation actually ablates. Does it only affect actin? Or are also CD4-late endosomes and other tip structures affected? Third, is the recovery observed after ablation correlated with new actin recruitment around old or new late endosomes? Forth, I find the experiments in cells with secondary subcellular tubes very confusing and the explanations very speculative Finally, and most importantly. I think that performing laser ablation experiments in mutant conditions that affect actin recruitment (VhaDN and Wash RNAi,....) would be very informative. One would expect to find a decrease in recoil. If this was the case, it would validate, on the one hand, that in control conditions there is a tension that depends (at least in part) on actin organization, and on the other hand it would show that when actin recruitment is affected tension decreases, supporting the "anchoring" model. I understand that laser ablation experiments are not easy to perform, but I think this would be a useful experiment. To my understanding, as it stands, the laser ablation experiments "....support the notion that adequate cytoskeletal organization at the tip is required for tube guidance and stability" as the authors acknowledge, but they do not convincingly support their "anchoring" model

Other comments:

• From the images presented, it is often difficult to figure out where the subcellular tube forms, the presence of vesicles, the cell morphologies,... and to determine the correlation between the CD4 vesicles and tube guidance. For instance, in Fig 1H and 1J, is there a "lateral" CD4 vesicle? Why it does not generate a missguided tube? Fig 1I, are there 2 subcellular tubes? Can the authors mark them? I cannot really visualize them with the CD4 marker, they seem stalled or short or missing. Fig 1L: what do the authors mean by "corrected" tube sprouts? It is difficult to identify the cell in Fig 2D-F
• Movie S3: I find it difficult to spot the association of CD4 and utrGFP that the authors point. Can the authors label in the movie the vesicles and the association?
• The results with the Rab7 downregulation and upregulation are not very clear. Does the downregulation of Rab 7 (Rab7 DN construct) have any effect on tube guidance? Does it decrease or eliminate actin association with CD4 vesicles in the embryo? The authors show that in the larvae expression of Rab7 DN leads to loss of actin enrichment in Rab7 vesicles. Does this have an effect on terminal branching? The Rab7 active construct produce effects at larval stages but not in the embryo. Is terminal cell branching in the larvae also dependent on late endosomes? Can the authors show "excess" of late endosomes in the larvae that lead to extra terminal branches? Even that the authors indicate that they cannot detect Rab7Q67L, can they find any effect at embryonic stages (e.g. presence and position of CD4 vesicles, other unrelated effects,...)?
• In some examples in the movies there seem to be a correlation between CD4 vesicles presence/positioning and basal lamellipodia/filopodia or actin enrichment, and also in -btl experiments. Have the authors explored this? They may want to comment on this in the discussion section.

Significance

This work is relevant for the morphogenesis field and deals with the important issue of how the cytoskeleton regulates shape and cellular events. The work represents a deep analysis of a specific issue in the specialized field of tracheal development, but the results may be relevant for other types of cells forming subcellular tubes. Describing a function of trafficking vesicles (late endosome in this case) in cell morphogenesis (in addition to cargo trafficking) in an in vivo system is also relevant to advance in the cell biology field.

Referees cross-commenting

I agree with the comments of reviewer #3. I find relevant the points raised in "major comments number 2 and 4".

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Referee #1

Evidence, reproducibility and clarity

Summary:

The authors investigate the role of late endosomes in the context of actin organization during cell morphogenesis. They use as experimental model the polarized terminal cells in the Drosophila tracheal system that forms a sub-cellular projection containing a tube. The authors show that disruption of the sub-cellular localization or maturation of late endosomes leads to increased proportion of terminal cells with mis-guided tubes. Their analysis indicated that endosomal F-actin recruitment is crucial for the directionality of the tube growth. The authors propose a model where, late endosomes control a coordinated crosstalk between endosomal and cortical actin pools to drive subcellular tube-guidance.

Major comments:

1. The conclusion about how WASH functions in the tube-guidance, is not clearly shown and it should be better explained and documented. It is known that loss of function of the WASH leads to dysregulation of endosomal tubulation inducing enlarged endosomes, which in turn affects the endosome-to-plasma-membrane recycling of various cargos (including luminal cargos like Serp) (Gomez, et al., Mol. Biol. Cell, 2012; Dong et al, Nat. Comm. 2013). The authors should clarify if there is a defect in the integrity of endosomes located close to the cell tip in the btl>WASHIR knock down. In the cartoon panel C' (Figure 7), the endosomes in the cell tip are shown intact (Including their relative position to the tip) but no experimental data support this conclusion.

-The functional analysis of WASH was based on RNAi knock down. The authors express a single RNAi construct against WASH. The expression of this RNAi line gave a low penetrance phenotype. A well-known caveat of RNAi is off-targeting. Hence, phenotypic analysis needs to include a verification by a second independent RNAi construct or a rescue of the RNAi phenotype with an overexpressed cDNA of WASH. Ideally, the null wash mutant (Nagel et al. 2017) can be used to confirm the phenotype.

1. The authors claim a role of the late endosomes in subcellular tube growth and guidance. But show no data on lumen formation to prove tube presence in the tracheal terminal cells of V100R755A, btl>WASHIR, shrb mutants or in GrabFP-Bint treated terminal cells. The interpretation and quantification of the phenotypic classes "miss-tube-guided" and "ventrally-tube-guided" are based on membrane markers and not on luminal markers. The presented data with the provided resolution does not prove if the mCD4-mIFP or PH-GFP markers define apical membrane protrusions/extensions or tubular structures. Therefore, the classifications of the tube-guidance phenotype and the quantification of "distance from tube to tip" may be suggestive. The authors need to provide additional confocal data of co.stainings of the endosomal compartments with luminal antigens (i.e. GASP or Serp or Verm).
2. page 8 line 248, the authors interpret that reducing the dose of Shrb by half strongly enhances the wash-RNAi phenotype and suggest that WASH and Shrb act in the same pathway. Shrub is a subunit of the ESCRT-III complex involved in inward membrane budding of endosomes and WASH functions in outward endosomal membrane budding. The Shrb and WASH form discrete molecular complexes in endosomes. The authors should consider that Shrb and WASH may well act in parallel to control directional tube growth.
3. The authors use nanobody-based GFP trap construct to investigate the effect of Rab7YFP localization. This is an excellent way to provide novel information for protein miss-localization in vivo. Using this method the authors concluded that ... "the correct distribution of late endosomes is required for proper tube guidance" (page 5, lines 157-158). The authors obviously consider that GrabFP-B-Int construct affected the distribution of late endosomes. However, this is unclear and additional control experiments are needed to support the author's claims. For instance, did expression of GrabFP-B-Int, target the Rab7-YFP protein or the Rab7-associated endosomes? With the presented data, it is not clear if the Rab7-YFP positive vesicles are endosomes? or aggregates formed by the trapped Rab7-YFP protein? Co-stainings using GFP in Rab7-YFP terminal cells with another endosomal markers i.e. Avl, or hrs, should be provided. It is also not clear if endocytosis of apical/basal membrane or luminal cargos was affected in GrabFP-B-Int treated terminal cells. The loss of endocytic components has been associated with defects in subcellular tube shape and morphology (Schottenfeld-Roames et al, Cur Biol. 2014). The authors should clarify these issues.
4. In the legends of Figure 7 (C'), the authors stated that.... "lack of actin regulators at the basal cortex prevents the connection of the actin meshwork at the tip to the basal plasma membrane".... by depicting the singed mutant phenotype. singed mutant analysis is not shown in the manuscript.
5. The authors consider the late endosomes nucleate actin ahead of the tube (i.e. page3, line 87-88, page 9, line 285). This is not very convincing from the presented data. The authors should provide some quantitative data showing that lack of WASH (and endosomal F-actin network) effects the apical and basal F-actin pools in the tip of the cell.

Minor concerns:

1. The authors concluded (page 9, line 285) that "endosomes serve as actin nucleating centres that propagate forces within the cell by physically linking different subcellular compartments". The authors may want to consider that endosomes can serve as platforms to assemble important actin polymerization regulators and/or signals in the tip of the terminal cell to instruct tube directionality.
2. The authors should depict in the panels the Ventral/Dorsal axis.
3. Numerous omissions need to be corrected. Labeling is missing in the panels J-M' (Figure 1). The statistical significance and the p values levels are not indicated in Figure 2 (G). The panel figure 5 (D) is miss-labelled. The panels C-C' in figure 7 are not very informative. They do not reflect the general model of the study. How the prevention of actin nucleation at late endosomes, or apical or basal cortex affects tube directionality is not graphically shown.
4. In the section "Crosstalk between cytoskeletal compartments" (Lines 359- 400, discussion) the argument about the involvement of microtubules in tube-guidance is a likely scenario. But I found this argument over-extended. WASH interacts with tubulin Derivery et al. Dev Cell (2009) and WASH activity balances the endosomal and cortical F-actin networks during epithelial tube maturation in multicellular tracheal tubes (Tsarouhas et al., Nat. Comm 2019). These results should be considered in the discussion section.

Significance

The important role of actin cytoskeleton in the initiation of endocytosis is well established. Actin structures in the plasma membrane are dynamically organized to assist the remodeling of the cell surface and to facilitate the inward movement of vesicles. Similarly actin networks in endosomes are critical for endosomal fusion and fission. In this work, the authors identified an opposing but interesting scenario. They propose a role for the late endocytic pathway in organizing actin networks for proper cell morphogenesis and point out an intracellular crosstalk and coordination between distinct cytoskeletal pools within a cell.

Although the mechanism about how the separate F-actin pools communicate is not shown, the paper is interesting and shows an original contribution in the area of cell morphogenesis. In addition it represents a conceptual advance as it proposes a mechanism through which actin cytoskeleton is coordinated to regulate tube morphogenesis. The proposed mechanism may be relevant for tracheal terminal cells, but could represent a general mechanism in the field of cell biology. The methodology is appropriate and the text flow is well organized. However, as explained, there are few inconsistencies in the manuscript. I believe the above additions would strengthen the conclusion of the paper.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): Very high evidence and clarity. Excellent scientific rigor. The findings are important and reported clearly. The experiments are conducted in a rigorous way by numerous participating laboratories. Reviewer #1 (Significance (Required)): Very high significance, both from a molecular biology and clinical standpoints. This is an important manuscript that challenges the findings and conclusions of a prior high-profile paper in Science by Ma et al 2016, claiming that LAG3 is a receptor for aggregation-prone species of alpha-synuclein and that deletion of LAG3 results in reduced cell to cell propagation of alpha-synuclein aggregates. The experiments in this paper are numerous and employ a variety of techniques. The overall conclusions are that LAG3 is not expressed by the relevant neurons and that LAG3 is not a receptor for alpha-synuclein fibrils (of different sizes). Therefore, the authors conclude that LAG3 is unlikely to play a role in the spread of alpha-synuclein pathology in Parkinson's disease and related disorders. There are, however, some weaknesses. For example, the Introduction contains passages that are not written in a stringent way: 1. "Histologically, PD is characterized by α-synuclein aggregates known as Lewy Bodies in neurons of the substantia nigra," That is not a good description of PD neuropathology. Lewy pathology is present in numerous areas of the CNS and PNS, and is not restricted to the substantia nigra.

We have added a more detailed account:

“Histologically, PD is characterized by α-synuclein inclusions known as Lewy Bodies whose accumulation is associated with neurodegeneration (Dickson, 2012; Mullin and Schapira, 2015; Corbillé et al., 2016). These inclusions affect the Substantia nigra and other mesencephalic regions as well as, in some cases, the amygdala and neocortex (Dickson, 2018).”

1. "Growing evidence suggests that α-synuclein fibrils spread from cell to cell". While alpha-synuclein pathology can spread from cell to cell, it is not known if the fibrils are the species (alone or combined with other conformers) that cause the spreading of the pathology in a seeding fashion, or if smaller alpha-synuclein assemblies play that role.

We have reformulated the sentence to credit the fact that we do not know which synuclein species is the one that is transmitted:

“Growing evidence suggests that α-synuclein aggregates spread from cell to cell (Volpicelli-Daley et al., 2011; Volpicelli-Daley, Luk and Lee, 2014)… “

1. "...by a "prionoid" process of templated conversion (Aguzzi, 2009; Aguzzi and Lakkaraju, 2016; Jucker and Walker, 2018; Kara, Marks and Aguzzi, 2018; Scheckel and Aguzzi, 2018; Uemura et al., 2020)." This sentence gives the impression that the corresponding author has led the field when it comes to alpha-synuclein's prionid properties. That is not really the case, and it would be appropriate to cite the literature in a more scholarly fashion that reflects how this part of the alpha-synuclein research field developed.

I cannot disagree, and in fact I suspect that the present paper may be my second and possibly last experimental contribution to the synuclein field! However, I do claim intellectual parenthood of the prionoid (not “prionid”) concept, which I first expounded in a 2009 Nature paper. Anyway, we now provide a more balanced citation:

“…by a “prionoid” process of templated conversion (Aguzzi, 2009; Jucker and Walker, 2018; Kara, Marks and Aguzzi, 2018; Henderson, Trojanowski and Lee, 2019; Karpowicz, Trojanowski and Lee, 2019; Uemura et al., 2020; Kara et al., 2021).“

1. "Interrupting transmission of a-synuclein may slow down or abrogate the disease course." This is a bold statement and far from certain. While one might propose that this is the case, it is still just a hypothesis and the Introduction should reflect that.

We have rewritten the sentence in a more subdued manner:

“It is thought that interrupting transmission of a-synuclein may slow down or abrogate the disease course.”

**Referee Cross-commenting** I concur with reviewers 2 and 3, and the new comment from reviewer 2. This paper should be published as soon as possible.

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Reviewer #2 (Evidence, reproducibility and clarity (Required)): This study conclusively shows that LAG3 is not the receptor for a-synuclein that underlies the spread of synucleinopathic damage in various PD-related conditions. The paper is done extremely carefully and comprehensively. My only suggestion is to indicate the significance level in Figure 5a, as it may turn out that LAG3 is actually protective.

We have added the significance level in Fig. 5A, in the legend: “The survivals of ASYNA53T LAG3-/-, LAG3+/- and LAG3+/+ mice were similar (Mantel-Cox log-rank test, p-value = 0.165).”

Reviewer #2 (Significance (Required)): This study is of extremely high significance - we need mechanisms to deal with spectacular results in the literature that should not have been published because they are were uncompelling to begin with, but were published for various sociological/political reasons. Science won't progress if we don't find correction mechanisms for wrong conclusions. **Referee Cross-commenting** I agree with reviewers 1 and 3, especially with the suggestions made by reviewer 1, which should be instituted. I think we all concur that the paper should be published without new experiments. I believe testing a-synuclein propagation in vivo in LAG3 KO mice would be useful, but given the complete lack of replication of LAG3 expression in brain and of a-synuclein binding to LAG3, this is not necessary.

We considered running experiments in addition to those performed in vivo in ASYNA53T transgenic mice (including LAG3 KO) and ex vivo in organotypic slices, the latter using pre-formed fibrils. However, the outcome of these experiments, along with the absence of LAG3 expression in neurons and its unclear binding, convinced us that the usage of further animals and reagents would be unwarranted.

*****************************************

Reviewer #3 (Evidence, reproducibility and clarity (Required)): It was proposed that LAG3 is important in the treatment of PD and related disorders, because it functions as a receptor of pathogenic α-synuclein and the treatment with anti-LAG3 antibodies attenuated the spread of pathological α-synuclein and drastically lowered the aggregation in vitro (Mao et al, Science 2016). In this study, authors characterized 8 antibodies to LAG3 and investigated the presence of LAG3 in cultured cell lines, NSC-derived neural cultures, or organ homogenates for the presence of human or murine LAG3. But it was not detected in any of the neuronal samples tested. In addition, single cell (sc) RNAseq yielded only minimal counts for the LAG3 transcript in neurons, astrocytes, and mixed glial cells, and single-nucleus (sn) RNAseq human brain dataset for LAG3 expression across different cell types confirmed no LAG3 signals for any of 34 identified cell clusters, including 13 clusters of excitatory and 11 subtypes of inhibitory neurons, oligodendrocytes, oligodendrocyte precursor cells, microglia, astrocytes, and endothelial cells. Authors also analyzed the binding of LAG3 with α-synuclein in mouse and human model systems, and concluded that the affinity of LAG3 for α-synuclein fibrils, if any, is micromolar or less. Furthermore, authors studied the propagation of pre-formed fibrils (PFFs) of α-synuclein in neural stem cell (NSC)-derived neural cultures in the presence or absence of LAG3, and the impact of LAG3 on survival in ASYNA53T transgenic mice expressing wild-type LAG3 as well as hemizygous or homozygous deletions thereof. However, they were unable to see any significant role for LAG3 in these in vitro and in vivo models of α-synucleinopathies. In this connection, the reviewer would like to ask one question: Have you conducted any experiments of the propagation of PFFs of α-synuclein in LAG3-KO mice ? If they did, what were the results ?

We did consider the possibility of replicating the experiments using PFFs in LAG3 KO mice. However, as stated above, we felt that our experiments – including the survival study in vivo in ASYNA53T transgenic mice – were unambiguous. After critical consideration, we remained unconvinced that this additional experiment would change the weight of our evidence in a substantial manner that would justify the inoculation of other animals and the utilisation of more resources.

**Minor point** In Page 10, I think it's a typo: ASYYN mice must be ASYN mice.

Thank you for pointing this out. We corrected it.

Reviewer #3 (Significance (Required)): These negative findings about the LAG in α-synucleinopathies shown in this manuscript do not provide any new insight into the mechanisms of α-synuclein propagation. However, it is clear that LAG3 is not expressed in neuronal cells and the binding of LAG3 to α-synuclein fibrils appears limited. Overexpression of LAG3 in cultured human neural cells did not cause any worsening of α-synuclein pathology ex vivo. The overall survival of A53T α- synuclein transgenic mice was unaffected by LAG3 depletion and the seeded induction of α-synuclein lesions in hippocampal slice cultures was unaffected by LAG3 knockout. These data shown in this manuscript are convincing and the information is very important in terms of correcting the direction of disease treatment and research. **Referee Cross-commenting** I agree with reviewers 1 and 2. This paper should be published as soon as possible.

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Referee #3

Evidence, reproducibility and clarity

It was proposed that LAG3 is important in the treatment of PD and related disorders, because it functions as a receptor of pathogenic α-synuclein and the treatment with anti-LAG3 antibodies attenuated the spread of pathological α-synuclein and drastically lowered the aggregation in vitro (Mao et al, Science 2016).

In this study, authors characterized 8 antibodies to LAG3 and investigated the presence of LAG3 in cultured cell lines, NSC-derived neural cultures, or organ homogenates for the presence of human or murine LAG3. But it was not detected in any of the neuronal samples tested. In addition, single cell (sc) RNAseq yielded only minimal counts for the LAG3 transcript in neurons, astrocytes, and mixed glial cells, and single-nucleus (sn) RNAseq human brain dataset for LAG3 expression across different cell types confirmed no LAG3 signals for any of 34 identified cell clusters, including 13 clusters of excitatory and 11 subtypes of inhibitory neurons, oligodendrocytes, oligodendrocyte precursor cells, microglia, astrocytes, and endothelial cells.

Authors also analyzed the binding of LAG3 with α-synuclein in mouse and human model systems, and concluded that the affinity of LAG3 for α-synuclein fibrils, if any, is micromolar or less.

Furthermore, authors studied the propagation of pre-formed fibrils (PFFs) of α-synuclein in neural stem cell (NSC)-derived neural cultures in the presence or absence of LAG3, and the impact of LAG3 on survival in ASYNA53T transgenic mice expressing wild-type LAG3 as well as hemizygous or homozygous deletions thereof. However, they were unable to see any significant role for LAG3 in these in vitro and in vivo models of α-synucleinopathies.

In this connection, the reviewer would like to ask one question: Have you conducted any experiments of the propagation of PFFs of α-synuclein in LAG3-KO mice ? If they did, what were the results ?

Minor point

In Page 10, I think it's a typo: ASYYN mice must be ASYN mice.

Significance

These negative findings about the LAG in α-synucleinopathies shown in this manuscript do not provide any new insight into the mechanisms of α-synuclein propagation. However, it is clear that LAG3 is not expressed in neuronal cells and the binding of LAG3 to α-synuclein fibrils appears limited. Overexpression of LAG3 in cultured human neural cells did not cause any worsening of α-synuclein pathology ex vivo. The overall survival of A53T α- synuclein transgenic mice was unaffected by LAG3 depletion and the seeded induction of α-synuclein lesions in hippocampal slice cultures was unaffected by LAG3 knockout. These data shown in this manuscript are convincing and the information is very important in terms of correcting the direction of disease treatment and research.

Referee Cross-commenting

I agree with reviewers 1 and 2. This paper should be published as soon as possible.

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Referee #2

Evidence, reproducibility and clarity

This study conclusively shows that LAG3 is not the receptor for a-synuclein that underlies the spread of synucleinopathic damage in various PD-related conditions. The paper is done extremely carefully and comprehensively. My only suggestion is to indicate the significance level in Figure 5a, as it may turn out that LAG3 is actually protective.

Significance

This study is of extremely high significance - we need mechanisms to deal with spectacular results in the literature that should not have been published because they are were uncompelling to begin with, but were published for various sociological/political reasons. Science won't progress if we don't find correction mechanisms for wrong conclusions.

Referee Cross-commenting

I agree with reviewers 1 and 3, especially with the suggestions made by reviewer 1, which should be instituted. I think we all concur that the paper should be published without new experiments. I believe testing a-synuclein propagation in vivo in LAG3 KO mice would be useful, but given the complete lack of replication of LAG3 expression in brain and of a-synuclein binding to LAG3, this is not necessary.

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Referee #1

Evidence, reproducibility and clarity

Very high evidence and clarity. Excellent scientific rigor.

The findings are important and reported clearly. The experiments are conducted in a rigorous way by numerous participating laboratories.

Significance

Very high significance, both from a molecular biology and clinical standpoints. This is an important manuscript that challenges the findings and conclusions of a prior high-profile paper in Science by Ma et al 2016, claiming that LAG3 is a receptor for aggregation-prone species of alpha-synuclein and that deletion of LAG3 results in reduced cell to cell propagation of alpha-synuclein aggregates.

The experiments in this paper are numerous and employ a variety of techniques. The overall conclusions are that LAG3 is not expressed by the relevant neurons and that LAG3 is not a receptor for alpha-synuclein fibrils (of different sizes). Therefore, the authors conclude that LAG3 is unlikely to play a role in the spread of alpha-synuclein pathology in Parkinson's disease and related disorders.

There are, however, some weaknesses. For example, the Introduction contains passages that are not written in a stringent way:

1. "Histologically, PD is characterized by α-synuclein aggregates known as Lewy Bodies in neurons of the substantia nigra," That is not a good description of PD neuropathology. Lewy pathology is present in numerous areas of the CNS and PNS, and is not restricted to the substantia nigra.
2. "Growing evidence suggests that α-synuclein fibrils spread from cell to cell". While alpha-synuclein pathology can spread from cell to cell, it is not known if the fibrils are the species (alone or combined with other conformers) that cause the spreading of the pathology in a seeding fashion, or if smaller alpha-synuclein assemblies play that role.
3. "...by a "prionoid" process of templated conversion (Aguzzi, 2009; Aguzzi and Lakkaraju, 2016; Jucker and Walker, 2018; Kara, Marks and Aguzzi, 2018; Scheckel and Aguzzi, 2018; Uemura et al., 2020)." This sentence gives the impression that the corresponding author has led the field when it comes to alpha-synuclein's prionid properties. That is not really the case, and it would be appropriate to cite the literature in a more scholarly fashion that reflects how this part of the alpha-synuclein research field developed.
4. "Interrupting transmission of a-synuclein may slow down or abrogate the disease course." This is a bold statement and far from certain. While one might propose that this is the case, it is still just a hypothesis and the Introduction should reflect that.

Referee Cross-commenting

I concur with reviewers 2 and 3, and the new comment from reviewer 2. This paper should be published as soon as possible.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

In this paper, Dr. Tanenbaum and colleagues present a new method to determine the exact point of the cell cycle in which a cell is. This new method has the potential to be applied to any cell-cycle phase and even to other processes. Focusing on M-G1 transition, they do sequencing of single human cells. They identify two groups of cell cycle-related genes, expressing mRNAs which are degraded either immediately after exit from mitosis or later on during G1. One of the factors involved in this degradation is identified as CNOT1.

In my opinion, the new method is well stablished and has the potential to be very useful to future work. In general, I think that the main conclusions are based on more than one approaches and are convincing. In relation to these, I have two major concerns:

1. Although it is clear that a scheduled mRNA decay exits, this does not exclude the possibility of a concomitant effect on mRNA synthesis. A measurement of nascent transcription is needed.
2. As mentioned in the discussion, it is possible that the limited effect of depleting CNOT1 is due to the partial knockdown. However, it is also possible that a different pathway of mRNA degradation is involved. This should be addressed by targeting other decay factors (for example Xrn1 and/or an exosome component).

Minor comments:

1. Cell cycle control is not absolutely universal. The authors should mention that their results and conclusions correspond to human cells; if not in the title, at least in the abstract.
2. Is SORT-seq (mentioned exclusively in the methods section) the same as scRNA-seq?
3. Figure 2: there is no correspondence between the TOP2A images and their quantification. This experiment also needs an unrelated mRNA FISH as a negative control.
4. Figure 3D: if I correctly understood this experiment, "Time in Actinomycin D" is a better title for the X axis. "Time after mitotic shake-off" is misleading because it suggests that the cells were released from the mitotic blockage.
5. Figure S3L: the blockage of transcription by Actinomicin D should be demonstrated by a more general method, such as EU (5-ethynyl uridine) incorporation.
6. Figure 4A: what is the cell cycle phenotype of CNOT1 siRNA? If a reduction with CRISPRi of 50 % causes a phenotype (Figure S4C), then a reduction of 90 % by the siRNA (Figure S4A) should cause a stronger phenotype.
7. Do the two waves of protein degradation (mentioned in the second paragraph of page 12) affect the same genes than the two waves of mRNA degradation?

Significance

The new method described in this paper could be useful to address many questions in the field of cell-cycle control. Moreover, with modifications, it could be applied to any time-dependent biological problem. In addition, the scheduled degradation of mRNAs in the M-G1 transition is a discovery of biological significance.

In my opinion, the paper is technically interesting to a broad range of investigators, and biologically relevant for those studying the cell cycle.

Keywords of my field of expertise: transcription, chromatin, gene expression.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study Krenning, Sonneveld, and Tanenbaum have investigated the temporal control of mRNA decay after mitosis. Previous work has demonstrated that following mitosis, regulated protein degradation serves an important role in erasing any lingering memory of the previous cell cycle. Left unanswered however, is whether mRNA decay is similarly regulated after mitosis, and if so, what role does it play in the cell cycle. The authors use time-lapse imaging and single-cell RNAseq to measure decay rates of mRNAs after mitosis. They use the FUCCI sensors to identify the precise age of each individual cell prior to performing single-cell RNAseq. Using this pseudo-timelapse approach, they identify several genes that are actively degraded after mitosis. Interestingly, they find that some mRNAs are decayed rapidly and immediately after mitosis while other mRNAs are decayed only after a delay of about 1.5 hours after mitosis. The authors find that, at least for several of the genes, the protein CNOT1 mediates the decay. The authors conclude that regulated mRNA decay occurs after mitosis and helps reset the transcriptome at the onset of a new cell cycle.

The question being asked in this manuscript is interesting and potentially very important to the cell cycle field. However, I believe this study suffers from several technical issues highlighted below as well as relatively modest effect sizes, particularly when it comes to ascribing CNOT1 as the key regulator mediating mRNA decay upon mitotic exit.

Major Comments:

1) The authors repeatedly claim that they can accurately measure the time a cell has spent in G1 phase, due to using live-cell imaging to calibrate their FACS data. However, following mitosis, cells bifurcate into either G0/Quiescence or into G1 phase. Importantly, the FUCCI-G1 sensor is not capable of distinguishing between these two cell cycle phases. Thus, while two cells may have spent the same amount of time since mitosis, one cell may be in Quiescence while the other cell is in G1 phase and they would both have the same level of FUCCI-G1. Even by live-cell imaging its not possible to distinguish between these two cell cycle phases with the markers used in this study. I believe you can see evidence for this in the Flow cytometry data in Figure 1C where there is a large population of cells with very high FUCCI-G1 levels (even higher than most of the S phase cells) but very low FUCCI-G2 levels. These cells likely represent cells that entered G0 after mitosis, remained there for several hours, and thus accumulated very high levels of the FUCCI-G1 sensor. This technical limitation has several implications. First, it means what is likely going into the single-cell mRNA seq workflow is a mixture of G0 and G1 cells. Since the authors observe two distinct "waves" of mRNA decay, it makes me wonder if one wave might be occurring in G1 cells while the other wave is occurring in G0 cells? Second, the authors state several times they can accurately determine the time a cell has spent in G1 phase. The more accurate statement however is that the authors can accurately determine the time that has elapsed since mitosis, since they cannot distinguish between G0 and G1 phase. This is admittedly a nuanced distinction but an important one given that quiescence cells are in a very different cellular state than cells in G1 phase. The authors actually use the correct x-axis label of "Time after metaphase (min)" in several of their figures, but they do not use the same language in the main text or to describe their conclusions. To overcome the technical challenge of distinguishing between G0/G1 cells and to address these two points, the authors could use an additional FUCCI sensor, mVenus-p27K(-), which accumulates in G0 cells but not in G1 cells (PMID: 24500246).

2) One of the main novelty claims of the paper is that mRNA decays following mitotic exit in two waves. In order to support this claim, the authors plot the time since metaphase vs normalized transcripts for many single cells. For several genes including CDK1, TOP2A, and UBE2C, there is an immediate drop from time 0 to the next most densely populated timepoint of about 20 minutes. This results in a bimodal histogram as seen in Figure 2A, where there is one single bin representing genes that are maximally decayed at time 0, while another population is more normally distributed with a median decay time of ~80minutes. I have two concerns about this data. First, there are very few if not zero cells analyzed that were between 0 and 20 minutes old at the time of collection. Therefore the authors do not know if the mRNA decayed immediately after mitosis or with a 20minute delay after mitosis. Thus, rather than some genes decaying immediately after mitotic exit resulting in that one bin at time=0 and some genes decaying with a delay, there could actually be just one wave of mRNA decay that is broadly and normally distributed from 20-80minutes after mitosis (see histogram Figure 2 and Figure S3G; if you ignore anything less than 20minutes due to lack of data during this time window, then there is just a single distribution). While likely technically challenging due to cytokinesis, sampling cells that are between 0-20minutes old may be important to accurately measuring the decay rates of mRNAs upon mitotic exit. Second, its not entirely clear from the methods section, but I am assuming that for time 0 of the plots in Figure S3A-F, the authors are using G2/M sorted cells as defined by FUCCI-G2 high/FUCCI-G1 low status. However, depending on what precise FACS gates were used to do this sort, these cells could be anywhere in early G2, late G2, prometaphase, metaphase, etc and they are all averaged together. Thus, when the authors claim that the mRNAs are decaying immediately after mitosis, that's based on comparing the mRNA levels in this mixed G2/M population with cells that are 20minutes or more after mitosis. For genes like CDK1 where the mRNA is almost completely gone at 20 minutes after mitosis when they first have any cells to measure, its entirely possible these mRNAs were already decayed either before or within mitosis, rather than upon mitotic exit. What we really need to know is what are the mRNA levels precisely at metaphase and plot that value as time=0 (for example in figure S3A-F). Perhaps the authors could use CDK1i plus Taxol treatment to accumulate cells in mitosis like they describe in the methods for the transcription inhibition experiments. (If this is what was done for the Sort-Seq experiments as well as the data in Fig S3A-F, my apologies for not completely understanding, but the methods section should be updated to make this more clear)

3) As the authors point out in the discussion, the effect size of CNOT1 depletion on mRNA decay are rather small. Notably the genes that appear to be statistically significant are all the genes that are hardly decayed after mitosis anyways (see Figure 4D, ARLGIP1, PSD3, etc). These genes appear to be only down about 2-fold (-1 on a log2 scale axis) in the control group, which would be expected during mitosis when the mother cell splits in half into two daughter cells. Depending on the method of normalization, this change in mRNA levels may simply be due to this. I understand the technical limitations in knocking down an essential gene, but given that one of the major novelty claims of this study is that CNOT1 mediates the mRNA decay upon mitotic exit, more robust proof is warranted. The authors could employ the inducible protein degradation system they referenced in the discussion. Additionally they could perhaps show data that CNOT1 is somehow differentially regulated during mitotic exit that would account for this sudden change in mRNA stability. If the authors were to include additional corroboratory data demonstrating CNOT1 is most active during mitotic exit for example, it would help to overcome that low effect size upon mild CNOT1 depletion.

Minor comment:

1) The authors state that they can "accurately determine the time a cell has spent in G1 phase based on its FUCCI-G1 fluorescence as measured by FACS" (Page 6, last line of the first paragraph). It would be nice to know how accurately? What is the level of uncertainty in your measurements? +/- how many minutes?

2) The authors only focused on those genes whose mRNA's were decayed upon mitotic exit, but of equal interest would be those cell cycle genes that were not observed to decay upon mitotic exit. The authors may want to highlight these genes, because it might shed light on what aspects of the cell cycle cells want to reset, and what aspects of the cell cycle the cells may wish to "remember" from the previous cell cycle. For example, what is the status of the cyclins? CIPs? Origin licensing genes? There is growing evidence that the status of the mother cell can influence the cell cycle of the daughter cell and mRNA levels of key cell cycle genes have been implicated in this (PMIDs: 28514656, 28317845, 28869970).

Significance

This paper offers a potential conceptual advance to our understanding of how cells reset after the cell cycle is completed. By demonstrating that cells regulate protein as well as mRNA degradation upon cell cycle exit, the authors show cells utilize multiple mechanisms to reset the biochemical state of the cell at the onset of a fresh cell cycle. This work would be of potential interest to the cell cycle field, particularly those interested in G1 regulation. It would also be of interest to people interested in mRNA regulation as it would demonstrate a clear window during which mRNA decay was specifically upregulated.

While my expertise lies in the cell cycle and the use of FUCCI sensors to identify cell cycle stages, I have less expertise in single-cell RNAseq and methods of mRNA quantification.

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Referee #1

Evidence, reproducibility and clarity

In the manuscript "Time-resolved single-cell sequencing identifies multiple waves of mRNA decay during mitotic exit", Krenning et al. describe a method that connects live-cell microscopy with single-cell RNA sequencing in order to monitor global changes in mammalian mRNA gene expression in a cell-cycle-dependent manner. To this end they employ a fluorescent, ubiquitination-based cell cycle indicator (FUCCI system) in human untransformed RPE-1 cells coupled to SORT-Seq in order to generate a high-resolution, time-resolved transcriptome profile of cells spanning the transition form M phase into G1 phase. By comparing FACS-based sampling with an in silico trajectory inference method the authors provide convincing evidence that this system allows for high-resolution, time-resolved transcriptome profiling of cells in the transition from M-phase into G1 phase. Subsequent analysis of changes in steady-state gene expression revealed a set of >200 transcripts that undergo rapid decay in two distinct waves, first around the time of mitotic exit and second upon G1 entry. Those results were independently validated by single molecule FISH of select transcripts, revealing that the first wave of RNA decay initiates at the start of anaphase and the second wave starts during early G1 phase. Using mathematical modeling followed by selective validation (using cell-cycle staging combined with global inhibition of RNA decay), the authors derive and confirm precise mRNA decay rates for cell cycle regulated mRNAs that were overall lower than what has been observed in previously described population-based half-life measurements. Finally, the authors establish a role of deadenylation by the CCR4-NOT complex in selective mRNA decay during M-phase/G1 transition by revealing a partial stabilization upon NOT1-depletion by RNAi.

I have only a minor comment to help improve the mechanistic insights: While the authors attribute the partial stabilization of cell-cycle regulated mRNAs to an incomplete depletion of NOT1 (which is possible), an alternative hypothesis would be that decapping and 5´-to-3´ decay further contribute to mRNA turnover. Notably, the authors describe the use of siRNAs targeting Dcp2 in the methods section (without referring to it in the results part), indicating that they may have data that could clarify this. They authors may consider adding this data to complete an otherwise nicely executed and well-written manuscript.

Significance

Overall, this is an impressive and well-controlled body of work providing novel insights into cell-cycle controlled mRNA decay. It reveals novel insights into the targets and molecular mechanisms of mRNA decay in the transition of mitosis to G1, thereby adding significantly to our understanding of the scope of tightly controlled gene expression for proper execution of the cell cycle.

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Reply to the reviewers

Rebuttal letter – Response to Reviewers

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

This study focused on P. vivax, which is an important neglected human malaria killer. The reported evidence will have a significant impact on diagnosing infectious diseases. The language in the manuscript is very good. However, some typos were reported. Some paragraphs might need particular attention to punctuation. Overall, the work is very good. The statistics are straight forward. However, there are a couple of major points that must be addressed before publication. Some of my comments are just recommendations to clarify some sections of the text.

**Major comments:**

The statistical methods can be improved by using generalised mixed models (GLMM).

1- PCA graphs need to be organised in more descriptive ways. Dim1 and Dim2 in each axis need to be defined clearly in the figures. PCA in Fig2 c is very difficult to follow, and it needs to be organised.

Answer: Figures have been amended to be more self-explanatory and clearer to the reader.

2- In this study, patients were male and female, and we know already male and female haematological parameters are hugely different, specially Hb level, and so on. My question is how the sex variable is treated in this study? Did your control group were from both sexes? Sex could be treated as a random variable in all studies if GLMM models were used.

Answer: Information in how the sex variable was treated in the study has been added to the methods section. In our cross-sectional study with uncomplicated P. vivax malaria patients seen at FMT-HVD in Manaus, Brazil, patients and healthy donors (controls) were matched by age and sex. In both groups, frequency of female individuals was 30% and male individuals 70%.

We think sex is better fitted as fixed effect since only two levels for this factor are possible. Thus, we used linear models with age and sex as fixed variables for statistical testing and to ensure that the differences observed between P.vivax- infected patients and controls, as well as between the clusters, were only due to disease status. This analysis showed that red blood cells count, hemoglobin, hematocrit, MXD and neutrophils counts (this parameter only when comparing the clusters) needed to be corrected only due to sex influence. For these parameters, estimates of predicted sex influence were subtracted from the raw parameter values and residuals were used for statistical testing. We have added this information in the Methods section as indicated below:

Page 6, line 128: Patients and healthy donors were age and sex-matched, with a frequency of 30% female and 70% male individuals in both groups.

Page 14, line 336:

To ensure that differences observed between P. vivax - infected patients and controls, as well as between the clusters, were due to disease status and not confounded by age or sex, the clinical parameters were fitted as response variables in a linear model with sex and/or age fitted as explanatory variables. Age and sex were included in the model if their coefficients were estimated as different from zero with p-value The residuals from the linear model were then used as age and/or sex corrected parameters in subsequent analyses.

3- Why 6h and 18h used for the HUVEC evaluation?

Answer. We ran several optimization experiments with individual plasma samples where we observed maximal mRNA expression changes after 6h of stimulation. For experiments detecting protein expression (IFA and flow cytometry), we increased the stimulation time to 18h. Preliminary experiments suggested this to be the optimal duration without compromising cellular viability.

4- It is mentioned only neutrophil enriched in this study, if myelopoiesis is affected, why the other granulocytes were not showed significant enhancement?

Answer: Our data reveal no change in the number of circulating neutrophils in the different clusters of individuals. However, mixed cell counts (MXD), a parameter representing monocytes, basophils and eosinophils numbers, was significantly reduced in Vivaxhigh patients. As a result, there was a significant enrichment of neutrophils in the leukocyte fraction in the blood of Vivaxhigh patients as well as a higher Neutrophil:Lymphocyte count ratio (NLCR) (Figure 4). In hematopoietic progenitors, stochastic changes in each factor’s concentration could result in one factor’s becoming more abundant and committing a hematopoietic progenitor to a particular lineage. To generate each mature granulocyte population (e.g. basophils, eosinophils and neutrophils), common myeloid precursor cells (CMPs) and later precursors for granulocytic and monocytic lineages (GMPs) follow in the BM different lineage commitment programs, tightly-regulated or instructed by a specific set of soluble factors, cell-cell interactions and transcription factors, that define cell fate decisions and lineage restrictions. For instance, differential PU.1 activity can specify different cell fates during haematopoiesis regulating monocyte and neutrophils differentiation. Genetic and biochemical analyses have shown that G-CSF can direct granulocyte differentiation by changing the ratio of C/EBPα to PU.1 (Zhu et al., Oncogene 2002; Friedman Oncogene 2002; Dahl et al., Nat Immunol 2003). High expression levels of PU.1 and C/EBPa, stimulated by G-CSF, promote GMP differentiation to neutrophils and inhibits monocyte differentiation, while only PU.1 expression, IRF-8 and lower expression/activity of C/EBPs induce GMP differentiation to monocytes (Zhu et al., Oncogene 2002; Friedman Oncogene 2002; Dahl et al., Nat Immunol 2003). Meanwhile, a combination of PU.1, C/EBPb and low levels of GATA-1 differentiates GMPs to eosinophil lineage (Kulessa et al., 1995; McDevitt et al., 1997; Yamaguchi et al., 1999) and PU.1 must also cooperate with GATA2 to direct mast cell differentiation (Walsh et al., Immunity 2002). In addition, eosinophil and basophil differentiation are induced by a different set of cytokines, usually produced in prevalent T-helper 2 response, such as IL-5, which should be inhibited in the strong Th1 environment evidenced by our and previous Luminex data in Pv patients. The enrichment of activated neutrophils in the peripheral circulation of P. vivax patients could be due to a response that specifically enhances neutrophil production and release from the bone marrow (BM). This hypothesis is supported by emerging evidence for enrichment of P. vivax parasites in the hematopoietic niche of BM, our Luminex data showing significant increase in pro-inflammatory cytokines associated with emergency myelopoiesis (e.g., TNF-a, IL-1a, IL-1b, IL-6, IL-8), and increased circulating levels of G-CSF, the major inducer of neutrophils production in the BM. Likewise, increased activation-induced cell death (AICD) in T cells, splenic T-cell and platelet accumulation or decreased lymphopoiesis due to myeloid-biased HSC differentiation induced by inflammatory cytokines and EC activation in the BM (refs 36,37,39) might explain the neutrophil enrichment in vivax patients.

5- I would also ask the authors to speculate a bit on, What could be the mechanism behind the different function of P. vivax compared to P. falciparum? From an evolutionary perspective, the parasite should rather become softer and keep the host alive for its own benefit.

Answer: One of the characteristics of P. vivax that could play an important role in immunity is its restriction to invade immature reticulocytes. For example, the infected reticulocyte could play a role in the presentation of parasite antigens as reticulocytes (but not mature RBCs) express MHC-I and are capable to process and present antigens on their surface for recognition by T cells. Indeed, it has been shown that reticulocytes act directly as an antigen-presenting cell, emphasizing the importance of erythrocyte surface antigens both in the induction as well as the target of a protective immune response (Burel et al 2016, Junqueira et al 2018). Recent investigations comparing P. vivax and P. falciparum controlled human infection models (CHMIs) also revealed marked differences in the immune profiles generated following infection with the two species and postulated that protective immune responses to Plasmodium are species-specific. It has been hypothesized that this difference is due to strict P. vivax tropism for MHC-I-expressing reticulocytes that, unlike mature red blood cells, can present antigen directly to CD8+T cells. Specifically, P. vivax but not P. falciparum infection led to the expansion of a specific subset of CD38+CD8+ T cells which were associated with an activated phenotype and cytotoxic potential. Corroborating Burel et al findings in the CHMI model, Junqueira et al showed that P. vivax–infected reticulocytes express HLA-I. In P. vivax-infected patients, CD8+ T cells in the peripheral blood express high levels of cytotoxic proteins, recognize and form immunological synapses with P. vivax–infected reticulocytes in HLA–dependent manner. Next, it was showed that P. vivax-specific CD8+ T cells release their cytotoxic granules to kill both host cell and intracellular parasite, which prevented reinvasion (Junqueira et al 2018). Although these data indicate a protective role of cytotoxic CD8+ T cells during P. vivax blood-stage malaria, it is not clear whether these lymphocytes would always be beneficial because they might contribute to anemia, inflammation or other pathological sequelae of infection, which needs to be further investigated.

**Minor comments:**

• It is important to have a reference, version, and date for the R software, packages and GraphPad.

Answer: We have added version and date for the R and GraphPad software.

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2- In Fig 5, E missed to report. This figure can be better organised. It is very hard to read and follow.

Answer: There is no E in Figure 5. We will organize the figure to make it easier to read and follow.

Reviewer #2 (Significance (Required)):

1. • vivax remains endemic in 51 countries across Central and South Americas, the Horn of Africa, Asia and the Pacific islands. In most areas it is co-endemic with P. falciparum, which has been the priority species to address for national malaria control programmes. Malaria related deaths are mostly attributable to the more pathogenic P. falciparum, but over the last decade these have declined, however there has been a consistent rise in the proportion of malaria cases due to P. vivax. However, because it is difficult to diagnose resistant strains, strategies to detect and track drug resistant P. vivax* are limited. In this context it is vital to develop better tools to assess diagnostic, antimalarial efficacy and drug susceptibility so that emerging drug resistance can be tracked, and novel treatment strategies explored. From my viewpoint, despite some statistical problems to understand the complex nature of data (mixed interactions among multiple variables), these findings seem to be very interesting and (after a major revision) worth to be published. As said before, the story told by the authors could become interesting.

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

The manuscript titled: "Total parasite biomass but not peripheral parasitaemia is associated with endothelial and haematological perturbations in Plasmodium vivax patients" by Silva-Filho et al., reinforce the original observation and data by the group of Nicholas Anstey and coworkers, who first proposed the use of plasma parasite lactate dehydrogenase and PvLDH as a marker of parasite biomass. In that work, it was already demonstrated that P. vivax biomass is related to plasma concentration of LDH levels. As such, the present work cannot be considered of high novelty. Yet, through a meticulous approach including clinical data, computational approaches, machine learning, LDH measurement, multiplex analysis and quantitave RT-PCR, the authors here have extended the original observations that a large biomass of P. vivax parasites is out of blood circulation. In contrast, unlike the original observations of Anstey´s group, a correlation between total parasite biomass and systemic levels of markers of endothelial cells activation, was observed. The manuscript is very well written and the discussion brings new knowledge in this key topic for elimination of malaria. This manuscript is therefore recommended for publication after the following comments are addressed.

**Major comments:**

1. The vascular endothelium plays a pivotal role in malaria. Therefore, to test whether cell and/or parasite factors affect the vascular endothelium, HUVEC cells were used in this study. This is of major concern as endothelial cells from the bone marrow, where most hematological disturbances, notoriously thrombocytopenia, occur, were not used instead. HUVEC cells seems the only endothelial cell that does not express ABO blood group antigens, thus suggesting that surface expression on these cells is highly altered (O´Donnell et al., 2000 J Vasc Res). Moreover, significant functional differences between HUVEC cells and adult vascular endothelium have been reported (Chan et al., 2004). Together, this indicates that results obtained with HUVEC cells might not reflect responses of the bone marrow vascular endothelium. As one of the corresponding authors have ample experience with working with human bone marrow endothelial cells (Mantel et al., 2016 Nat Comm), it is suggested to perform some experiments with these cells to assure extrapolation of the results obtained with HUVEC cells.

Answer: We agree with the reviewer that performing ex vivo assays with primary human bone marrow endothelial cells would be an excellent alternative. However, we would like to argue that HUVECs are also suitable for our purposes. HUVECs are widely used to study endothelial barrier function, for example in the context of angiogenesis and inflammatory responses/barrier disruption. To emphasise this point, we have now referenced examples where HUVECs were used in the context of endothelial barrier biology and in different inflammatory conditions (see also lists a, b, c below).

1. Papers showing the use of HUVECs in studies yielding important insights about endothelial barrier function

• Krispin S et al. Growth Differentiation Factor 6 Promotes Vascular Stability by Restraining Vascular Endothelial Growth Factor Signaling. Arterioscler Thromb Vasc Biol. 2018.
• Aranda JF et al. MYADM controls endothelial barrier function through ERM-dependent regulation of ICAM-1 expression. Mol Biol Cell. 2013.
• Orsenigo F et al. Phosphorylation of VE-cadherin is modulated by haemodynamic forces and contributes to the regulation of vascular permeability in vivo. Nat Commun. 2012.
• *

1. Papers that used HUVECs in studies about endothelial barrier function in inflammatory conditions

• Dickinson CM et al. Leukadherin-1 ameliorates endothelial barrier damage mediated by neutrophils from critically ill patients. J Intensive Care. 2018.
• Kuck JL et al. Ascorbic acid attenuates endothelial permeability triggered by cell-free hemoglobin. Biochem Biophys Res Commun. 2018.
• Tramontini Gomes de Sousa Cardozo F et al. **Serum from dengue virus-infected patients with and without plasma leakage differentially affects endothelial cells barrier function in vitro. PLoS One. 2017.
• Fox ED et al. Neutrophils from critically ill septic patients mediate profound loss of endothelial barrier integrity. Crit Care. 2013.
• Rahbar E et al. Endothelial glycocalyx shedding and vascular permeability in severely injured trauma patients. J Transl Med. 2015.
• *

1. Papers showing that HUVECs behave similarly to other endothelial cell types in regard to barrier function, except when the comparison is with blood brain barrier models

• *

• Totani L et al. Mechanisms of endothelial cell dysfunction in cystic fibrosis. Biochim Biophys Acta Mol Basis Dis. 2017, Dec;1863(12):3243-3253.

• Gündüz D et al. Effect of ticagrelor on endothelial calcium signalling and barrier function. **Thromb Haemost. 2017 Jan 26;117(2):371-381.
• Deitch EA et al. Mesenteric lymph from rats subjected to trauma-hemorrhagic shock are injurious to rat pulmonary microvascular endothelial cells as well as human umbilical vein endothelial cells. ** 2001 Oct;16(4):290-3. Importantly, we were able to reproduce in the HUVEC ex vivo assays a phenotype of endothelial perturbations that is inferred based on the in vivo Luminex data using the same plasma sample. These data also support our hypothesis that patients with higher parasite biomass present higher endothelial cell perturbations, corroborating the associations between parasite accumulation in deep tissues (total parasite biomass represented by PvLDH levels) and endothelial cell activation as demonstrated in the Figure 6.

Strikingly, the authors stated that "P. vivax infection results in different ranges of EC alterations without massive cytoadhesion". This statement has no data supporting it. In fact, their own flow cytometry data convincingly demonstrated that exposure of HUVEC cells to plasma of vivax-high patients significantly increased the surface expression of ICAM-1 and VCAM. ICAM-1 expression is a well know receptor for cytoadhesion in malaria and Dr. Costa first demonstrated the importance of this receptor in cytoadherence of P. vivax (Carvalho et al., 2010). Moreover, these data are in some contradiction with the original observations of Anstey and collaborators who demonstrated that parasite LDH concentration did not correlate with markers of endothelial activation (Barber et al., 2015 PLoS Path). Therefore, this sentence should be modified to accommodate the alternative possibility of cytoadherence, deleted from the manuscript or binding functional assays should be performed to sustain it.

Answer: We agree with the reviewer and have removed this statement.

Page 22, line 543: The association between endothelial activation, Syndecan-1 and parasite biomass (PvLDH) indicates a positive feedback loop between glycocalyx breakdown, activation of endothelial receptors such as ICAM-1and VCAM-1 and parasite accumulation in deep tissues9,12.

Extracellular vesicles are key players in pathology of malaria and this includes P. vivax where concentration of circulating microparticles were associated with acute infections (Campos et al., 2010 Mal J). Moreover, Dr. Marti has pioneered this field since the original manuscript describing the role of EVs in malaria as intercellular communicators (Mantel et al., 2013 Cell). More recently, his group also demonstrated that interaction of EVs with bone marrow endothelial cells induce expression of IL-6 and IL-1 as well as vascular endothelium perturbations after trans-endothelial electrical resistance experiments (Mantel et al., 2016 Nat Comm). Furthermore, another recent report showed the physiological role of EVs in vivax malaria by demonstrating that EV uptake by human spleen fibroblast induced nuclear translocation of the NF-kB transcriptional factor, concomitant with surface expression of ICAM-1, thus facilitating cytoadherence of infected reticulocytes from P. vivax patients (Toda et al., 2020 Nat Comm). This growing evidence indicates that plasma circulating EVs are key communicators in malaria infections potentially explaining some of the findings reported in this work. Neglecting the importance of EVs in the discussion of this article is not reasonable and weakens this manuscript. Including a paragraph on EVs and accurate references in the discussion is thus strongly recommended.

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Answer: We agree with the reviewer that extracellular vesicles are key communicators in malaria infection. We have not measured them in our study, however, and therefore can only speculate about their impact on our observations. We have added a phrase in the discussion:

Page 27, line 661: It is likely that other circulating factors that we have not directly measured in our study are also contributing to EC activation and vascular permeability. In particular, extracellular vesicles (EV) originating from ECs, platelets, and RBCs are present during malaria infection and are known to modulate the host immune response to the parasite54-56 . In P. falciparum, infected RBCs release EVs containing immunogenic parasite antigens, that activate macrophages, induce neutrophil migration and alter endothelial barrier function54,55. In P. vivax, plasma-derived EVs from iRBCs are taken up by human spleen fibroblasts (hSFs). This event signals NF-kB translocation and upregulation of ICAM-1 expression, facilitating cytoadherence of P. vivax-infected reticulocytes56.

**Minor comments:**

1. The lack of a group including severe vivax malaria patients is a drawback of this article as this group would have firmly validated the predictor of severe disease.

Answer: This study was investigating a cohort of uncomplicated P. vivax malaria compared to controls. We agree that it will be important to extent our analysis to severe vivax malaria in future studies.

In the selection criteria of the patients to be included in the study, no information on other co-infections were mentioned. Is this information available? If so, this should be mentioned.

Answer: As described in the Methods sections, Page 6, line 132, mono infection by P. vivax was confirmed by analysis of blood smears and quantitative PCR (qPCR) for both P. vivax and P. falciparum. We agree that excluding other coinfections could have been of interest. However, the differential diagnosis for an acute febrile illness is very broad and it would be impractical to track all other possible diseases. In addition, the patients included in the present work had mild disease, and therefore were discharged from hospital after a positive malaria diagnosis. No further investigation on other infections was done.

The main coinfection to be considered for an acute febrile illness with no localizing signs in our context is Dengue Fever. Although Dengue coinfection in our cohort is possible, the incidence at the Hospital is only 2.8% (P. vivax/Dengue coinfection) (Magalhães et al, Plos NTD 2014). Thus, it is unlikely that such a coinfection would have a major impact on our findings.

This work determined the levels of PvLDH in a cohort of uncomplicated P. vivax patients as well as healthy volunteers using a double-sandwich ELISA assay: (i) are the clones to determine PvLDH values freely available to facilitate similar studies by independent groups? (ii) How was the cut-off of positivity defined? This is not evident, neither in the materials and methods, nor in the results.

Answer: Clones are commercially available and were purchased from Vista Diagnostics International LLC, WA, USA. Information has been amended to the text in the Methods section.

Page 8, line 186: “Cut-off of positivity was defined by correcting absorbance values generated in the plasma samples from healthy donors (controls) by blank values (plate controls), with both values being in the same range. Absorbance values higher than controls were considered positive. In parallel, we used schizont extracts to perform standard curves and lower absorbance values were in the range of O.D = 0.03-0.04. All positive patient samples gave O.D. values equal or higher than 0.05. This information has also been added in the Methods section.:

It is not clear why varying percentages of pooled plasma (30% for imaging and flow cytometry, and 20% for impedance changes) from the different clusters were used for the functional EC assays. Moreover, no information about the concentration of plasma used for transcriptional analysis is available. Please clarify.

Answer: The concentration of 30% pooled plasma was also used for transcriptional analysis, as indicated in the Methods section, page 11, line 250. This information was also added in the legend of Figure 5B. We had run several optimisation time-course and titration experiments with individual plasma samples, testing concentrations of plasma varying from 10% up to 30% v/v and we did not observe differences in mRNA expression between 20% and 30% v/v plasma conditions.

As for the ECIS, our collaborators (Erich V de Paula group) have optimised this assay and they use a range of 15 to 20% (Santaterra et al 2020). Higher concentrations of plasma reduces the reproducibility, probably to fibrin formation.

Reference 9 is a nonhuman primate study where no LDH is used. Please remove it.

Answer: Reference 9 has been removed following the reviewer suggestion.

Reference 39 is a review on the subject and cannot be included in the sentence on line 556 "In agreement with a previous study8,39, where reference 8 is accurate. Please remove reference 39 from here.

Answer: The text has been amended as suggested.

Reviewer #3 (Significance (Required)):

This paper further contributes to explain the conundrum of low peripheral blood parasitemia and clinical severity in P. vivax. Moreover, by including new human markers and solidly applying computational tools, this paper further contributes to advance clinical research in P. vivax.

Clinical diagnosis of hematological disorders including anemia, lymphopenia and thrombocytopenia, are routinely obtained from a complete blood count. Therefore, I believe the major significance of this work is to raise public health awareness of including in these clinical examinations, the determination of PvLDH levels. They might prognose, as suggested by the authors, better diagnosis and treatment of P. vivax,

My main expertise is the biology of host-pathogen interactions with a focus on P. vivax.

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Reviewer #4 (Evidence, reproducibility and clarity (Required)):

The study evaluates P. vivax biomass (serum LDH) versus peripheral parasitemia with multiple variables. From the biomass Vivax high vs. Vivax low, they compare multiple determination in patients with uncomplicated P. vivax. This raises questions about disease and the presence of parasites in various organs. The question is if P. vivax sequesters and the answer is yes in the bone marrow and spleen. Does it sequester like P. falciparum that causes disease by sequestration by binding endothelium in various organs. That is less clear. As P. vivax is rarely fatal, the sequestration has not been studied. The presence of parasites in organs of P. vivax infected splenectomized squirrel and Aotus monkeys has been found in bone marrow and liver (note: splenecotomized monkeys so parasitemia can rise to higher levels than in non-splenectomized monkeys). There are studies of binding of schizonts infected red cells to lung endothelium in vitro does not answer the question of whether sequestration occurs in vivo.

The most important complication of P. vivax is generally anemia. This did not correlate with vivax biomass, but this raises the question of the length of infection and the possibility that parasite biomass may vary at different times of infection. Anemia was seen in P. vivax infected patients, but it did not relate to biomass at the time of study. Note the caveat mentioned in the previous sentence on long term effects of infection on anemia.

The finding of biomass with reduced platelet counts and endothelial effects that may be related to a serum factor and not sequestration. This is the main limitation of the paper besides the unknown long term effect infection. If one could identify an effect of P. vivax infected human serum, this may be worth a study in the future on what is in serum causing the effects.

Reviewer #4 (Significance (Required)):

This study is unique with the caveats mentioned above. It has a good review of the literature.

Answer: We appreciate the reviewer comments. In our cohort, the frequency of anaemia was not as high or severe as the frequency of thrombocytopenia and lymphopenia. However, we still find associations between endothelial cell activation marker Ang-2 and the pro-inflammatory cytokine IL-1 IL-1 negatively associated with several markers of anaemia, such as haemoglobin, haematocrit and RBC numbers. Although we did not further investigate this association, it may indicate indirect effects of parasite biomass on anaemia mediated by inflammation and EC activation, which will be further investigated in other current longitudinal cohort studies.

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Referee #3

Evidence, reproducibility and clarity

The study evaluates P. vivax biomass (serum LDH) versus peripheral parasitemia with multiple variables. From the biomass Vivax high vs. Vivax low, they compare multiple determination in patients with uncomplicated P. vivax. This raises questions about disease and the presence of parasites in various organs. The question is if P. vivax sequesters and the answer is yes in the bone marrow and spleen. Does it sequester like P. falciparum that causes disease by sequestration by binding endothelium in various organs. That is less clear. As P. vivax is rarely fatal, the sequestration has not been studied. The presence of parasites in organs of P. vivax infected splenectomized squirrel and Aotus monkeys has been found in bone marrow and liver (note: splenecotomized monkeys so parasitemia can rise to higher levels than in non-splenectomized monkeys). There are studies of binding of schizonts infected red cells to lung endothelium in vitro does not answer the question of whether sequestration occurs in vivo.

The most important complication of P. vivax is generally anemia. This did not correlate with vivax biomass, but this raises the question of the length of infection and the possibility that parasite biomass may vary at different times of infection. Anemia was seen in P. vivax infected patients, but it did not relate to biomass at the time of study. Note the caveat mentioned in the previous sentence on long term effects of infection on anemia. The finding of biomass with reduced platelet counts and endothelial effects that may be related to a serum factor and not sequestration. This is the main limitation of the paper besides the unknown long term effect infection. If one could identify an effect of P. vivax infected human serum, this may be worth a study in the future on what is in serum causing the effects.

Significance

This study is unique with the caveats mentioned above. It has a good review of the literature.

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Referee #2

Evidence, reproducibility and clarity

The manuscript titled: "Total parasite biomass but not peripheral parasitaemia is associated with endothelial and haematological perturbations in Plasmodium vivax patients" by Silva-Filho et al., reinforce the original observation and data by the group of Nicholas Anstey and coworkers, who first proposed the use of plasma parasite lactate dehydrogenase and PvLDH as a marker of parasite biomass. In that work, it was already demonstrated that P. vivax biomass is related to plasma concentration of LDH levels. As such, the present work cannot be considered of high novelty. Yet, through a meticulous approach including clinical data, computational approaches, machine learning, LDH measurement, multiplex analysis and quantitave RT-PCR, the authors here have extended the original observations that a large biomass of P. vivax parasites is out of blood circulation. In contrast, unlike the original observations of Anstey´s group, a correlation between total parasite biomass and systemic levels of markers of endothelial cells activation, was observed. The manuscript is very well written and the discussion brings new knowledge in this key topic for elimination of malaria. This manuscript is therefore recommended for publication after the following comments are addressed.

Major comments:

1. The vascular endothelium plays a pivotal role in malaria. Therefore, to test whether cell and/or parasite factors affect the vascular endothelium, HUVEC cells were used in this study. This is of major concern as endothelial cells from the bone marrow, where most hematological disturbances, notoriously thrombocytopenia, occur, were not used instead. HUVEC cells seems the only endothelial cell that does not express ABO blood group antigens, thus suggesting that surface expression on these cells is highly altered (O´Donnell et al., 2000 J Vasc Res). Moreover, significant functional differences between HUVEC cells and adult vascular endothelium have been reported (Chan et al., 2004). Together, this indicates that results obtained with HUVEC cells might not reflect responses of the bone marrow vascular endothelium. As one of the corresponding authors have ample experience with working with human bone marrow endothelial cells (Mantel et al., 2016 Nat Comm), it is suggested to perform some experiments with these cells to assure extrapolation of the results obtained with HUVEC cells.
2. Strikingly, the authors stated that "P. vivax infection results in different ranges of EC alterations without massive cytoadhesion". This statement has no data supporting it. In fact, their own flow cytometry data convincingly demonstrated that exposure of HUVEC cells to plasma of vivax-high patients significantly increased the surface expression of ICAM-1 and VCAM. ICAM-1 expression is a well know receptor for cytoadhesion in malaria and Dr. Costa first demonstrated the importance of this receptor in cytoadherence of P. vivax (Carvalho et al., 2010). Moreover, these data are in some contradiction with the original observations of Anstey and collaborators who demonstrated that parasite LDH concentration did not correlate with markers of endothelial activation (Barber et al., 2015 PLoS Path). Therefore, this sentence should be modified to accommodate the alternative possibility of cytoadherence, deleted from the manuscript or binding functional assays should be performed to sustain it.
3. Extracellular vesicles are key players in pathology of malaria and this includes P. vivax where concentration of circulating microparticles were associated with acute infections (Campos et al., 2010 Mal J). Moreover, Dr. Marti has pioneered this field since the original manuscript describing the role of EVs in malaria as intercellular communicators (Mantel et al., 2013 Cell). More recently, his group also demonstrated that interaction of EVs with bone marrow endothelial cells induce expression of IL-6 and IL-1 as well as vascular endothelium perturbations after trans-endothelial electrical resistance experiments (Mantel et al., 2016 Nat Comm). Furthermore, another recent report showed the physiological role of EVs in vivax malaria by demonstrating that EV uptake by human spleen fibroblast induced nuclear translocation of the NF-kB transcriptional factor, concomitant with surface expression of ICAM-1, thus facilitating cytoadherence of infected reticulocytes from P. vivax patients (Toda et al., 2020 Nat Comm). This growing evidence indicates that plasma circulating EVs are key communicators in malaria infections potentially explaining some of the findings reported in this work. Neglecting the importance of EVs in the discussion of this article is not reasonable and weakens this manuscript. Including a paragraph on EVs and accurate references in the discussion is thus strongly recommended.

Minor comments:

1. The lack of a group including severe vivax malaria patients is a drawback of this article as this group would have firmly validated the predictor of severe disease.
2. In the selection criteria of the patients to be included in the study, no information on other co-infections were mentioned. Is this information available? If so, this should be mentioned.
3. This work determined the levels of PvLDH in a cohort of uncomplicated P. vivax patients as well as healthy volunteers using a double-sandwich ELISA assay: (i) are the clones to determine PvLDH values freely available to facilitate similar studies by independent groups? (ii) How was the cut-off of positivity defined? This is not evident, neither in the materials and methods, nor in the results.
4. It is not clear why varying percentages of pooled plasma (30% for imaging and flow cytometry, and 20% for impedance changes) from the different clusters were used for the functional EC assays. Moreover, no information about the concentration of plasma used for transcriptional analysis is available. Please clarify.
5. Reference 9 is a nonhuman primate study where no LDH is used. Please remove it.
6. Reference 39 is a review on the subject and cannot be included in the sentence on line 556 "In agreement with a previous study8,39, where reference 8 is accurate. Please remove reference 39 from here.

Significance

This paper further contributes to explain the conundrum of low peripheral blood parasitemia and clinical severity in P. vivax. Moreover, by including new human markers and solidly applying computational tools, this paper further contributes to advance clinical research in P. vivax.

Clinical diagnosis of hematological disorders including anemia, lymphopenia and thrombocytopenia, are routinely obtained from a complete blood count. Therefore, I believe the major significance of this work is to raise public health awareness of including in these clinical examinations, the determination of PvLDH levels. They might prognose, as suggested by the authors, better diagnosis and treatment of P. vivax,

My main expertise is the biology of host-pathogen interactions with a focus on P. vivax.

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Referee #1

Evidence, reproducibility and clarity

This study focused on P. vivax, which is an important neglected human malaria killer. The reported evidence will have a significant impact on diagnosing infectious diseases. The language in the manuscript is very good. However, some typos were reported. Some paragraphs might need particular attention to punctuation. Overall, the work is very good. The statistics are straight forward. However, there are a couple of major points that must be addressed before publication. Some of my comments are just recommendations to clarify some sections of the text.

Major comments:

The statistical methods can be improved by using generalised mixed models (GLMM).

1- PCA graphs need to be organised in more descriptive ways. Dim1 and Dim2 in each axis need to be defined clearly in the figures. PCA in Fig2 c is very difficult to follow, and it needs to be organised.

2- In this study, patients were male and female, and we know already male and female haematological parameters are hugely different, specially Hb level, and so on. My question is how the sex variable is treated in this study? Did your control group were from both sexes? Sex could be treated as a random variable in all studies if GLMM models were used.

3- Why 6h and 18h used for the HUVEC evaluation?

4- It is mentioned only neutrophil enriched in this study, if myelopoiesis is affected, why the other granulocytes were not showed significant enhancement?

5- I would also ask the authors to speculate a bit on, What could be the mechanism behind the different function of P. vivax compared to P. falciparum? From an evolutionary perspective, the parasite should rather become softer and keep the host alive for its own benefit.

Minor comments:

1- It is important to have a reference, version, and date for the R software, packages and GraphPad.

2- In Fig 5, E missed to report. This figure can be better organised. It is very hard to read and follow.

Significance

P. vivax remains endemic in 51 countries across Central and South Americas, the Horn of Africa, Asia and the Pacific islands. In most areas it is co-endemic with P. falciparum, which has been the priority species to address for national malaria control programmes. Malaria related deaths are mostly attributable to the more pathogenic P. falciparum, but over the last decade these have declined, however there has been a consistent rise in the proportion of malaria cases due to P. vivax. However, because it is difficult to diagnose resistant strains, strategies to detect and track drug resistant P. vivax are limited. In this context it is vital to develop better tools to assess diagnostic, antimalarial efficacy and drug susceptibility so that emerging drug resistance can be tracked and novel treatment strategies explored.

From my viewpoint, despite the some statistical problems to understand the complex nature of data (mixed interactions among multiple variables), these findings seem to be very interesting and (after a major revision) worth to be published. As said before, the story told by the authors could become interesting.

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Reply to the reviewers

We thank the reviewers for their evaluation and are pleased that they appreciated both the significance and the novelty of our work, as well as the quality of its execution. Please find below a reply to the comments made by the reviewers.

To address the point raised by reviewer #1, we used a BY strain (from an S288C background), which is one of the most widely used lab strains in yeast genetics. Although a mutation in the HAP1 gene was identified in this strain, it does not compromise the ability of the cells to respire, as shown in our experiments performed in a non-fermentative medium in this manuscript (Fig. 2). Similarly, we have already published growth curves, drop tests, and proliferation rates of this strain in glycerol/ethanol or lactate-containing medium (please see Jimenez et al., JCS, 2014). More importantly, detailed respiration parameters have been measured for our BY background by the Daignan-Fornier lab, a long-standing Sagot lab collaborator (please see Gauthier et al., Mol Mic, 2008). Last, we have previously shown that upon quiescence establishment, there is no difference in mitochondrial network reorganization between BY/S288C and W303 or CEN PK background (Laporte et al., Elife, 2018, Fig2 SupFig1 F-G). Altogether, these results indicate that using this particular lab strain background does not detract from the generality of the observations reported in our manuscript. We will include a short discussion on this specific topic in the main text in a full revision.

Regarding reviewer #2’s comments, we are committed to providing all necessary details to fully replicate the microfluidic devices upon a final revision of our manuscript to make it widely accessible to the research community.

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

These investigators have teamed up to solve a technical problem that has thwarted efforts to get a clear picture of the chronology of events in yeast cultures as they naturally exhaust their nutrient supply. This is a challenge because the time course is long and the density of the culture makes single cell analysis problematic. Previous studies involving abrupt starvation have shown that there is a pH drop when nutrients are eliminated, but abrupt starvation also leads to rapid loss of viability compared to what is observed with cells as they respond and adapt to changes in their environment. This microfluidic devise and an intracellular pH detector allowed them to follow pH change as cells transition from fermentation to respiration and stationary phase. About 15% of the population responds completely differently than the other 85%, making this single cell analysis crucial. It also provides a negative control of sorts, to further substantiate the correlations they draw. This 15% fails to enter the respiratory phase and dies rapidly. The pH also drops rapidly and is correlated with loss of mitochondrial function and aggregation of proteins. The 85% of cells that succeed in shifting to respiration suffer the same pH drop, but it is much slower and is correlated with slower protein aggregation, P Body, actin body, and proteosome storage Granule assembly. They also followed the cytoplasmic transition to a glassy state, based on the mobility of protein foci and lipid droplets. This transition occurs at the same pH in both populations but with completely different timing. This recapitulates the transition observed after abrupt starvation. It shows that the same transition occurs in viable, quiescent cells and provide further evidence that it is correlated with pH changes.

The only concern I have is that they used only one strain, which reduces the universality of their findings. Moreover, it is ambiguous which strain was used. The strain table says they used S288c which is known to carry a hap1 mutation that compromises respiration and isn't the best choice for studying respiring cells. The text mentions that they are working in the BY background, (where most of their GFP studies have been carried out. The BY strains have the same hap1 mutation and several other unknown polymorphisms that prevent ethanol utilization and biomass increase after the diauxic shift.

Reviewer #1 (Significance (Required)):

This kind of single cell analysis is clearly the way forward and will have many further applications to understanding how cells adapt to their environment. The paper is well written and the figures are well laid out and easy to understand. It is a significant advance for the field and will set the bar for future experiments. However, this work was done with a single strain that is known to be defective in respiration. It would be extremely valuable to know if their results with this strain are generalizable to other lab and wild strains.

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

In this manuscript, the authors interrogated single cells of yeast as they developed into quiescence after the natural depletion of glucose from the culture medium. To do so, they constructed a microfluidic platform to track individual cells in a batch culture of cells transitioning from a growing phase into stationary phase. They then used a number of assays to monitor the metabolic changes that accompany this transition. They observed that internal pH dropped during development of quiescence, with some cells showing a rapid drop and others showing a delayed and heterogeneous drop. At diauxie, cells transition from fermentation to respiration, and the minority of cells that showed a rapid drop in pH were respiration-deficient (R-) and unable to resume growth, while cells with a delayed pH drop were respiration proficient (R+) and able to resume growth. Using established markers to follow the previously described structural changes that accompany the development of quiescence, they found that the pH changes were temporally related to these structural changes. They suggest that the dynamic changes in intracellular pH promote waves of structural remodeling that eventually leads to a transition of cells to a gel-like state. The early drop in pH in R- cells was proposed to lead to a precocious transition of the cytoplasm, contributing to the inability of these cells to resume growth.

This study is well done, well-written, and the results are clearly presented and generally convincing. Data accumulation and analysis were well documented and appropriate statistics were used. While the authors provided details of the materials used to construct the microfluidic device, it would be appropriate for them to provide a detailed blueprint (and a video, for example) to other investigators who would like to employ this device in their studies of quiescence once this manuscript has been published.

Reviewer #2 (Significance (Required)):

The cell fate program that is set in motion as yeast cells transition from fermentation to respiration is still not well understood. The development of the microfluidic platform described in this manuscript could make a significant contribution to our understanding of the succession of metabolic and structural changes occurring during this transition. The Sagot lab has made a series of important contributions in this area, and the application of single cell tracking to monitor the temporal program of these changes represents a major technical advance that will be of general interest to researchers interested in defining the developmental programs that contribute to cellular quiescence and longevity.

Expertise: yeast chromatin biology

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, the authors interrogated single cells of yeast as they developed into quiescence after the natural depletion of glucose from the culture medium. To do so, they constructed a microfluidic platform to track individual cells in a batch culture of cells transitioning from a growing phase into stationary phase. They then used a number of assays to monitor the metabolic changes that accompany this transition. They observed that internal pH dropped during development of quiescence, with some cells showing a rapid drop and others showing a delayed and heterogeneous drop. At diauxie, cells transition from fermentation to respiration, and the minority of cells that showed a rapid drop in pH were respiration-deficient (R-) and unable to resume growth, while cells with a delayed pH drop were respiration proficient (R+) and able to resume growth. Using established markers to follow the previously described structural changes that accompany the development of quiescence, they found that the pH changes were temporally related to these structural changes. They suggest that the dynamic changes in intracellular pH promote waves of structural remodeling that eventually leads to a transition of cells to a gel-like state. The early drop in pH in R- cells was proposed to lead to a precocious transition of the cytoplasm, contributing to the inability of these cells to resume growth.

This study is well done, well-written, and the results are clearly presented and generally convincing. Data accumulation and analysis were well documented and appropriate statistics were used. While the authors provided details of the materials used to construct the microfluidic device, it would be appropriate for them to provide a detailed blueprint (and a video, for example) to other investigators who would like to employ this device in their studies of quiescence once this manuscript has been published.

Significance

The cell fate program that is set in motion as yeast cells transition from fermentation to respiration is still not well understood. The development of the microfluidic platform described in this manuscript could make a significant contribution to our understanding of the succession of metabolic and structural changes occurring during this transition. The Sagot lab has made a series of important contributions in this area, and the application of single cell tracking to monitor the temporal program of these changes represents a major technical advance that will be of general interest to researchers interested in defining the developmental programs that contribute to cellular quiescence and longevity.

Expertise: yeast chromatin biology

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Referee #1

Evidence, reproducibility and clarity

These investigators have teamed up to solve a technical problem that has thwarted efforts to get a clear picture of the chronology of events in yeast cultures as they naturally exhaust their nutrient supply. This is a challenge because the time course is long and the density of the culture makes single cell analysis problematic. Previous studies involving abrupt starvation have shown that there is a pH drop when nutrients are eliminated, but abrupt starvation also leads to rapid loss of viability compared to what is observed with cells as they respond and adapt to changes in their environment. This microfluidic devise and an intracellular pH detector allowed them to follow pH change as cells transition from fermentation to respiration and stationary phase. About 15% of the population responds completely differently than the other 85%, making this single cell analysis crucial. It also provides a negative control of sorts, to further substantiate the correlations they draw. This 15% fails to enter the respiratory phase and dies rapidly. The pH also drops rapidly and is correlated with loss of mitochondrial function and aggregation of proteins. The 85% of cells that succeed in shifting to respiration suffer the same pH drop, but it is much slower and is correlated with slower protein aggregation, P Body, actin body, and proteosome storage Granule assembly. They also followed the cytoplasmic transition to a glassy state, based on the mobility of protein foci and lipid droplets. This transition occurs at the same pH in both populations but with completely different timing. This recapitulates the transition observed after abrupt starvation. It shows that the same transition occurs in viable, quiescent cells and provide further evidence that it is correlated with pH changes.

The only concern I have is that they used only one strain, which reduces the universality of their findings. Moreover, it is ambiguous which strain was used. The strain table says they used S288c which is known to carry a hap1 mutation that compromises respiration and isn't the best choice for studying respiring cells. The text mentions that they are working in the BY background, (where most of their GFP studies have been carried out. The BY strains have the same hap1 mutation and several other unknown polymorphisms that prevent ethanol utilization and biomass increase after the diauxic shift.

Significance

This kind of single cell analysis is clearly the way forward and will have many further applications to understanding how cells adapt to their environment. The paper is well written and the figures are well laid out and easy to understand. It is a significant advance for the field and will set the bar for future experiments. However, this work was done with a single strain that is known to be defective in respiration. It would be extremely valuable to know if their results with this strain are generalizable to other lab and wild strains.

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Reply to the reviewers

Response/revision plan

(Point-by-point response)

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

The manuscript by Pennauer et al is the first to systematically investigate the role of class I&II Arfs using a knockout approach. It builds on earlier work by the Kahn lab who used an RNAi approach (Volpicelli-Daley et al. 2005) and is complementary to the overexpression approach used by the Hauri lab (Ben-Tekaya et al, 2010). The work is elegant and the data are strong. I am strongly in favor of publishing this work and my comments are technical in nature (2-5) and a request for some text changes (1). have the following comments for improvements:

1- When it comes to evaluating the role of depletions of Arfs on cell fitness, it would be better to use a non-transformed cell line. I am not asking the authors to go through the painstaking process of generating knockout cell lines in RPE1 cells for instance. Rather, I suggest that the authors make the reader aware that conclusions about cell survival have to be taken with care due to the use of a transformed cell line.

We will add this valid point to the Discussion.

2- Why do Arf1 and Arf4 ko cells grow more slowly. Is it a higher rate of cell death? Is it a block in a certain phase of the cell cycle. Given the link of the Golgi to G2-M entry, I think that an analysis of the cell cycle distribution would add more depth to these data. If the cell cycle distribution is unaffected, then I would conclude that that the difference in doubling time are due to reduced cell survival. If there is an effect on the cell cycle distribution, then the conclusion of the authors is safe that no single Arf is required for survival

We plan to analyze cell cycle distribution.

3- It is not clear to me how many cells were quantified in Figure 2D-F. I suppose that each dot represents a cell. In this case, the number of cells quantified is a bit low. Such a quantification of fluorescence intensities in two channels in the same region is a simple task and I think it should be no problem obtaining at least 100 cells per condition.

We will add the number of cells analyzed to the figure legends: At least 40 Golgis were quantified in each experiment. thus >100 in total.

4- Is the drop in the ratio of beta-COP/GM130 in Arf1 depleted cells reflecting reduced recruitment to the Golgi? Because the Golgi is bigger, it might be reflecting a reduced density in the number of coatomer molecules per surface area. If it is due to reduced recruitment, then the ratio of membrane/cytosolic betaCOP should be altered. This of course requires to show that the knockout does not affect total levels of coatomer. I think that such fractionation experiments would be a valuable addition to the manuscript and increase the depth of the data.

We are currently performing immunoblot analysis to determine bCOP levels.

In the Figure below, we have plotted the total intensity of GM130 or bCOP per Golgi from our immunoflurescence data. Total intensity of GM130 significantly increased in the cell lines lacking Arf1, consistent with the increase in Golgi volume. The amount of bCOP at the Golgi remained constant, resulting in reduced bCOP/GM130 ratio. Deletion of Arf1 thus results in reduced rate of coat recruitment that is compensated by an increase in Golgi mass. In the simplest model, reduced formation of Golgi-exit carriers causes Golgi growth until exit carrier formation allows for the required flux.

We propose to include this data in the revised manuscript.

FIGURE

5- The finding that Arf4-ko cells exhibit a defect on retrieval of ER-resident proteins is exciting, and in my opinion, it is the most significant finding in this manuscript. How can this be reconciled with the lack of an ARf4 ko effect on coatomer recruitment to the Golgi. Looking carefully at the data, I see that in 2 out of 3 experiments, Arf4 ko reduced the betaCOP/GM130 ratio. This is why I think it is crucial to perform more experiments and add more cells to increase the confidence in the data. Reduced retrieval of ER chaperones is frequently found in tumors and we still don't understand the reason behind this. Therefore, this finding is of significance beyond the community of cell biologists.

We plan to repeat quantitation with COPI for better statistical validity.

6- I find Figure 6A confusing. Why do Arf1 overexpressing parental HeLa cells exhibit less Arf1 than control cells?

In order not to overload the immunoblot of Arf overexpressing lysates, a smaller aliquot (1/20) was loaded. We will indicate this directly below the blots to make this more obvious in the revised figure.

7- Why was the following condition not tested: Arf4ko cells with Arf1 overexpression. Given the importance of Arf1 in retrograde (Golgi-to-ER) trafficking, I would expect a partial rescue of the retrieval of ER chaperones.

We will to do this experiment.

Reviewer #1 (Significance (Required)):

**Significance of the work:**

The paper is important because it is the first to examine the role of Arfs using a knockout approach. Another very important finding is that Arf4 depleted cells exhibit problems with retrieval of ER chaperones. This is a very novel finding and to the best of my knowledge

**Audience:**

The primary audience is of course the community working on membrane trafficking, organelle biology and proteostasis. However, I think that the data on the role of Arf4 in retrieval of ER chaperones might be of relevance for cancer biologists. Secretion of ER chaperones is frequently found in many tumors and we still do not understand why this is happening and what the significance thereof is.

**My own expertise:**

Export from the endoplasmic reticulum Golgi fragmentation in cancer cell migration Rho GTPases Kinase signaling Pseudoenzymes Cell migration of breast cancer cells Proteostasis in multiple myeloma

**Referee Cross-commenting**

Just a follow-up comment from my side:

I agree that it has not been unequivocally established that Arf1 is the main/sole of retrograde transport. However, even less established is the role of Arf4 in this process. The authors show that it is mainly Arf1 depletion that reduces the amount of COPI at the Golgi (ratio of COPI/GM130). Thus, I remain very surprised that it is actually the Arf4 depletion that results in reduced retrieval.

What is the significance of having less COPI at the Golgi in Arf1-ko cells? Certainly, the Golgi is not more "leaky". Does the level of COPI at the Golgi not reflect the strength of retrograde trafficking? Maybe there is no less COPI at the Golgi, and it only appears to be less, because the Golgi is bigger. This is why a simple fractionation experiment would be good. Something like making a cytosol and a microsome fraction and looking at the ratio of COPI (Cyt/Mem).

If both reviewers think it is too much, or unlikely to work, then I am happy to drop this point.

Below are my comments to the evaluations by the other two reviewers:

1- I agree with most comments that the two other reviewers made. Some of them are actually overlapping with mine (e.g. the use of a cell line other than HeLa).

2- I am not sure whether the impact of the paper would improve by adding data on Arf6.

3- To the comment on Golgi polarity. Maybe we could be more specific here and say that it would be sufficient to show that a trans-Golgi protein and a cis-Golgi protein can be separated by fluorescence microscopy, or whether we alternatively want them to actually do it by immunogold labeling for EM (which is more difficult).

4- I agree with reviewer 2 that the work proposed needs 1-3 months. I think reviewer 3 is a bit too optimistic with 1 month, because her/his comment on using a cell line other than HeLa cannot be addressed in just a month.

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

Pennauer uses HeLa cells and CRISPR/Cas9 to delete the 5 members of the class I and class II ARF family of small regulatory GTPases either individually or in combinations. The characterization of the KO cells is excellent and convincingly demonstrates that true KOs were generated. The quality of the data presented is high. Using the KO cells she documents minor alterations in Golgi architecture and the recruitment of vesicular coats in cells deleted of all ARFs except ARF4. In contrast, there is a significant lack of retention/recycling to the ER of KDEL-containing ER proteins in ARF4 KO cells, with numerous ER chaperones now released into the medium (the ARF4 KO secretome). This is a well-done study that showcases the ability of ARF4 alone to sustain cellular life (quite a surprise to this reviewer). Yet, the characterization of the phenotypes is somewhat minimal and the conclusions would be more robustly supported by additional experiments. Specifically:

1. The authors completely ignore class III ARF6 and this paper would be much more comprehensive and informative if analysis of that ARF was also included (ARF6 has been seen at the Golgi and also mediates endosomal trafficking that intersects with the TGN).

In agreement with the reviewers' consensus in cross-commenting, we consider Arf6ko to be beyond the scope of this study.

Although the overall Golgi architecture seems to be largely conserved, it remains essential to test whether Golgi polarity is similarly maintained, and such data would significantly expand the significance of the reported findings

We have performed super-resolution microscopy of wild-type and Arf1ko Golgis for GM130 and TGN46 as cis- and trans-Golgi markers, respectively, showing that polarity is still intact for Arf1ko, the morphologically most affected knockout cell line. We plan to include the following Figure in the revised manuscript.

FIGURE

Golgi complexes were imaged by superresolution microscopy for GM130 (green) and TGN46 (red), and displayed as maximum intensity projections, or tomographic 2D slices. Scale bar, 3 μm.

Since there is a defect in retrieval of KDEL-proteins, it would be important to show the intracellular localization of the KDEL-R in the cells (especially in the ARF4 KO cells that don't retrieve KDEL-GFP) - is the receptor degraded, stuck in some specific place - knowing that would increase the impact of this study and provide a mechanistic explanation for the observed phenotype

We plan to perform immunoblot analysis for KDELR to test for changes in levels in Arf deletion cells, and immunofluorescence microscopy to analyze changes in KDELR localization.

The rescue experiments in Figure 6 are good as far as they go, but this experiment would be much more informative if in addition to the same class rescue, the other class ARFs (at least one!) were also characterized.

We will to do this experiment.

This is maybe a little too much to ask, but since the authors propose a mechanistic explanation for the ARF4 KO KDEL phenotype as being due to different effectors recruited by this ARF (in this case different COPI isotypes - this study would increase in impact by actually testing this mechanisms by assessing whether ARF4Q71L mutant preferentially bound any particular isotype of COPI or even try to do mass spec to identify relevant effectors for this extremely interesting ARF.

We also think that this additional analysis is beyond the scope of this study.

The Discussion is a very limited and would be more impactful by adding some discussion of organismal effects of ARF deletions (many are embryonic lethal while cells seems to live quite happily) or mutations (links to cancer come to mind here), as well as some mention of data from yeast ARF (what is and isn't essential in those cells). As is, the authors miss an opportunity to highlight the importance of their findings as they relate to current knowledge of ARFology.

We agree to add a discussion of information on embryonic lethality and disease.

Reviewer #2 (Significance (Required)):

This is an important paper for the ARF field and people interested in ARF signaling will be glad to read about the findings and perhaps also use the developed KO cell lines - this is a significant advancement. The impact would be even higher if some of the experiments suggested above were incorporated into the manuscript.

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

This paper describes the application of CRISPR/Cas9 to systematically delete from HeLa cells all four Arf genes, either singly or in combination. The authors find it is possible to generate a number of double deletions (notably one lacking both Class I Arfs), and a triple deletion lacking all but Arf4. The authors characterise the structure of the Golgi in these mutants as well as retention of ER residents. The work is a comprehensive study of an exceptionally high technical standard. There is excellent validation of the deletions, and then the application of a wide range of methods including immunofluorescence, electron microscopy and mass-spectrometry, all with careful and extensive quantitation. The finding that cells can survive without Class I Arfs is interesting and unexpected, as is the fact that Arf4 alone is sufficient. This work will provide an excellent platform for future studies on Arf protein function in human cells. There are of course many questions that arise from these findings, but given the scope and quality of the work they would seem better left for future publications. There is one experiment that could be added, and some additions needed to the text for clarity and minor adjustments to the figures (all listed below), but if these are addressed, this would be a high quality paper of wide audience to a cell biological audience.

**Specific comments:**

1) Have the authors tested the levels and/or localisation of the KDEL receptor in the various lines? This is not essential, but if it were easily done, it would add to the work on ER resident secretion.

We plan to perform immunoblot analysis for KDELR to test for changes in levels in Arf deletion cells, and immunofluorescence microscopy to analyze changes in KDELR localization.

2) The work is entirely done in HeLa cells. The authors should note that the situation might be different in other cells types and cell lines. For instance, the DepMap CRISPR database suggests that quite a lot of cell lines are strongly affected by loss of Arf1.

We agree to add a discussion on known effects in other tissues.

3) Figure 2. Please show single channels as grey scale, and only merge as RGB. This is easier to see, especially for the colour blind. Likewise, Figure 3D would be clearer in greyscale rather than green, and 6B better in grey than in red.

We will make these changes.

4) Figure 5C. A brief comment is needed as to why it might be that BiP and calreticulin are not so efficiently secreted when Arf5 is knocked out in addition to Arf4.

This was a mistake in labeling that lane and will be corrected. It should read "Arf3+5ko" not "Arf4+5ko. Thank you for pointing this out.

5) Discussion:

a) The authors should relate these studies to work in other species. For instance, in yeast reduction of Arf levels causes the Golgi to enlarge (PubMed ID 9487133).

We can discuss this.

1. b) Some more discussion is needed of the fact that Arfs may not all act in the same part of the Golgi, which could explain some of the differences observed between the various deletions.

We can add this point in the discussion.

Reviewer #3 (Significance (Required)):

The Arf GTPases have been studied extensively for over 30 years as major regulators of Golgi function. They are essential for the recruitment to Golgi membranes of both COPI and clathrin/AP-1 coats, as well as various other proteins that regulate Golgi function. In addition, they have been reported to have roles in viral replication, and even other cellular processes such as lipid droplet formation and mitochondrial division. In humans there are four Arfs, Arf1 and Arf3 (Class I Arfs), and Arf4 and Arf5 (Class II Arfs). All are present on the Golgi, but their precise individual roles have remained unclear. Attempts have been made to deplete individual Arfs using RNAi, but incomplete knockdowns have made the results hard to interpret.

**Referee Cross-commenting**

There is probably no need for a prolonged debate about this, but I agree that the importance of Arf4 is striking, but it reflects the nature of this work that CRISPR has finally allowed these sorts of questions to be addressed unequivocally. COPI is also involved in recycling of Golgi resident enzymes, and it may be that Arf1 acts in this role.

If the authors check levels of COPI by blotting, and measure the intensity over the Golgi by quantitative IMF, that will reveal whether stability or membrane association if affected without fractionation which is probably less reliable.

If they want to do some extra experiments, then it would be quite easy to check the levels of some Golgi enzymes, or look at lectin binding as a proxy for glycosylation enzyme levels.

Overall, I agree with the positive comments of Reviewers 1 and 2, and it good that we all recognise the quality and importance of the work. However, I feel that one or two of their requests go beyond the scope of a single publication, or would add rather little for a lot of additional work. It is of course easy to propose experiments that someone else has to do!

**[On] Reviewer 1:**

Point 4. I agree that it would be useful to perform a blot to determine if the levels of coatomer are effected in the various KO lines. I am not sure if Reviewer 1 is also proposing fractionation to determine cytosol vs membrane ratio, but if so, then this would be less useful as peripheral membrane proteins tend to fall off membranes during fractionation and so such analysis is generally questionable. A blot, and clarification of the way the COPI/GM130 ratio is determined, would answer the key points in a relatively straightforward way.

Point 5. I agree that the defect in retrieval of ER residents in Arf4-KO is striking, but it a clear effect even if the reviewer does not understand it themselves! It does not seem so surprising to me, given that Arf4 is likely to act on the early Golgi were such retrieval occurs from. However, the experiment suggested by myself and Reviewer 32 of checking the levels and localisation of the KDEL-receptor would seem to me a good first step to addressing possible mechanism, and certainly sufficient for an initial publication.

Point 7. I am not sure that it has been unequivocally established that Arf1 is important in retrograde traffic. The reality is that many labs have taken Arf1 as being representative of all others and so concentrated biochemical and in vivo studies on this protein. This paper is really important as it highlights the need to investigate both Class I and Class II Arfs, and to bear in mind that their roles in vivo may well be more distinct than their in vitro properties would lead one to suspect. Perhaps, the simplest explanation for this is that the GEFs that activate them have a strong preference for one or the other.

Follow up Comment 1. I was not suggesting that the authors repeat all this in a cell line other than HeLa cells, as this is clearly impractical. HeLa cells are widely used, and so the findings are useful, and whilst it seems certain that some other cell lines would give different data (and indeed the DepMap data show this), then testing one other line would not change the conclusions much. All I wanted the authors to do is to clearly state in the text that what they see in HeLa cells may well be different in other cell lines. This does not detract from the fact that their HeLa cells will provide an excellent platform for focused studies on the role of individual Arfs.

Follow up Comment 2. I agree that Arf6 is not relevant to this paper (as discussed in detail below).

Follow up Comment 3. agree that a simple IMF experiment would suffice to check polarity and immuno-EM is technically very demanding and would add little in this context. The authors have already shown that the Golgi forms stacks in the KO cell lines, and I cannot see how this could occur without the stack being polarised - it has to form at one end and then mature to the other. In addition, after decades of working on the Golgi I have yet to see a credible report of a change to cells causing a loss of Golgi polarity, but maintaining a stacked structure. If the Golgi is not polarised it could not form a stack.

Follow up Comment 4. I agree that one month is perhaps too short to look at KDEL-R, COPI levels and checking polarity by IMF. As noted above, I am NOT suggesting that they repeat all this in a different cell line.

**[On] Reviewer 2.**

Point 1. I agree with Reviewer 1 that the authors are correct to ignore Arf6. It is a completely different GTPase with a distinct function in a different part of the cell. The family of Arf1-Arf5 arose in metazoans from a single Arf, but Arf6 had already split away from the Arf1-5 family in the last eukaryotic common ancestor, as Arf6 is present in plants and yeasts. There is overwhelming evidence that Arf1-Arf5 are partially redundant and this has hampered their study. Arf6 does not share these roles. The fact that it is acts on endosomes and has been reported to be on the Golgi (which is not widely agreed), is also true of many other GTPases. Indeed, other distant relatives of Arf1-5 are actually on the Golgi (Arl1, Arl5 etc), but these are also not relevant as like Arf6 they do not bind coat proteins and other major effectors of Arf1-5.

Point 2. As noted above, it is hard to see how polarity could be affected given that a Golgi stack is formed, but, at most, a simple application of IMF would seem sufficient to confirm this.

Point 3. Agreed.

Point 5. I agree with the reviewer that this is (much!) too much to ask for an initial publication. Various labs have already reported analysis of the effectors of Class II Arfs and they tend to overlap with Class I. Moreover, it is quite possible that the difference of role in vivo reflects differing interactions with regulators.

Point 6. Agreed.

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Referee #3

Evidence, reproducibility and clarity

This paper describes the application of CRISPR/Cas9 to systematically delete from HeLa cells all four Arf genes, either singly or in combination. The authors find it is possible to generate a number of double deletions (notably one lacking both Class I Arfs), and a triple deletion lacking all but Arf4. The authors characterise the structure of the Golgi in these mutants as well as retention of ER residents. The work is a comprehensive study of an exceptionally high technical standard. There is excellent validation of the deletions, and then the application of a wide range of methods including immunofluorescence, electron microscopy and mass-spectrometry, all with careful and extensive quantitation. The finding that cells can survive without Class I Arfs is interesting and unexpected, as is the fact that Arf4 alone is sufficient. This work will provide an excellent platform for future studies on Arf protein function in human cells. There are of course many questions that arise from these findings, but given the scope and quality of the work they would seem better left for future publications. There is one experiment that could be added, and some additions needed to the text for clarity and minor adjustments to the figures (all listed below), but if these are addressed, this would be a high quality paper of wide audience to a cell biological audience.

Specific comments:

1) Have the authors tested the levels and/or localisation of the KDEL receptor in the various lines? This is not essential, but if it were easily done, it would add to the work on ER resident secretion.

2) The work is entirely done in HeLa cells. The authors should note that the situation might be different in other cells types and cell lines. For instance, the DepMap CRISPR database suggests that quite a lot of cell lines are strongly affected by loss of Arf1.

3) Figure 2. Please show single channels as grey scale, and only merge as RGB. This is easier to see, especially for the colour blind. Likewise, Figure 3D would be clearer in greyscale rather than green, and 6B better in grey than in red.

4) Figure 5C. A brief comment is needed as to why it might be that BiP and calreticulin are not so efficiently secreted when Arf5 is knocked out in addition to Arf4.

5) Discussion:

a) The authors should relate these studies to work in other species. For instance, in yeast reduction of Arf levels causes the Golgi to enlarge (PubMed ID 9487133).

b) Some more discussion is needed of the fact that Arfs may not all act in the same part of the Golgi, which could explain some of the differences observed between the various deletions.

Significance

The Arf GTPases have been studied extensively for over 30 years as major regulators of Golgi function. They are essential for the recruitment to Golgi membranes of both COPI and clathrin/AP-1 coats, as well as various other proteins that regulate Golgi function. In addition, they have been reported to have roles in viral replication, and even other cellular processes such as lipid droplet formation and mitochondrial division. In humans there are four Arfs, Arf1 and Arf3 (Class I Arfs), and Arf4 and Arf5 (Class II Arfs). All are present on the Golgi, but their precise individual roles have remained unclear. Attempts have been made to deplete individual Arfs using RNAi, but incomplete knockdowns have made the results hard to interpret.

Referee Cross-commenting

There is probably no need for a prolonged debate about this, but I agree that the importance of Arf4 is striking, but it reflects the nature of this work that CRISPR has finally allowed these sorts of questions to be addressed unequivocally. COPI is also involved in recycling of Golgi resident enzymes, and it may be that Arf1 acts in this role.

If the authors check levels of COPI by blotting, and measure the intensity over the Golgi by quantitative IMF, that will reveal whether stability or membrane association if affected without fractionation which is probably less reliable.

If they want to do some extra experiments, then it would be quite easy to check the levels of some Golgi enzymes, or look at lectin binding as a proxy for glycosylation enzyme levels.

Overall, I agree with the positive comments of Reviewers 1 and 2, and it good that we all recognise the quality and importance of the work. However, I feel that one or two of their requests go beyond the scope of a single publication, or would add rather little for a lot of additional work. It is of course easy to propose experiments that someone else has to do!

Reviewer 1:

Point 4. I agree that it would be useful to perform a blot to determine if the levels of coatomer are effected in the various KO lines. I am not sure if Reviewer 1 is also proposing fractionation to determine cytosol vs membrane ratio, but if so, then this would be less useful as peripheral membrane proteins tend to fall off membranes during fractionation and so such analysis is generally questionable. A blot, and clarification of the way the COPI/GM130 ratio is determined, would answer the key points in a relatively straightforward way.

Point 5. I agree that the defect in retrieval of ER residents in Arf4-KO is striking, but it a clear effect even if the reviewer does not understand it themselves! It does not seem so surprising to me, given that Arf4 is likely to act on the early Golgi were such retrieval occurs from. However, the experiment suggested by myself and Reviewer 3 of checking the levels and localisation of the KDEL-receptor would seem to me a good first step to addressing possible mechanism, and certainly sufficient for an initial publication.

Point 7. I am not sure that it has been unequivocally established that Arf1 is important in retrograde traffic. The reality is that many labs have taken Arf1 as being representative of all others and so concentrated biochemical and in vivo studies on this protein. This paper is really important as it highlights the need to investigate both Class I and Class II Arfs, and to bear in mind that their roles in vivo may well be more distinct than their in vitro properties would lead one to suspect. Perhaps, the simplest explanation for this is that the GEFs that activate them have a strong preference for one or the other.

Follow up Comment 1. I was not suggesting that the authors repeat all this in a cell line other than HeLa cells, as this is clearly impractical. HeLa cells are widely used, and so the findings are useful, and whilst it seems certain that some other cell lines would give different data (and indeed the DepMap data show this), then testing one other line would not change the conclusions much. All I wanted the authors to do is to clearly state in the text that what they see in HeLa cells may well be different in other cell lines. This does not detract from the fact that their HeLa cells will provide an excellent platform for focused studies on the role of individual Arfs.

Follow up Comment 2. I agree that Arf6 is not relevant to this paper (as discussed in detail below).

Follow up Comment 3. agree that a simple IMF experiment would suffice to check polarity and immuno-EM is technically very demanding and would add little in this context. The authors have already shown that the Golgi forms stacks in the KO cell lines, and I cannot see how this could occur without the stack being polarised - it has to form at one end and then mature to the other. In addition, after decades of working on the Golgi I have yet to see a credible report of a change to cells causing a loss of Golgi polarity, but maintaining a stacked structure. If the Golgi is not polarised it could not form a stack.

Follow up Comment 4. I agree that one month is perhaps too short to look at KDEL-R, COPI levels and checking polarity by IMF. As noted above, I am NOT suggesting that they repeat all this in a different cell line.

Reviewer 2.

Point 1. I agree with Reviewer 1 that the authors are correct to ignore Arf6. It is a completely different GTPase with a distinct function in a different part of the cell. The family of Arf1-Arf5 arose in metazoans from a single Arf, but Arf6 had already split away from the Arf1-5 family in the last eukaryotic common ancestor, as Arf6 is present in plants and yeasts. There is overwhelming evidence that Arf1-Arf5 are partially redundant and this has hampered their study. Arf6 does not share these roles. The fact that it is acts on endosomes and has been reported to be on the Golgi (which is not widely agreed), is also true of many other GTPases. Indeed, other distant relatives of Arf1-5 are actually on the Golgi (Arl1, Arl5 etc), but these are also not relevant as like Arf6 they do not bind coat proteins and other major effectors of Arf1-5.

Point 2. As noted above, it is hard to see how polarity could be affected given that a Golgi stack is formed, but, at most, a simple application of IMF would seem sufficient to confirm this.

Point 3. Agreed.

Point 5. I agree with the reviewer that this is (much!) too much to ask for an initial publication. Various labs have already reported analysis of the effectors of Class II Arfs and they tend to overlap with Class I. Moreover, it is quite possible that the difference of role in vivo reflects differing interactions with regulators.

Point 6. Agreed.

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Referee #2

Evidence, reproducibility and clarity

Pennauer uses HeLa cells and CRISPR/Cas9 to delete the 5 members of the class I and class II ARF family of small regulatory GTPases either individually or in combinations. The characterization of the KO cells is excellent and convincingly demonstrates that true KOs were generated. The quality of the data presented is high. Using the KO cells she documents minor alterations in Golgi architecture and the recruitment of vesicular coats in cells deleted of all ARFs except ARF4. In contrast, there is a significant lack of retention/recycling to the ER of KDEL-containing ER proteins in ARF4 KO cells, with numerous ER chaperones now released into the medium (the ARF4 KO secretome). This is a well-done study that showcases the ability of ARF4 alone to sustain cellular life (quite a surprise to this reviewer). Yet, the characterization of the phenotypes is somewhat minimal and the conclusions would be more robustly supported by additional experiments. Specifically:

1. The authors completely ignore class III ARF6 and this paper would be much more comprehensive and informative if analysis of that ARF was also included (ARF6 has been seen at the Golgi and also mediates endosomal trafficking that intersects with the TGN).
2. Although the overall Golgi architecture seems to be largely conserved, it remains essential to test whether Golgi polarity is similarly maintained, and such data would significantly expand the significance of the reported findings
3. Since there is a defect in retrieval of KDEL-proteins, it would be important to show the intracellular localization of the KDEL-R in the cells (especially in the ARF4 KO cells that don't retrieve KDEL-GFP) - is the receptor degraded, stuck in some specific place - knowing that would increase the impact of this study and provide a mechanistic explanation for the observed phenotype
4. The rescue experiments in Figure 6 are good as far as they go, but this experiment would be much more informative if in addition to the same class rescue, the other class ARFs (at least one!) were also characterized.
5. This is maybe a little too much to ask, but since the authors propose a mechanistic explanation for the ARF4 KO KDEL phenotype as being due to different effectors recruited by this ARF (in this case different COPI isotypes - this study would increase in impact by actually testing this mechanisms by assessing whether ARF4Q71L mutant preferentially bound any particular isotype of COPI or even try to do mass spec to identify relevant effectors for this extremely interesting ARF.
6. The Discussion is a very limited and would be more impactful by adding some discussion of organismal effects of ARF deletions (many are embryonic lethal while cells seems to live quite happily) or mutations (links to cancer come to mind here), as well as some mention of data from yeast ARF (what is and isn't essential in those cells). As is, the authors miss an opportunity to highlight the importance of their findings as they relate to current knowledge of ARFology.

Significance

This is an important paper for the ARF field and people interested in ARF signaling will be glad to read about the findings and perhaps also use the developed KO cell lines - this is a significant advancement. The impact would be even higher if some of the experiments suggested above were incorporated into the manuscript.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Pennauer et al is the first to systematically investigate the role of class I&II Arfs using a knockout approach. It builds on earlier work by the Kahn lab who used an RNAi approach (Volpicelli-Daley et al. 2005) and is complementary to the overexpression approach used by the Hauri lab (Ben-Tekaya et al, 2010). The work is elegant and the data are strong. I am strongly in favor of publishing this work and my comments are technical in nature (2-5) and a request for some text changes (1). have the following comments for improvements:

1- When it comes to evaluating the role of depletions of Arfs on cell fitness, it would be better to use a non-transformed cell line. I am not asking the authors to go through the painstaking process of generating knockout cell lines in RPE1 cells for instance. Rather, I suggest that the authors make the reader aware that conclusions about cell survival have to be taken with care due to the use of a transformed cell line.

2- Why do Arf1 and Arf4 ko cells grow more slowly. Is it a higher rate of cell death? Is it a block in a certain phase of the cell cycle. Given the link of the Golgi to G2-M entry, I think that an analysis of the cell cycle distribution would add more depth to these data. If the cell cycle distribution is unaffected, then I would conclude that that the difference in doubling time are due to reduced cell survival. If there is an effect on the cell cycle distribution, then the conclusion of the authors is safe that no single Arf is required for survival

3- It is not clear to me how many cells were quantified in Figure 2D-F. I suppose that each do represents a cell. In this case, the number of cells quantified is a bit low. Such a quantification of fluorescence intensities in two channels in the same region is a simple task and I think it should be no problem obtaining at least 100 cells per condition.

4- Is the drop in the ratio of beta-COP/GM130 in Arf1 depleted cells reflecting reduced recruitment to the Golgi? Because the Golgi is bigger, it might be reflecting a reduced density in the number of coatomer molecules per surface area. If it is due to reduced recruitment, then the ratio of membrane/cytosolic betaCOP should be altered. This of course requires to show that the knockout does not affect total levels of coatomer. I think that such fractionation experiments would be a valuable addition to the manuscript and increase the depth of the data.

5- The finding that Arf4-ko cells exhibit a defect on retrieval of ER-resident proteins is exciting, and in my opinion, it is the most significant finding in this manuscript. How can this be reconciled with the lack of an ARf4 ko effect on coatomer recruitment to the Golgi. Looking carefully at the data, I see that in 2 out of 3 experiments, Arf4 ko reduced the betaCOP/GM130 ratio. This is why I think it is crucial to perform more experiments and add more cells to increase the confidence in the data. Reduced retrieval of ER chaperones is frequently found in tumors and we still don't understand the reason behind this. Therefore, this finding is of significance beyond the community of cell biologists.

6- I find Figure 6A confusing. Why do Arf1 overexpressing parental HeLa cells exhibit less Arf1 than control cells?

7- Why was the following condition not tested: Arf4ko cells with Arf1 overexpression. Given the importance of Arf1 in retrograde (Golgi-to-ER) trafficking, I would expect a partial rescue of the retrieval of ER chaperones.

Significance

Significance of the work:

The paper is important because it is the first to examine the role of Arfs using a knockout approach. Another very important finding is that Arf4 depleted cells exhibit problems with retrieval of ER chaperones. This is a very novel finding and to the best of my knowledge

Audience:

The primary audience is of course the community working on membrane trafficking, organelle biology and proteostasis. However, I think that the data on the role of Arf4 in retrieval of ER chaperones might be of relevance for cancer biologists. Secretion of ER chaperones is frequently found in many tumors and we still do not understand why this is happening and what the significance thereof is.

My own expertise:

Export from the endoplasmic reticulum Golgi fragmentation in cancer cell migration Rho GTPases Kinase signaling Pseudoenzymes Cell migration of breast cancer cells Proteostasis in multiple myeloma

Referee Cross-commenting

Just a follow-up comment from my side:

I agree that it has not been unequivocally established that Arf1 is the main/sole of retrograde transport. However, even less established is the role of Arf4 in this process. The authors show that it is mainly Arf1 depletion that reduces the amount of COPI at the Golgi (ratio of COPI/GM130). Thus, I remain very surprised that it is actually the Arf4 depletion that results in reduced retrieval.

What is the significance of having less COPI at the Golgi in Arf1-ko cells? Certainly, the Golgi is not more "leaky". Does the level of COPI at the Golgi not reflect the strength of retrograde trafficking? Maybe there is no less COPI at the Golgi, and it only appears to be less, because the Golgi is bigger. This is why a simple fractionation experiment would be good. Something like making a cytosol and a microsome fraction and looking at the ratio of COPI (Cyt/Mem).

If both reviewers think it is too much, or unlikely to work, then I am happy to drop this point.

Below are my comments to the evaluations by the other two reviewers:

1- I agree with most comments that the two other reviewers made. Some of them are actually overlapping with mine (e.g. the use of a cell line other than HeLa).

2- I am not sure whether the impact of the paper would improve by adding data on Arf6.

3- To the comment on Golgi polarity. Maybe we could be more specific here and say that it would be sufficient to show that a trans-Golgi protein and a cis-Golgi protein can be separated by fluorescence microscopy, or whether we alternatively want them to actually do it by immunogold labeling for EM (which is more difficult).

4- I agree with reviewer 2 that the work proposed needs 1-3 months. I think reviewer 3 is a bit too optimistic with 1 month, because her/his comment on using a cell line other than HeLa cannot be addressed in just a month.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): **Summary:** In this study authors investigated the role of NAMPT, NAD+ and PARP1/parthanatos in skin inflammation using a zebrafish psoriasis model with an hypomorphic mutation of spint1a and human organotypic 3D skin models of psoriasis. Authors showed that genetic deletion and/or pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases reduced oxidative stress, inflammation, keratinocyte DNA damage, hyperproliferation and cell death in zebrafish models of chronic skin inflammation. Authors also showed the expression of pathology-associated genes in human organotypic 3D skin models of psoriasis with pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases. The key finding of this study is that PARP1 hyperactivation caused by ROS-induced DNA damage mediates skin inflammation through parthanatos. **Major comments:** This is a very comprehensive study to investigate the role of PARP1 in skin inflammation. The main conclusion was made based on the genetic inhibition and/or pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases. Although the finding of this study that NAMPT-derived NAD+ fuels PARP1 to promote skin inflammation through parthanatos is interesting and important, there are lots of major concerns and questions, which have to be addressed to better support the main conclusion. In addition, the data and methods were not presented with sufficient detail.

1. This study is heavily relied on pharmacology inhibition. However, the specificity and selectivity of many inhibitors were not tested in this study.

At least 3 concentrations of each inhibitor were tested and the lowest one able to rescue the phenotype was then used for further testing (please, see Table S1). More importantly, the specificity of all compounds used were confirmed by genetic inhibition of their targets.

Fig. 1: it is quite confusing how NAD+ increases H2O2 levels? Is NAD+ cell permeable? It is not clear if NAD+ has been really up taken by cells in the larvae. If NAD+ fuels PARP1 to promote skin inflammation, why NAM treatment increased H2O2 levels but NMN precursor failed to increase skin oxidative stress? No reasonable explanation has been provided.

This is an interesting point. We have shown that exogenous NAD+ added in the water of larvae increased larval NAD+ (please, see Fig. 2K). It has been shown that neurons can take up NAD+ through CX43 (Fig. S7), so a similar mechanism may operate in larval skin. As regards, the effect of NAM and NMN, a recent study has demonstrated that NAM supplementation increased zebrafish larval NAD+; however, NA, NMN and NR failed to boost larval NAD+ level (PMID: 32197067). These results are consistent with our data.

Fig. 1E and 1G: it is not clear what is the green channel. Similarly, there is no clear description what is red or green in many other figures.

To help the interpretation of larval pictures, we have indicated in all figures what is analyzed in each fluorescent channel.

1. Fig. 1K and 1L: It is hard to understand why FK-866 reduced H2O2 release, but it increased neutrophils infiltration. How to interpret this conclusion?

Fig. 2C-D: Why low doses FK-866 reduced neutrophil infiltration whereas high dose FK-866 increased neutrophil infiltration?

Answer to 4&5: As it was explained in lines 145-156, FK-866 induces NF-kB activation in the muscle and neutrophil infiltration in this tissue when used at 100 uM. This result may be deleted if the reviewers think it is confusing, since a 10 uM dose was used in all subsequent experiments to study the impact of Nampt in skin inflammation. This dose has no effects in the muscle but robustly reduced skin H2O2 production and neutrophil skin infiltration.

Fig. 2I-J: it is not clear how NF-kB activity was measured. Is that based on green fluorescence shown in Fig. 2J? if so, the representative images were not consistent with the quantification data shown in I. Similarly, many other representative images were also not consistent with their quantification data throughout the manuscript. For example, Fig. 3C/D, 3E/F, 3G/H, 3L/M, Figure S2C/D, S2G/H, Fig. 4C/D, 4J/K.

The quantification of NFkB was measured in the skin, as it has already been reported previously (Candel et al., 2014). This is indicated in M&M section. The images show the whole larvae and NFkB is expressed at high levels in different tissues, such as neuromasts. To clarify this, we have included an additional figure to explain the ROI used for quantification of H2O2 and NfkB (Fig. S1G).

Figure S1C, Nampta/Namptb protein expression should be checked and shown after its KO using crispr/cas9 technique.

Unfortunately, we have used to different antibodies and both failed to crossreact with zebrafish Nampta/b. However, we have included the efficiency of CRISPR-Cas9 in Fig. S1F of the revised version. The efficiency is relatively low, probably indicating that is indispensable for zebrafish development, as occurs in mice (PMID 28333140).

Fig. 3I: protein expression of nox1, nox4 and nox 5 should be checked after genetic inhibition using CRISPR/Cas9 technique.

Unfortunately, we do not have antibodies able to recognize zebrafish Nox1, Nox4 and Nox5. However, we have provided the efficiency of the gRNA used for each gene (Fig. S3) and it is about 65%.

Fig. 4: If Olaparib treatment increased DNA damage, will it increase PARP1 activation and PAR formation?

As it has widely used in mammalian models, parthanatos is triggered by overactivation of PARP1 following DNA damage. Therefore, although inhibition of olaparib may further induces DNA damage, it blocks parthanatos. This is consistent with our results showing that olaparib reduces PARylation (Fig. S4H) and cell death (Figs. 4J, 4K).

Fig. 4M: it is not clear what staining has been done. No difference was observed among different groups.

As indicated in the figure legends, pγH2Ax+ (green) keratinocytes (red) are shown. We have indicated this in the figure and include arrows to show pγH2Ax+ cells. The quantitation of this experiment (Fig. 4L) show that FK-866 robustly reduced, while olaparib increases, keratinocyte DNA damage.

Authors used N-phenylmaleimide (NP) to block AIF nuclear translocation. How does this inhibitor work? what is its actual effect on AIF nuclear translocation? Experiments are required to show this inhibitor actually blocks AIF nuclear translocation.

NP has been shown to block AIFM1 nuclear translocation, since it inhibits cysteine proteases which are required for its cleavage which precedes nuclear translocation (PMID 8879205). Although we have shown that genetic inhibition of Aifm1 rescues skin inflammation, confirming the specificity of the inhibitor, we agree on this point. Therefore, we have performed additional experiments and showed nuclear Aifm1 in keratinocyte aggregates of Spint1-deficient larvae and that NP treatment blocked nuclear translocation (Fig. S6C). In addition, we have also shown increased nuclear translocation of AIFM1 in keratinocytes of lesional skin from psoriasis patients (Figs. 6C, 6D).

Figure S4: it is hard to understand why lane #2 with Olaparib has the highest PAR signal.

We are sorry for this mistake labeling the WB. The right legend is: 1 +/+, 2 -/- treated with DMSO, 3 -/- treated with FK-866 and 4 -/- treated with olaparib.

Does spint1a-/- zebrafish show parthanatos cell death? It is not clear how cell death was measured.

We have shown that skin keratinocytes from Spint1a-deficient fish show increased cell death, as assayed by TUNEL, that is fully reversed by olaparib (Figs. 4J, 4K). In addition, skin keratinocytes from the mutant fish also have increased PARylation that is reversed by either FK-866 or olaparib (Fig. S4G, S4H). Further, pharmacological and genetic inhibition of Aifm1 inhibition and forced expression of Parga also rescue skin inflammation. Finally, we have included new experiments showing Aifm1 nuclear translocation in both Spint1a-deficient larvae and psoriasis patient lesional skin. Therefore, all these results show that Spint1a-deficient fish show parthanatos cell death-induced inflammation.

NAD+ levels were regulated by 3 different pathways. Expression of many genes involved in these 3 pathways were altered in psoriasis. However, it is not clear if the other two pathways play a role in PARP1-mediated inflammation.

NAD+ salvage pathway has been shown to be the major pathway regulating NAD+ levels in most tissues. The inhibition of this pathway with FK-866 rescues all skin phenotypes observed in Spint1a-deficient larvae as well as in organotypic 3D skin models of psoriasis. These results were further validated using another inhibitor (GMX1778) and genetic inhibition. Therefore, our results support that the salvage pathway is the one involved in psoriasis and inhibition of this pathway would rescue inflammation. However, it will be worthy to investigate if other pathways play a role in psoriasis and specifically upon inhibition of the salvage pathway.

**Minor comments:**

1. Page 9: To test this hypothesis, we used N-phenylmaleimide (NP), a chemical inhibitor of Aifm1 translocation from the nucleus to the mitochondria (Susin et al., 1996). The statement is not correct.

We are sorry for this mistake. It has been amended to: “To test this hypothesis, we used N-phenylmaleimide (NP), a chemical inhibitor of Aifm1 translocation from the mitochondria to the nucleus (Susin et al., 1996).”

Page 12: To the best of our knowledge, this is the first study demonstrating the existence of parthanatos in vivo. This statement is not correct.

We have removed this statement.

Figure S3 and S6E: they should be presented in an easy understandable way for the general readers.

We have explained in the legends the graph output of TIDE analysis.

Figure legends should be presented in a clearer way.

We have tried our best writing the legends. All suggestions and request were made.

Reviewer #1 (Significance (Required)): Parthanatos is a new type of cell death distinct from apoptosis, necrosis, necroptosis and plays a pivotal role in ischemic stroke and neurodegenerative diseases (Wang Y et a., Science. 2016; Kam TI et al., Science 2018). The current study may provide new evidence of the importance of PARP1 and parthanatos in skin inflammation and potential targets for the treatment of skin inflammation. We thank the reviewer’s opinion on the significance of our study.

The reviewer has the expertise in oxidative stress, PARP1 and parthanatos research. Reviewer #2 (Evidence, reproducibility and clarity (Required)): **Summary:** The manuscript entitle "NAMPT-derived NAD+ fuels PARP1 to promote skin inflammation through parthanatos" is well written, divided and organized. This work demonstrated that models of psoriasis are characterized by ROS stress, inflammation and cell death. It was clear that NAMPT, a rate-limiting enzyme of NAD salvage pathway, and PARP1, a Poly-ADP-ribose polymerase, could be targeted to decrease ROS stress and inflammation that are contributing to cell death through parthanatos pathway. However, it was not clear that NAD+ are the responsible for fuel these processes in the psoriasis models analyzed. Nevertheless, the present work demonstrated that the cell death observed in the psoriasis model analyzed was correlated to an unidentified programmed cell death pathway, parthanatos that up to date has not been demonstrated.

We are pleased with the reviewer’s comments on our study.

**Major comments:** Most of the data showed confirmed that inhibition of NAMPT or PARP1 seems to be beneficial for the relief of some characteristics related to oxidative stress and inflammation in the skin. However, the author should show data about NAD+ levels only instead of the ratio NAD+/NADH to state that NAMPT-derived NAD+ is promoting oxidative stress (line 366-368) (fig2K).

The data shown in Fig 2K are NAD+ plus NADH. Considering that cytosolic and nuclear NAD+/NADH ratio typically ranges from 100 to 1000 (PMID: 21982715), these data mainly show intracellular NAD+ concentration in larvae.

Some data images are not convincing, or they don't really show an increase or decrease as the author showed in graph data. (Fig1D, 1E - 1F,1G).

The quantification of H2O2 and NFkB was measured in the skin, as it has already been reported previously (Candel et al., 2014). To clarify this, we have shown the ROI used for quantification of H2O2 and NfkB in Fig. S1G.

What is the relevance to analyze muscle and what is the relevance of the results obtained, since the effect of FK-866 in muscle increases the NFKB activity?

This is essentially a similar concern raised by reviewer 1. FK-866 induces NF-kB activation in the muscle and neutrophil infiltration in this tissue when used at 100 uM. This result may be deleted if the reviewers think it is confusing, since a 10 uM dose was used in all subsequent experiments to study the impact of Nampt in skin inflammation. This dose has no effects in the muscle but robustly reduced skin H2O2 production and neutrophil infiltration.

Figure S4H is not convincing with what the author wrote.

We are sorry for this mistake labeling the WB. The right legend is: 1 +/+, 2 -/- treated with DMSO, 3 -/- treated with FK-866 and 4 -/- treated with olaparib. Both FK-866 and olaparib rescue PARylation in the skin of Spint1a-deficient larvae.

The author should make the keratinocyte aggregation experiment with FK-866 treatment to better substantiate what they are proposing.

These results are shown in Figs. 2E and 2F.

**Minor comments:** Line 281: "NP, a chemical inhibitor of Aifm1 translocation from the nucleus to the mitochondria..." should be the opposite: NP, a chemical inhibitor of Aifm1 translocation from mitochondria to nucleus.

We are sorry for this mistake. It has been amended.

Line 299 "figure 6A" should be Figure 6B.

We have checked and it is correct.

How the author explains the relationship between all the results being related to NAMPT and supposedly to NAD+, but an important precursor to make NAD through salvage pathway (NMN) and a well NAD+ booster didn't show any effect?

This is an interesting point that was also raised by reviewer 1. A recent study has demonstrated that NAM supplementation increased zebrafish larval NAD+; however, NA, NMN and NR failed to boost larval NAD+ level (PMID: 32197067). This explains our results. We have discussed this point in the revised manuscript.

Line 178: should be NAMPT inhibitor stead of FK-866 inhibitor.

Thanks a lot. It has been amended.

Line 191-192: I suggest reformulating this sentence since the result showed was only the ratio NAD/NADH.

Please, see our response above. We are measuring NAD+ plus NADH. We have amended the text to clarify this fact.

Reviewer #2 (Significance (Required)): The present work greatly demonstrated the relevance of PARP1 and NAMPT in the field of inflammation and ROS in the skin that contribute to diseases like psoriasis. Although it is not a lethal disease, as the author mentioned, it affects the physical and mental health of the individual. Understanding the mechanism that underlie this condition would help to trigger new and more efficient treatments. It was clear that the result showed a promising strategy in targeting NAMPT and PARP1. Furthermore, inhibitor for them is already know and may be useful for future treatment of psoriasis disease. We thank this comments on the impact of our study.

Reviewer #3 (Evidence, reproducibility and clarity (Required)): This study shows NAMPT derived NAD facilitates PARP activation to promote skin inflammation via parthanatos. The authors used the zebrafish model and organoid models of psoriasis and observed that inhibition of NAMPT reduces inflammation in zebrafish and human skin organoid models. They also observed that NADPH oxidase-derived oxidative stress activates PARP, and PARP inhibition or over-expression of PARG or AIF mimics protection mediated by NAMPT inhibition. This is an interesting study, but there are several weaknesses to support the conclusions of this study. While pharmacological inhibition is a powerful tool, complementary methods (knock out of PARP-1) are critical for this paper's conclusions. PARP inhibitor used in this study may not specifically inhibit PARP1 but other PARPs too. Therefore, genetic knockout of PARP will make the make this conclusions/interpretation of this study strong.

We thank these comments on our manuscript. All pharmacological inhibitions used in this study were confirmed by genetic experiments, including Parp1. The genetic inhibition of Parp1 is shown in Figs. S4C-S4F.

Additional comments include: This study's primary focus is PARP activation and PAR-mediated parthanatos, but it is not shown how different inhibitors used in this study and supplementations of NAD alter PARP activation and PAR formation.

We have shown through the quantitation of PARylation that Spint1a-deficient skin shows increased PAR activity and that pharmacological inhibition of either Nampt or Parp was able to fully reverse it (Figs S4g & S4H). In addition, we have also shown a dramatically increased PAR activity in lesional skin biopsies from psoriasis patients (Fig. 6E).

NAMPT is not the only NAD biosynthesis pathway; how other NAD pathways respond when NAMPT is inhibited with FK-866.

NAD+ salvage pathway has been shown to be the major pathway regulating NAD+ levels in most tissues. The inhibition of this pathway with FK-866 rescues all skin phenotypes observed in Spint1a-deficient larvae as well as in organotypic 3D skin models of psoriasis. Therefore, our results support that the salvage pathway is the one involved in psoriasis and inhibition of this pathway would rescue inflammation. However, we agree that it will be worthy to investigate if other pathways play a role in psoriasis and specifically upon inhibition of the salvage pathway. However, this is out of the scope of this manuscript.

PARG is used in this study, but the protein levels of PARG are not shown, and it is not clear whether the PARG overexpression is sufficient to reduce PAR levels in the models used. AIF pharmacological and genetic manipulation of AIF is used, but it is not shown that AIF translocates to the nucleus in this model.

We agree on these points, so we have analyzed Aifm1 translocation in Spint1a-deficiet larvae and psoriasis patient lesional skin (please, see above our response to reviewer 1) and PARylation upon forced expression of Parga (Fig. 5M).

Does NAMPT inhibition reduce NAPD oxidase activity?

Our results indicate that Nampt inhibition reduce NAPDH oxidase activity, since a drastic reduction of H2O2 production was observed in the skin of Spint1a-deficient larvae treated with FK-866.

PAR plots provided in fig S4 need quantification, and the blots (Fig S4 G&H) should be run on the same gel to make sure the exposure levels are the same. It is not clear which group is represented in lane 4 of Fig S4 G.

We have provided the quantitation. The problem is that we mislabeled the legend of Fig. S4H. The right legend is: 1 +/+, 2 -/- treated with DMSO, 3 -/- treated with FK-866 and 4 -/- treated with olaparib. Therefore, either Nampt or Parp inhibition robustly reduces PARylation of Spint1a-deficient skin to the levels of their wild type counterparts.

Reviewer #3 (Significance (Required)): This study in interesting potentially showing the role of PARP-1 activation and Parthanatos in skin inflammation. It could be very significant if above identified weaknesses are addressed.

We are pleased with this reviewer’s assessment on the significance of our study.

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Referee #3

Evidence, reproducibility and clarity

This study shows NAMPT derived NAD facilitates PARP activation to promote skin inflammation via parthanatos. The authors used the zebrafish model and organoid models of psoriasis and observed that inhibition of NAMPT reduces inflammation in zebrafish and human skin organoid models. They also observed that NADPH oxidase-derived oxidative stress activates PARP, and PARP inhibition or over-expression of PARG or AIF mimics protection mediated by NAMPT inhibition. This is an interesting study, but there are several weaknesses to support the conclusions of this study. While pharmacological inhibition is a powerful tool, complementary methods (knock out of PARP-1) are critical for this paper's conclusions. PARP inhibitor used in this study may not specifically inhibit PARP1 but other PARPs too. Therefore, genetic knockout of PARP will make the make this conclusions/interpretation of this study strong.

Additional comments include:

This study's primary focus is PARP activation and PAR-mediated parthanatos, but it is not shown how different inhibitors used in this study and supplementations of NAD alter PARP activation and PAR formation. NAMPT is not the only NAD biosynthesis pathway; how other NAD pathways respond when NAMPT is inhibited with FK-866 PARG is used in this study, but the protein levels of PARG are not shown, and it is not clear whether the PARG overexpression is sufficient to reduce PAR levels in the models used. AIF pharmacological and genetic manipulation of AIF is used, but it is not shown that AIF translocates to the nucleus in this model. Does NAMPT inhibition reduce NAPD oxidase activity? PAR plots provided in fig S4 need quantification, and the blots (Fig S4 G&H) should be run on the same gel to make sure the exposure levels are the same. It is not clear which group is represented in lane 4 of Fig S4 G.

Significance

This study in interesting potentially showing the role of PARP-1 activation and Parthanatos in skin inflammation. It could be very significant if above identified weaknesses are addressed.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The manuscript entitle "NAMPT-derived NAD+ fuels PARP1 to promote skin inflammation through parthanatos" is well written, divided and organized. This work demonstrated that models of psoriasis are characterized by ROS stress, inflammation and cell death. It was clear that NAMPT, a rate-limiting enzyme of NAD salvage pathway, and PARP1, a Poly-ADP-ribose polymerase, could be targeted to decrease ROS stress and inflammation that are contributing to cell death through parthanatos pathway. However, it was not clear that NAD+ are the responsible for fuel these processes in the psoriasis models analyzed. Nevertheless, the present work demonstrated that the cell death observed in the psoriasis model analyzed was correlated to an unidentified programmed cell death pathway, parthanatos that up to date has not been demonstrated.

Major comments:

Most of the data showed confirmed that inhibition of NAMPT or PARP1 seems to be beneficial for the relief of some characteristics related to oxidative stress and inflammation in the skin. However, the author should show data about NAD+ levels only instead of the ratio NAD+/NADH to state that NAMPT-derived NAD+ is promoting oxidative stress (line 366-368) (fig2K). Some data images are not convincing, or they don't really show an increase or decrease as the author showed in graph data. (Fig1D, 1E - 1F,1G). What is the relevance to analyze muscle and what is the relevance of the results obtained, since the effect of FK-866 in muscle increases the NFKB activity?<br> Figure S4H is not convincing with what the author wrote. The author should make the keratinocyte aggregation experiment with FK-866 treatment to better substantiate what they are proposing.

Minor comments:

Line 281: "NP, a chemical inhibitor of Aifm1 translocation from the nucleus to the mitochondria..." should be the opposite: NP, a chemical inhibitor of Aifm1 translocation from mitochondria to nucleus. Line 299 "figure 6A" should be Figure 6B. How the author explains the relationship between all the results being related to NAMPT and supposedly to NAD+, but an important precursor to make NAD through salvage pathway (NMN) and a well NAD+ booster didn't show any effect? Line 178: should be NAMPT inhibitor stead of FK-866 inhibitor. Line 191-192: I suggest reformulating this sentence since the result showed was only the ratio NAD/NADH.

Significance

The present work greatly demonstrated the relevance of PARP1 and NAMPT in the field of inflammation and ROS in the skin that contribute to diseases like psoriasis. Although it is not a lethal disease, as the author mentioned, it affects the physical and mental health of the individual. Understanding the mechanism that underlie this condition would help to trigger new and more efficient treatments. It was clear that the result showed a promising strategy in targeting NAMPT and PARP1. Furthermore, inhibitor for them is already know and may be useful for future treatment of psoriasis disease.

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

Summary:

In this study authors investigated the role of NAMPT, NAD+ and PARP1/parthanatos in skin inflammation using a zebrafish psoriasis model with an hypomorphic mutation of spint1a and human organotypic 3D skin models of psoriasis. Authors showed that genetic deletion and/or pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases reduced oxidative stress, inflammation, keratinocyte DNA damage, hyperproliferation and cell death in zebrafish models of chronic skin inflammation. Authors also showed the expression of pathology-associated genes in human organotypic 3D skin models of psoriasis with pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases. The key finding of this study is that PARP1 hyperactivation caused by ROS-induced DNA damage mediates skin inflammation through parthanatos.

Major comments:

This is a very comprehensive study to investigate the role of PARP1 in skin inflammation. The main conclusion was made based on the genetic inhibition and/or pharmacological inhibition of Nampt/PARP1/AIFM1/NADPH oxidases. Although the finding of this study that NAMPT-derived NAD+ fuels PARP1 to promote skin inflammation through parthanatos is interesting and important, there are lots of major concerns and questions, which have to be addressed to better support the main conclusion. In addition, the data and methods were not presented with sufficient detail.

1. This study is heavily relied on pharmacology inhibition. However, the specificity and selectivity of many inhibitors were not tested in this study.
2. Fig. 1: it is quite confusing how NAD+ increases H2O2 levels? Is NAD+ cell permeable? It is not clear if NAD+ has been really up taken by cells in the larvae. If NAD+ fuels PARP1 to promote skin inflammation, why NAM treatment increased H2O2 levels but NMN precursor failed to increase skin oxidative stress? No reasonable explanation has been provided.
3. Fig. 1E and 1G: it is not clear what is the green channel. Similarly, there is no clear description what is red or green in many other figures.
4. Fig. 1K and 1L: It is hard to understand why FK-866 reduced H2O2 release, but it increased neutrophils infiltration. How to interpret this conclusion?
5. Fig. 2C-D: Why low doses FK-866 reduced neutrophil infiltration whereas high dose FK-866 increased neutrophil infiltration?
6. Fig. 2I-J: it is not clear how NF-kB activity was measured. Is that based on green fluorescence shown in Fig. 2J? if so, the representative images were not consistent with the quantification data shown in I. Similarly, many other representative images were also not consistent with their quantification data throughout the manuscript. For example, Fig. 3C/D, 3E/F, 3G/H, 3L/M, Figure S2C/D, S2G/H, Fig. 4C/D, 4J/K.
7. Figure S1C, Nampta/Namptb protein expression should be checked and shown after its KO using crispr/cas9 technique.
8. Fig. 3I: protein expression of nox1, nox4 and nox 5 should be checked after genetic inhibition using CRISPR/Cas9 technique.
9. Fig. 4: If Olaparib treatment increased DNA damage, will it increase PARP1 activation and PAR formation?
10. Fig. 4M: it is not clear what staining has been done. No difference was observed among different groups.
11. Authors used N-phenylmaleimide (NP) to block AIF nuclear translocation. How does this inhibitor work? what is its actual effect on AIF nuclear translocation? Experiments are required to show this inhibitor actually blocks AIF nuclear translocation.
12. Figure S4: it is hard to understand why lane #2 with Olaparib has the highest PAR signal.
13. Does spint1a-/- zebrafish show parthanatos cell death? It is not clear how cell death was measured.
14. NAD+ levels were regulated by 3 different pathways. Expression of many genes involved in these 3 pathways were altered in psoriasis. However, it is not clear if the other two pathways play a role in PARP1-mediated inflammation.

Minor comments:

1. Page 9: To test this hypothesis, we used N-phenylmaleimide (NP), a chemical inhibitor of Aifm1 translocation from the nucleus to the mitochondria (Susin et al., 1996). The statement is not correct.
2. Page 12: To the best of our knowledge, this is the first study demonstrating the existence of parthanatos in vivo. This statement is not correct.
3. Figure S3 and S6E: they should be presented in an easy understandable way for the general readers.
4. Figure legends should be presented in a clearer way.

Significance

Parthanatos is a new type of cell death distinct from apoptosis, necrosis, necroptosis and plays a pivotal role in ischemic stroke and neurodegenerative diseases (Wang Y et a., Science. 2016; Kam TI et al., Science 2018). The current study may provide new evidence of the importance of PARP1 and parthanatos in skin inflammation and potential targets for the treatment of skin inflammation.

The reviewer has the expertise in oxidative stress, PARP1 and parthanatos research.

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Reply to the reviewers

We thank the reviewers for the positive assessment of our work and for the constructive comments that helped us to improve the quality of our manuscript. We have carefully considered each point and have addressed most by modifying the manuscript text to increase clarity of our work. Based on a suggestion by Reviewer 2 we have also included the results of a new experiment.

In addition to addressing all comments of the reviewers, we have expanded the part of the study analysing the functionality of Caulobacter’s DnaA Nt in the heterologous host E. coli. Furthermore, we have replaced our original set of fluorescence data by a new data set that has been acquired using optimized measurement parameters (bottom read and 100 for the detector gain - see Material and Methods for details), which have improved the signal-to-noise ratio and the overall quality of the fluorescence profiles. Importantly, these new data do not change, but rather strengthen, our conclusions.

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

Felletti et al provide compelling new evidence that a CDS element in the dnaA mRNA is required for nutrient dependent translationol control. This provides a mechanisms by which dnaA translation is shut off during carbon starvation, and is supported by a rather rigorous analysis of the mRNA performed both in vitro and in vivo. Overall it was a pleasure to read and the data are generally very compelling. My specific comments are below:

**Major Comments:**

While the authors rule out differences in charging of different ala-tRNAs as controlling the nutrient dependent repression in translation, the authors assume that this must be due to the nascent sequence. However, could it also be possible that all ala-tRNA isoacceptors have lower charging after C-starvation?

We thank the reviewer for raising this important point. As Reviewer 1 pointed out, we cannot conclusively exclude that carbon starvation could lead to reduced charging levels of all isoacceptor Ala-tRNAs. However, based on the available literature, we consider it unlikely. In a first work by Elf et al 2003 (confirmed later by Dittmar et al 2005 and Subramaniam et al 2014) the authors argued that under amino acid-limiting conditions the charging levels of the different isoacceptor tRNAs depend directly on their codon usage during translation. Importantly, in our work we could show that Nt mediates the inhibition of translation independent of the synonymous codon choice, suggesting that aa-tRNA levels are not limiting in our experimental conditions. To address this comment of Reviewer 1, we discussed this matter in a greater detail in the revised version of the manuscript (line 374-379).

**Minor comments:**

It was observed many years ago that tmRNA is required for the proper timing of DNA replication initiation in Caulobacter (Cheng and Keiler J Bact 2009). Since the AAI motif is appearing to alter translation elongation, it might be interesting to discuss the AAI motif may be linked to ribosome arrest and rescue.

We appreciate this suggestion. Cheng and Keiler 2009 proposed an indirect involvement of the tmRNA in the transcriptional regulation of DnaA over Caulobacter’s cell cycle. In the revised version of the manuscript, we mention the tmRNA and ArfB protein as possible factors involved in ribosome rescue following Nt-induced ribosome stalling and we refer to Keiler et al 2000 and Feaga et al 2014.

Line 49 - add "initiation"

The word “initiation” was added to the text.

Line 61 - is "cleared" meant to be proteolyzed or simply meaning to have a lower protein level?

We apologize if we were not clear. We rephrased the text as follows: “[…] DnaA levels decrease at the onset of carbon starvation […]”.

Line 92-93 - is this 5' UTR based on a previously defined TSS determined in their previous study?

dnaA TSS has been first determined by primer extension (Zweiger and Shapiro 1994) and later by global 5’RACE (Schrader et al 2014 and Zhou et al 2015). In the new version of the manuscript, we include references to these previous studies (line 94).

Line 115-118 - this is interesting, might this conserved 5' UTR be added to rfam?

We thank the reviewer for this suggestion. We will submit our alignment to rfam after publication of the manuscript in a journal.

Line 126-127, 131,189 - Is the 3nt sequence the authors found here considered a Shine-Dalgarno site? I would imagine that this would be too small to consider this. Perhaps calling it SD-like sequence might be more appropriate.

We agree with this comment. In the new version of the manuscript, we refer to the identified 3-nucleotide sequence as a “SD-like sequence”.

Lines 136-140, 208-210 - Would the authors consider this upstream site with a potential CUG start codon a standby site? It appears to fit many of the criteria which could be used to define one.

According to our probing data, the mRNA region in proximity of the CUG start codon forms a very stable stem-loop structure. Based on our previous experience (especially the extensive work by the Wagner lab), typical ribosome standby sites only occur in largely unstructured regions. Furthermore, in Supplementary Fig. 4 we show that the deletion of stem P4 does not affect eGFP expression levels. For these reasons, we consider it unlikely that the putative CUG start codon is part of a ribosome standby site.

Lines 253-255 - this is a beautiful experiment, but very hard to understand from the text. Perhaps add a sentence or two to explain it in more detail.

We thank the reviewer for this comment. In the revised version of the manuscript, we provide a more detailed description of the dfsNt reporter mutant. We hope this will address the reviewer’s concerns.

Line 307 - add "synonomous"

The word “synonymous” was added in the revised version of the manuscript

When dnaA is depleted, it was observed that the chromsome can be erroneously segregated by the ParA/B/S system (mera et al PNAS). Does this occur in C-starvation when DnaA levels drop?

In a separate study we have also observed that in a fraction of DnaA depleted cells the origin of replication is erroneously translocated from the stalked to the swarmer cell pole. We have not studied this phenomenon under carbon starvation, as it lies outside the scope of this paper. However, if the ParA/B/S remains functional under carbon starvation, this might also happen in G1-arrested starved cells.

Reviewer #1 (Significance (Required)):

Appears to be quite significant to researchers studying regulation of bacterial cell cycle and translation. Since DnaA is conserved across bacteria, and this mechanism works in E. coli, it appears that the findings will likely be important in many bacterial systems.

Referee Cross-commenting

All the reviewer comments I read seem reasonable. Specifically, I found the point about E. coli 30S ribosomes is very important that the authors address. This could be done in writing, but should be better listed as a caveat to those experiments.

As suggested by the reviewers, we have partially rephrased some parts of the text describing the toeprint results. Moreover, we have inserted in the main text and in Fig. 1 legend explicit references to the use of purified E. coli 30S subunits and tRNA-fMet. We believe these changes will address the reviewers’ concerns.

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

**Summary:** The Jonas lab provide good evidence that they have found a new mechanism to regulate the amount of the DnaA protein by a starvation signal. The DnaA protein is the key chromosome replication initiator probably for most bacteria and as such DnaA is the target of many regulatory inputs. The authors created an accurate reporter system that allows them to dissect the 5' mRNA translated and untranslated sequences of dnaA and they have convincingly demonstrated that the N-terminal DnaA peptide sequence and not the RNA mediate the response to starvation by glucose exhaustion. This is potentially a model example for global translational responses in bacteria.

**Major comments:**

The main conclusion, i.e. that the DnaA leader peptide "Nt" mediates this response is convincing. However, there were 2 major problems that should be easily addressed. These do not subtract from the main conclusion.

Problem 1

E. coli 30S subunits were used in the "Toeprint" assay of Fig. 1. Obviously Caulobacter 30S Ribosome subunits should have been used, or a justification should be given. One remedy would be to make this supplementary information.

We thank Reviewer 2 for this comment. We agree that it would be better to use Caulobacter 30S ribosome subunits in our toeprint experiments. However, because toeprint assays with E. coli 30S ribosome were already established in our lab (i.e. the Wagner lab, where the assays were performed) and because works by other groups have shown that E. coli 30S subunits can be used to study the translation of mRNAs from other bacteria, we decided to use this experimental set up. Based on our results, we also had no reason to doubt the suitability of the E. coli 30S subunits. The toeprint showed that translation starts at the in silico predicted translation start site, which was further confirmed by our in vivo mutagenesis experiments. For these reasons, we are confident that the toeprint assays indicate the true translational start site. However, we acknowledge that we could have been more explicit about the use of the purified E. coli 30S subunits and tRNA-fMet in toeprinting assay. To increase clarity and transparency, in this revised version of the manuscript, some parts of the main text were rephrased and references to the use of E. coli 30S and tRNA-fMet were introduced (including Fig. 1 legend). We hope that these changes will address the reviewer’s concerns.

Problem 2

The results in Fig. 6B could be due to the Nt simply making the hybrid protein more unstable in E. coli. This is the main impression given by the drop in signal. In this case, the conclusion would be wrong, and Nt is not transferring a starvation translation block from C. crescentus to E. coli. Nt is just making the protein unstable. These results should be treated as preliminary pending protein stability measurements. However, this defect does not subtract from the other main points and without the Fig. 6 E. coli experiments they still make a complete and interesting story. One remedy would be to make this also supplementary information.

It is indeed striking that a drop of normalised fluorescence is observed for the 5’UTRdnaA-Nt construct in E. coli but not in Caulobacter. In order to address if this behavior can be explained by reduced protein stability, we have performed a translation shut-off assay using the 5’UTRdnaA-Nt E. coli reporter construct. The results of this experiment (shown in Supplementary Fig. 9A and described in line 327-329) show that the normalised fluorescence remains stable over 10 hours after chloramphenicol addition to the culture, ruling out that the presence of Nt significantly affects eGFP protein stability in E. coli. Importantly, this experiment also showed that in contrast to the chloramphenicol treated culture, in which the OD600 decreased after reaching stationary phase, the OD600 of the non-treated cultures slightly increased between 2 and 10 hours (Supplementary Fig. 9A). Because this increase was not observed in carbon starved Caulobacter cultures, we consider the different growth dynamics between E. coli and Caulobacter to be the most likely explanation for differences in eGFP accumulation at later time points during the experiment.

To further strengthen our E. coli data, we have analysed additional relevant Nt mutants that we identified as most critical mutants in our Caulobacter experiments presented in Fig. 5, namely dfsNt, mutD1, mutD2, ΔAAI and AAI>DDK. Determination of Δt and Δf values for the E. coli strains carrying these different Nt constructs showed similar results as for the corresponding constructs in Caulobacter. Collectively, these new data further support the notion that Nt operates in E. coli through a conserved inhibitory mechanism of translation. These data are now included in a reorganized new version of Fig. 6 (panels A, B) as well as in Supplementary Fig. 9.

**Minor comments:**

There are also 6 minor issues that are easily addressed, most by small changes to the text, and these should improve this otherwise fine manuscript.

Issue 1

Line 88 Fig. 1A shows DnaA degradation upon entering stationary phase from a low glucose media and not a simple starvation response to one component like glucose. Did the authors consider trying simple washout experiments, i.e. resuspend the cells in glucose-free media? This would have the advantage of suddenly exposing the cells to starvation and thereby studying the sudden response rather than the slower lingering response which would be due to many factors and not just glucose removal.

In a previous work from our lab (Leslie et al 2015), we have conclusively shown that the downregulation of DnaA synthesis depends primarily on the nutrient content of the growth medium.

Besides being in continuity with our previous work, we think that the starvation protocol that we used in the present study, and that was also used by the Sean Crosson lab (Boutte et al. 2012), might better reproduce what happens in the natural environment when nutrient levels gradually decrease until becoming limiting for bacterial growth.

Issue 2

Reference 16 should be cited are the first publication to show that glucose and other starvations induce DnaA degradation in Caulobacter.

We have added Reference 16 to the first sentence of the results section, in which we state that DnaA levels decrease when cells are shifted from a glucose-supplemented minimal medium to a glucose-limiting medium.

Issue 3

Fig. 1D shows that the TOEprint is not changed by adding the ribosome, very surprising considering its size and SD docking & alignment. 2 Minor bands then appear when the tRNA-Met is further added. These are presumably the "toeprints". A control with just the added tRNA-Met would make this result much more significant.

In the existing literature, there is a common consensus to consider real toeprints (i.e., indicative of the presence of an assembled translation pre-initiation complex) as only those bands that appear faintly in the presence of the 30S ribosome subunit but that become clearly enhanced upon addition of the initiator tRNA-fMet. Some examples can be found in Hoekzema et al 2019, Romilly 2014, Romilly 2020. In cases when the translation start site is buried in a structural element, the intensity of the toeprint signal is further increased when the mRNA is rendered unfolded, as seen in our data.

tRNA-30S-independent bands always show up in toeprint experiments, but their intensities differ with the sequence of the mRNA and sometimes the choice of RT used for primer extension. Addition of initiator tRNA-fMet alone is commonly not done in toeprint experiments (see references mentioned above). Finally, we want to point out again (see also our answer on “Problem 1”) that the toeprint data are very much consistent with our in silico predictions and our in vivo mutagenesis data. Therefore, we are confident that the observed toeprint upstream of the AUG corresponds to the true ribosome binding site.

Issue 4

Why does the cell OD drop, e.g. in Fig. 2, is it cell death from starvation?

We don’t think that the slight reduction of OD600 observed in our experiments is due to cell death. Based on our knowledge, carbon starved cells remain viable up to 24 hours after the starvation onset. Instead, we have observed a cell volume reduction, which may at least partially explain the observed OD600 decrease.

Issue 5

Line 327 Discussion "This study reveals a new mechanism, by which some bacteria can regulate the synthesis of the replication initiator DnaA in response to nutrient availability by modulating the rate of translation." Rate of translation or rate of translation abortions (as implied in Fig. 6)?

The rate of translation is the result of multiple contributions such as initiation, elongation, abortion and termination. Our data indicate that Nt is a regulator of DnaA translation elongation responding specifically to the nutritional state of the cell. Translation abortion could be one of the possible outcomes (but not the only one) of ribosome stalling. For these reasons, in the new version of the manuscript, we added the word “elongation” at the end of the sentence mentioned by Reviewer 2 (line 354).

Issue 6

It seems that that for most experiments with the eGFP the translation and protein decay components of the signal could have been easily uncoupled by running a parallel +chloramphenicol control. For example, this would simplify the interpretation of Fig. 6 where Nt eGFP stabilities are an issue and it is important to establish that comparable protein stability with and without the Nt peptide.

To address the reviewer’s comment, we have now included a chloramphenicol control experiment (stability assay) performed with E. coli carrying the 5’UTRdnaA-Nt reporter construct (Supplementary Fig. 9A). Please, see the response above for more details. For the experiments with the Caulobacter 5’UTRdnaA-Nt reporter we show in Supplementary Fig. 7 that the Nt peptide has no destabilising effect on eGFP.

Reviewer #2 (Significance (Required)):

Caulobacter crescentus is a model bacterium that has provided many insights into bacterial physiology that are now exploited to understand many organisms. These present results may provide one such example. It is known that the first amino acids of translated peptides can influence increase or impede exit from the ribosome, so this is a potential translation-level regulatory point that might be used by many organisms. This manuscript gives a concrete and important example of such usage suggesting that it many be widespread. Therefore, this work should find a wide audience and it should stimulate research in many other systems.

My lab also studies Caulobacter crescentus and we studied the same dnaA gene and protein including starvation responses. We at present do not have projects on dnaA but we do study other regulators and regulatory mechanisms of chromosome replication in Caulobacter crescentus.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The Jonas lab provide good evidence that they have found a new mechanism to regulate the amount of the DnaA protein by a starvation signal. The DnaA protein is the key chromosome replication initiator probably for most bacteria and as such DnaA is the target of many regulatory inputs. The authors created an accurate reporter system that allows them to dissect the 5' mRNA translated and untranslated sequences of dnaA and they have convincingly demonstrated that the N-terminal DnaA peptide sequence and not the RNA mediate the response to starvation by glucose exhaustion. This is potentially a model example for global translational responses in bacteria.

Major comments:

The main conclusion, i.e. that the DnaA leader peptide "Nt" mediates this response is convincing. However, there were 2 major problems that should be easily addressed. These do not subtract from the main conclusion.

Problem 1

E. coli 30S subunits were used in the "Toeprint" assay of Fig. 1. Obviously Caulobacter 30S Ribosome subunits should have been used, or a justification should be given. One remedy would be to make this supplementary information.

Problem 2

The results in Fig. 6B could be due to the Nt simply making the hybrid protein more unstable in E. coli. This is the main impression given by the drop in signal. In this case, the conclusion would be wrong, and Nt is not transferring a starvation translation block from C. crescentus to E. coli. Nt is just making the protein unstable. These results should be treated as preliminary pending protein stability measurements. However, this defect does not subtract from the other main points and without the Fig. 6 E. coli experiments they still make a complete and interesting story. One remedy would be to make this also supplementary information.

Minor comments:

There are also 6 minor issues that are easily addressed, most by small changes to the text, and these should improve this otherwise fine manuscript.

Issue 1

Line 88 Fig. 1A shows DnaA degradation upon entering stationary phase from a low glucose media and not a simple starvation response to one component like glucose. Did the authors consider trying simple washout experiments, i.e. resuspend the cells in glucose-free media? This would have the advantage of suddenly exposing the cells to starvation and thereby studying the sudden response rather than the slower lingering response which would be due to many factors and not just glucose removal.

Issue 2

Reference 16 should be cited are the first publication to show that glucose and other starvations induce DnaA degradation in Caulobacter.

Issue 3

Fig. 1D shows that the TOEprint is not changed by adding the ribosome, very surprising considering its size and SD docking & alignment. 2 Minor bands then appear when the tRNA-Met is further added. These are presumably the "toeprints". A control with just the added tRNA-Met would make this result much more significant.

Issue 4

Why does the cell OD drop, e.g. in Fig. 2, is it cell death from starvation?

Issue 5

Line 327 Discussion "This study reveals a new mechanism, by which some bacteria can regulate the synthesis of the replication initiator DnaA in response to nutrient availability by modulating the rate of translation." Rate of translation or rate of translation abortions (as implied in Fig. 6)?

Issue 6

It seems that that for most experiments with the eGFP the translation and protein decay components of the signal could have been easily uncoupled by running a parallel +chloramphenicol control. For example, this would simplify the interpretation of Fig. 6 where Nt eGFP stabilities are an issue and it is important to establish that comparable protein stability with and without the Nt peptide.

Significance

Caulobacter crescentus is a model bacterium that has provided many insights into bacterial physiology that are now exploited to understand many organisms. These present results may provide one such example. It is known that the first amino acids of translated peptides can influence increase or impede exit from the ribosome, so this is a potential translation-level regulatory point that might be used by many organisms. This manuscript gives a concrete and important example of such usage suggesting that it many be widespread. Therefore, this work should find a wide audience and it should stimulate research in many other systems.

My lab also studies Caulobacter crescentus and we studied the same dnaA gene and protein including starvation responses. We at present do not have projects on dnaA but we do study other regulators and regulatory mechanisms of chromosome replication in Caulobacter crescentus.

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Referee #1

Evidence, reproducibility and clarity

Felletti et al provide compelling new evidence that a CDS element in the dnaA mRNA is required for nutrient dependent translationol control. This provides a mechanisms by which dnaA translation is shut off during carbon starvation, and is supported by a rather rigorous analysis of the mRNA performed both in vitro and in vivo. Overall it was a pleasure to read and the data are generally very compelling. My specific comments are below:

Major Comments:

While the authors rule out differences in charging of different ala-tRNAs as controlling the nutrient dependent repression in translation, the authors assume that this must be due to the nascent sequence. However, could it also be possible that all ala-tRNA isoacceptors have lower charging after C-starvation?

Minor comments:

It was observed many years ago that tmRNA is required for the proper timing of DNA replication initiation in Caulobacter (Cheng and Keiler J Bact 2009). Since the AAI motif is appearing to alter translation elongation, it might be interesting to discuss the AAI motif may be linked to ribosome arrest and rescue.

Line 49 - add "initiation"

Line 61 - is "cleared" meant to be proteolyzed or simply meaning to have a lower protein level?

Line 92-93 - is this 5' UTR based on a previously defined TSS determined in their previous study?

Line 115-118 - this is interesting, might this conserved 5' UTR be added to rfam?

Line 126-127, 131,189 - Is the 3nt sequence the authors found here considered a Shine-Dalgarno site? I would imagine that this would be too small to consider this. Perhaps calling it SD-like sequence might be more appropriate.

Lines 136-140, 208-210 - Would the authors consider this upstream site with a potential CUG start codon a standby site? It appears to fit many of the criteria which could be used to define one.

Lines 253-255 - this is a beautiful experiment, but very hard to understand from the text. Perhaps add a sentence or two to explain it in more detail.

Line 307 - add "synonomous"

When dnaA is depleted, it was observed that the chromsome can be erroneously segregated by the ParA/B/S system (mera et al PNAS). Does this occur in C-starvation when DnaA levels drop?

Significance

Appears to be quite significant to researchers studying regulation of bacterial cell cycle and translation. Since DnaA is conserved across bacteria, and this mechanism works in E. coli, it appears that the findings will likely be important in many bacterial systems.

Referee Cross-commenting

All the reviewer comments I read seem reasonable. Specifically, I found the point about E. coli 30S ribosomes is very important that the authors address. This could be done in writing, but should be better listed as a caveat to those experiments.

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Reply to the reviewers

The authors wish to thank all three Reviewers for their appreciative comments regarding our ECPT and for very useful suggestions. Response to all points raised are presented below, we hope that the responses and new experiments proposed in the following pages will fully address remaining concerns.

Reviewer’s comments to the BiorXiv paper by Chesnais et al, 2021

“High content Image Analysis to study phenotypic heterogeneity in endothelial cell monolayers”

https://www.biorxiv.org/content/10.1101/2020.11.17.362277v3

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

The authors highlight the importance of endothelial heterogeneity using endothelial cells from different tissues. They examined aortic and pulmonary endothelium as well as HUVECs. They cultured the cells in identical conditions and also stimulated them with a physiological concentration of vascular endothelial growth factor as well high concentrations as would be found in cancers. They developed a profiling tool that allowed analysis of individual endothelial cells within a monolayer and quantification of inter-endothelial junctions, Notch activation, proliferation and other features.

**Major comments**

1. It would be useful to apply this technology one step beyond two-dimensional culture, to use vessels opened up longitudinally so that one can see the monolayer of endothelial cells and assess whether it is relevant in primary material in situ. I think this would be a major utility of the whole approach.

R: We thank this reviewer for the suggestion. In vivo analysis is not in the objectives of the paper. However, we propose to perform “En face” staining of murine blood vessels following the protocol in the reference below. We will perform stainings for murine CDH5 (VE-Cadherin), NOTCH1 intracellular domain, HES1 and DNA which parallel that used in vitro on human EC. We will then apply our revised ECPT workflow and present data in a new Figure.

En Face Preparation of Mouse Blood Vessels. Ko KA, Fujiwara K, Krishnan S, Abe JI. J Vis Exp. 2017 May 19;(123):55460. doi: 10.3791/55460. PMID: 28570508

2. There are some very nice images here but disappointed not see a field that could show staining and markers for several of the target proteins and thus show the heterogeneity and randomness or organisation of the endothelial cells.

R: We thank the reviewer for the appreciative comment. We propose to include representative microphotographs to illustrate the heterogeneity of different EC monolayers in the revised version of the manuscript. Furthermore, to further illustrate these aspects we will also include spatial correlation maps of cells and features measured with ECPT as explained below.

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3.

• The Notch signalling is an important aspect of this work, particularly evidence of lateral inhibition would have been of value. For example, one might expect cells adjacent to each other to have alternating high and low NICD. R: We thank the reviewers for the suggestion. To address this, we are currently developing a new module to perform spatial autocorrelation analysis based on cell maps built using ECPT. In particular we have developed a new module to export cell maps as spatial objects in R which can be then analysed using the adespatial R package and provide correlation metrics such as the Moran’s autocorrelation index (see reference below). The index works with continuous data, removing the need to establish arbitrary thresholds and thus provides formal metrics to demonstrate heterogeneity in EC monolayers. We have derived this index as an example of such analysis for synthetic data and for one ECPT cell map as shown below.

Figure 1: Moran’s spatial autocorrelation analysis using R and adespatial package. Moran’s index has values between –1 and 1. If adjacent cells had a consistent tendency to acquire alternate high and low NICD values, the corresponding bivariate Moran’s index would have an I+ value ~ 0 and an I- value approaching -1. In the example cell map both I+ and I- have relatively small absolute values and large p values which suggest a random cell distribution. The analysis was performed on synthetic data and ECPT derived data (HUVEC at baseline).

• *

Community ecology in the age of multivariate multiscale spatial analysis

S Dray et al, Ecological Monographs, 2012. doi:10.1890/11-1183.1

• NICD staining alone does score the extent of the signalling because of many factors that can influence the transport of the cleaved NICD. Really a marker of Notch signalling downstream e.g. HES or HEY family, DLL4 fis needed to give more information about this critical aspect. R): We thank the reviewer for the suggestion. We are currently performing HES1 staining (with no Pha staining) along with a new NICD mAb (see below). Preliminary qualitative data (Fig 2) show that HES1 staining also reveals single cell heterogeneity of NOTCH activation in the same monolayer. We will include ECPT analysis of HES1 and correlation with NICD and other features as suggested. We will reformat the current Fig 5 to include HES1 analysis and improved metrics of NOTCH pathway activation including spatial analysis (point 3 above).

Figure 2: HES1 immunostaining on HUVEC (Image enhanced for visualisations). Cell nuclei labelled as 1, 2 and 3 have raw mean grey values of HES1 signal equal to 2271, 11210 and 48261 (C2/C1 and C3/C2 >4 folds).

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I really do not think that in Figure 5 it is justified to have a red line drawn through the cloud of points. The correlation coefficient is so low that this is meaningless. The failure to distinguish a P value from biological relevant is worrying. Much better comparison would have been between NICD staining and a downstream gene regulated by notch.

R: We appreciate the reviewer’s concerns and are presenting our analyses of NOTCH activation using new immunostainings (HES1) and robust metrics for NOTCH activation as discussed above. We will therefore remove the mentioned corelation plots from the reviewed version of the manuscript.

It is important to know that the antibodies used for staining have be validated by the investigators. They would need to show a single band on Western blots or be able to block staining on immunohistochemistry. We all know the manufacturers can be unreliable and use high concentrations of proteins for Western blots. These should be added as a supplementary figure.

R: While the paper was under revision the AB8925 (NICD, Abcam) has been retracted from the market. To address this major concern, we have decided to acquire a different antibody targeting the intracellular portion of NOTCH receptor and validated its specificity by western blot. Fig 3 below, show western blots demonstrating a clean band at ~98 Kd as expected for cleaved NOTCH1 intracellular domain (NICD).

We are currently repeating the whole experiment presented in the current version of the manuscript and the ECPT analysis using the new antibody and including HES1 one of the canonical NOTCH target genes as also suggested by this and other Reviewers. We will provide WB analysis of all antibodies used in the paper in a supplementary figure in the revised manuscript.

Figure 1, WB analysis (NOTCH1 intracellular domain, AB52627, Abcam). of HUVEC (lanes 2,3), HAoEC (lanes 4,5) and HPMEC (lanes 6,7)

Reviewer #1 (Significance (Required)):

This represents a valuable and thorough methodology likely to be highly useful to many groups and show new insights into endothelial biology.

Wide audience, cancer, cardiology, vascular disease-covid.

My expertise >100 papers on angiogenis in cancer, basic mechanism, therapy models, bioinformatics IHC, patients, clinical trial. H score 190 Google Scholar

R: We thank Reviewer One for their very appreciative comments and we hope that the proposed revisions will fully address remaining concerns.

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

The manuscript by Chesnais et al reports development of workflow for analysis of cultured endothelial cells , which they call Endothelial Cell Profiling tool (ECPT). Using ECPT they analyse several parameters in three different endothelial cell types (HuAEC, HUVEC and HPMEC), such as cell morphology, activation of cytoskeleton, VE-cadherin junctions, cell proliferation and Notch activation, under steady conditions and upon treatment with VEGF. The analysis allows to observe some predicted changes, such as increase in cell cycle and junctional activation in cells treated with VEGF-A, and such changes are highly heterogeneous. Overall, this is a potentially useful albeit not revolutionary tool for batch analysis of cultured endothelial cell phenotypes.

I have the following comments:

1. To make their case the authors should provide a comparison with other currently used approaches for EC phenotypic analysis in vitro - what is the advantage of using ECPT? The authors repeatedly use the term "single-cell level of analysis ", but this is in fact the case of any IF based analysis of cultured cells.

R: We thank the reviewer for the suggestions. Indeed, several tools for imaging based single cell phenotyping are available. However, ECPT represents an improvement under several aspects. First, it allows improved segmentation of difficult-to-segment and heterogeneous cells; second, ECPT allows multi-parametric analysis on large image datasets in a semi-automated and structured way facilitating downstream data analysis; third, ECPT is open source.

Furthermore, ECPT is a very flexible workflow including tools which facilitate and automate several tasks such as systematic images re-labelling and grouping. We will now draft a table including a complete list of features and improvements in comparison to other available tools and include it in revised manuscript in appendix1 and include analyses which are not implemented in any currently available software such as spatial autocorrelation.

I strongly recommend to stain HPMECs for PROX1, these cells are frequently 100% lymphatic endothelial cells. In this case the authors compare different lineages and not blood endothelial cells from different locations.

R: We thank the reviewer for the suggestion. We will address this with a new characterisation as supplementary figure in the revised manuscript. We are currently performing a qRT-PCR screening of several EC marker including arterious, venous and lymphatic markers (e.g., CXCR4, Tie2, CDH5, PROX1, LYVE1 as well as baseline NOTCH1 and Dll4 and downstream genes such as HES1 and HEY2.

Please provide evidence for specificity of NICD antibody.

R: We thank this reviewer for the suggestion. Please see response to Reviewer one point 5.

Figure 1: HPMEC picture appears out of focus

R: We thank this reviewer for noticing, we will now include a clearer picture in revised version of the manuscript.

Figure 3 A - it is not entirely clear what is the difference between activated and stressed phenotype, they look quite similar.

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R: We will clarify the definitions of cell activation in revised version of the manuscript and present this analysis as supplementary material to demonstrate the flexibility of our ECPT rather than in main figures. We have removed Pha staining from the new experiments we are performing to allow HES1 staining and address NOTCH signalling in more details. The assessment of Pha and stress fibres in previous experiments will be moved to supplementary material. The classification is based on PhA staining using CPA classifier which was trained to distinguish among the two by the presence of stress fibres. The general rule to place cells in the stressed category during training of the CPA model was the observation of stress fibres crossing the nucleus while cells with peripheral bundles of actin were placed in the activated category.

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Figure 5 - what is the difference in NICD localization between "high" and "On" conditions?

R:

Since it has been noted by this and other reviewers that this classification might be difficult to interpret and in fact, the established thresholds are somehow arbitrary, we will completely revise the way we present analysis of NOTCH activation data including downstream analysis and more formal metrics of spatial correlation and extent of activation eliminating the need to impose thresholds (also see response to Reviewer one point 3).

Since the authors make a correlation between Notch activity and junctional stabilization, it would be important to confirm this by other means, such as analysis of Notch target genes.

R: We thank this reviewer for the comment which resonate with this and other Reviewers’ comments. We will include HES1 analysis in the revised manuscript, please see Response to point 6 and reviewer’s one point 3 above.

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**Technical and minor**

1. Methods mentions HDMECs (human dermal microvascular endothelial cells) but the authors discuss HPMEC throughout the text 2. Please add scale bars on all microscopy pictures. 3. Please provide the information on what isoform of VEGF-A was used for stimulation and the rationale for selecting the concentration.

R: We thank this reviewer for flagging these imprecisions and we will fix them in revised version of the manuscript.

Reviewer #2 (Significance (Required)):

The authors provide a workflow for the phenotypic analysis of cultured cells. Such tool is potentially useful, although the examples the authors show do not reveal striking examples of why such analysis is better in comparison to existing approaches. My guess is that the analysis may be faster and less tedious, once the training sets are generated, but this is not specified. My speciality is endothelial cells biology.

R: We thank this reviewer for their very useful and appreciative comments. As mentioned above we will expand appendix 1 to fully explain potential and utility of our ECPT and review the main text to clearly highlight main advantages.** We hope that our plan for revision will fully address remaining concerns.

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

**SUMMARY:**

The manuscript by Chesnais et al. presents a novel endothelial cell (EC) profiling tool (ECPT) which provides spatial and phenotypic information from individual ECs, and was tested with a variety of specialized EC subtypes (arterial, venous, microvascular). They present a high throughput immunostaining and imaging-based platform using culture of human ECs on 96-well plates and capture of fixed, stained samples on a Perkin Elmer Operetta CLS system. The authors report the use of this ECPT tool to investigate EC phenotypes from human umbilical vein ECs (HUVEC), human aortic ECs (HAoEC) and human pulmonary microvascular (HPMEC) in relation to 50 ng/mL VEGF stimulation for 48 hours, and the general parameters of proliferation, Notch activation and stress fiber rearrangement (F-actin), and present this as a prospective platform to examine differences in EC phenotypes and responses at a more individualized level.

**MAJOR COMMENTS:**

1. Fundamentally, the advantage of single cell technologies is the ability to segregate populations to make novel observations. One area that would be of interest to explore in this manuscript using this ECPT platform would be reporting the results from single cell analysis that is then subsequently pooled within a sub-population, rather than sub-stratifying populations to reflect the multiple phenotypes that may be present within a single "confluent" well. With analysis of EC heterogeneity, it would be of interest to differentiate heterogeneity within EC subtypes at the culture/treatment conditions presented, and heterogeneity between EC subtypes.

R: We thank this reviewer for the suggestions, we believe that the new approach to evaluate heterogeneity through spatial autocorrelation can provide a much better and clearer picture of this aspect (see responses to Reviewers One point 3 and Two points 6 and 7. Furthermore, we are currently restructuring the ECPT data structure to a more intuitive layout (list of lists rather than a single huge data frame) without affecting downstream data presentation. We will also update our Shiny App to enable the user to perform analyses on data subsets of interest without any R coding, we will present examples and walkthrough of this approach in appendix.

2.

The term "stable IEJ" is used and refers to 48h after seeding 40,000 cells on a 96-well plate, but it is unclear how the authors defined or demonstrated a "stable" junction. In previous reports, longer-term culturing of EC monolayers well beyond the point of confluence has been shown to result in junctional complex rearrangement (Andriopoulou P et al. Arterioscler Thromb Vasc Biol. 1999; reviewed in Bazzoni G & Dejana E. Physiol Rev. 2004). To this point, the fact that the different EC subtypes investigated had different percentages of "quiescent cells" suggests that the monolayers were not completely quiescent. The statement that the IEJ classification is "an immediate index of EC activation in contrast to quiescence" should be further supported by references or data. The definition of quiescent EC as simply non-proliferating, non-migrating is somewhat reductionist, and oversimplifies EC states. The authors state that HAoEC and HUVEC "...appeared more active...", but it is unclear what "active" means, and whether this may simply reflect that these cells had not yet reached confluence or quiescence in the 48h total culture time. As well, it is unclear how "migratory phenotypes" could occur in confluent monolayers. It would be helpful to see the data for these observations. If leaving ECs longer in culture, are the authors able to achieve a higher percentage of quiescent cells?

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R: We thank this reviewer for the very insightful comments and for suggesting the references. Indeed, we considered these aspects carefully. Regarding cell culture density and confluency, we previously tested seeding densities of 30000-60000 cell/well of 96 well plates (0.32 cm2, ~95000-190000cells/cm2) and we selected 40000 as the maximum seeding density allowing adhesion of >99% of cells. For HUVEC, a seeding density of 40000 cells/well (125000 cells/cm2) produced a high-density culture immediately after seeding (close to what reported for long-confluent cultures in Andriopoulou P et al, ATVB 1999, 140000 cells/cm2). We allowed further 48h culture aiming to achieve junctional “stabilisation” and “maximal” cell density. For consistency, we also seeded 40000 HAoEC and HPMEC per well in all our experiments, however both cell types are significantly larger than HUVEC (Fig 4). For all cells cultures we used EGM2 medium which has few differences with that reported in Andriopoulou P et al, namely, absence of antibiotics and antimycotics and use of defined cocktail of recombinant growth factors instead of Endothelial Cells Growth Supplement. In the past we compared HUVEC cultured in EGM2 and supplemented M199 medium and in our experience EGM2 promotes higher proliferation rates in sub-confluent cultures but similar morphology upon confluency. Is notable that several other factors (including flow, matrix, perivascular cells) are absent in our culture conditions and therefore the homeostatic balance found in vivo might not be fully achievable under our experimental conditions. However, we argue that the described culture conditions should be sufficient to reach a bona fide relatively quiescent EC phenotype in culture.

Save these considerations, we agree with this reviewer that providing examples of longer-term cultures would help substantiating our findings and further validate the ECPT approach. We will perform a supplementary experiment to evaluate this aspect by comparing 48h cultures with longer culture times (72h and 96h). Furthermore, we will expand the methods section with the details discussed above and in relation to the suggested references.

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Regarding the definition of “stable IEJ” and “active EC”, we used this terminology referring exclusively to our measures of IEJ stability (STB index) and Pha based cell classification where we used the terms of “quiescent”, “active” or “stressed”. Therefore, all statements mentioning more or less “stable IEJ” or “active” EC are relative to the specific context of our experiment (not in absolute terms).

Overall, we appreciate that the terminology we employed is a source confusion and might suggest inappropriate over-interpretation of our results. We will correct the text in the manuscript to avoid this confusion and to clarify that our observations are valid within the context of our in vitro conditions. In particular, we will present the data regarding junctions as proportions of different junction per cell, and we will rename cell “activation” categories based on PhA immunostaining using more neutral terms (e.g., No Fibres, Peripheral Bundles, Stress fibres). Finally, we will also attempt to generalise our observations to more physiologic context by performing immunostaining on “en face” preparation of murine blood vessels (cfr response to R1 point 1).

Fig 4: Cell area density distribution for HUVEC, HAoEC and HPMEC in baseline conditions.

Could the authors comment on the baseline NICD immunoreactivity in the nuclei in HAoEC and HPMEC compared to HUVEC? Is this a reflection of active NOTCH signaling? Or rather, is it possible contact-inhibition (and downregulation of NOTCH) may not have occurred? Demonstration of EC quiescence would help to ensure similar cell cycle states. The definition of "Notch-positive" and "Notch-negative" cells is a bit misleading, as NICD levels and localization are a better indication of canonical Notch activation, and not the presence or absence of Notch protein(s). Further, NICD activation is also dependent on the levels of Notch ligands, which was not addressed. Are the authors able to confirm "OFF", "Low", "High", and "ON" classifications based on NICD intensity and localization with downstream Notch gene activation at a single-cell level? Or correlation between NICD status and the phase of cell cycle or proliferation status?

R: We thank this reviewer for the comment. Overall, NICD either nuclear or cytoplasmic can give a measure of how much a cell is relaying canonical notch signalling in a small timescale (minutes, which is also the timescale affected by lateral inhibition, Sjoqvist M and Andersson ER, Dev Biol, 2019). By evaluating single cells in the context of their population in multiple fields of view and samples we can get an indication of how frequently a particular cell type tends to actively transduce canonical NOTCH (under confluent conditions). As this and other reviewers have pointed out NOTCH signal transduction mediated by NICD can be affected by several factors limiting the potential to infer actual activation of the pathway (i.e., downstream gene transcription. As suggested by this and other reviewers we are including measures of downstream gene activation, in particular we have included HES1 staining in our workflow, and we will include these data in a new analysis (also see response to R1 point 3). We will also provide new metrics of spatial autocorrelation to evaluate the tendency to lateral inhibition (R1 point 3) and correlation between parameters using continuous mesures and therefore we will remove the previous classification based on thresholds. Finally, we are performing a qRT-PCR screening to assess baseline levels of DLL4, NOTCH1 and JAG1 which we will present as supplementary material.

Do as I say, Not(ch) as I do: Lateral control of cell fate

Sjoqvist M and Andersson ER, Dev Biol, 2019

PMID: 28969930

The existing workflow/platform is adapted for images obtained from the Operetta CLS system (Perkin Elmer) and Harmony software (proprietary), which may not be available for broader users in the EC field. It would be helpful to include ImageJ macros for the bulk automatic import of TIFF, renaming and upscaling of resolution/bit quality to match the formats that are compatible with the software.

R: We thank this reviewer for the comment. We have now included an ImageJ macro (available in the GitHub repository) which in principle can import and elaborate images from any source. We didn’t include a specific option in our current user interface because the relabelling operates by parsing original filenames into fields which are then renamed according to user input and each HT platform adopt different regular expression to encode filename. Any user with a basic literacy in ImageJ macro scripting can achieve relabelling and elaboration of their own file given that their filenames use regular expressions which can be parsed. Also, it is relatively easy (again by modifying the macro) to include user defined pre-processing steps including image scaling. An example of parsing method for Operetta CLS filenames is provided in appendix 1.

Could the authors comment on the manpower (hours from start to finish for experiments, staining, imaging, analysis, etc.) and cost of the ECPT pipeline relative to emerging single cell technologies such as single cell-RNA sequencing.

Further, one major advantage of imaging technologies is the ability to assess live cell dynamics, which are particularly relevant in response to stimuli and agonists. Have the authors utilized the ECPT platform for these approaches, in particular, to assess the differential EC subtype dynamics in proliferative conditions?

R: In terms of manpower the workflow is not very demanding. Our current dataset is based on images extracted form 4 independent experiments (18 wells each). The process is sequential, therefore a single user trained in cell biology, automated microscopy and in the use of the different ECPT components (ImageJ, CP, CPA and R) could perform the experiment alone. The timing of each experiment will depend on circumstantial factors, however once the ECPT is trained for specific user’s requirements (which can require some trials and errors depending on user’s experience) the whole process from cell fixation and staining, through image acquisition (~2 h acquisition for each experiment on an Operetta CLS system), to dataset build-up can take less than one week. For example, elaborating the current image database (~6000 images for four fluorescence channels) which data are presented throughout, had the following raw elaboration times on a Mac Book Pro 2017 equipped with an intel i7 processor and 16 Gb of RAM:

- Image pre-processing and relabelling ~1h

- Generation of probability maps for VEC and NICD ~3h

- CP pipeline run (Cell segmentation, objects measurements and classification) ~16h

- Data import (R studio) ~20m

• *

We will measure these parameters more precisely in the new experimental run and present timings for each step in a new table in appendix 1.

• *

After main dataset is created R studio can perform most statistical analyses and data plotting almost instantly.

• *

We fully appreciate the value of employing ECPT in live imaging setups and we believe it is one of the most promising future applications. We didn’t address live microscopy experiments in the context of ECPT development and validation presented in the current manuscript therefore we cannot present example data or proof of concept. However, we can confidently comment that time lapse experiment would not endow further layers of complexity in terms of image analysis workflow. Therefore, given appropriate set of live markers (e.g., transgenic fluorescently tagged CDH5 for EC segmentation and junctions analysis) we believe that the current implementation of ECPT is already fully equipped to facilitate elaboration and analysis of imaging data derived from time lapse experiments.

The authors should discuss the ability to amend or revise of the ECPT platform to incorporate analysis of additional markers that may be obtained through imaging, and discuss greater implications and utility to specifically tailor the workflow for other researchers in vascular biology, or to other monolayer culture systems. Further, they should better highlight the novel observations obtained with the ECPT compared to traditional methodology.

R: We thank this reviewer for the comments. We will provide evidence of ECPT flexibility within this manuscript by including, during the time of this review process, a new analysis for downstream NOCTH signalling (HES1). We will move analysis of cell “activation” (i.e., stress fibres analysis) to supplementary information and include a more through discussion of how automated single cell classification could improve content, speed, reliability and robustness of quantification tasks which are currently exposed to long and tedious processing times and conscious/unconscious observer biases.

**MINOR COMMENTS:**

We thank this reviewer for the very thorough revision of the manuscript. It is truly invaluable to us to improve it. Below responses to specific technical points, we will fix all stylistic, formatting and typographical issues in revised version of the manuscript.

1. There are minor typographical, capitalization and grammatical errors throughout.

R1: Thanks, we will fix these in updated version of the manuscript.

Why was fibronectin used to coat plates, and what was rationale for using this ECM substrate versus gelatin (most commonly used in EC cultures) or type I collagen?

R2: We used fibronectin for immunostaining experiments similar to what reported in our previous work (Veschini et al, 2007, 2011, Wiseman et al, 2019) and also in Andriopoulou P et al,1999. In general, in our experience FN gives better cell adhesion in comparison to gelatin when culturing EC on glass or other substrates different from cell culture plastic. FN is the cell culture substrate recommended by Promocell therefore, we also used FN for cell expansion to avoid any phenotypic change which might have been caused by switch in cell culture substrate.

3. Based on the various box plots present throughout the figures, it appears that some parameters have a large range of values. Is it possible or helpful to set minimum and maximum exclusionary criteria? Further, in the way that these data are presented, it is difficult to appreciate the effects of a treatment such as 48h of VEGF, as the magnitude of STB Index difference, for example, appears small, and it is difficult to understand whether these significant differences are biologically relevant, as assessed.

R3: We agree that in absence of exclusion criteria it is difficult to infer biologic meaning out of subtle differences (e.g., the tiny difference in STB index between HAoEC in presence or absence of VEGF). In the current version of the manuscript, we attempted to be agnostic in regards whether some observed small but significant mean differences could endow biologic meaning and discussed larger variation as biologically meaningful, for example the differences in STB index among cell types. We argue that tiny differences in the distribution of some selected parameter across experimental conditions could reflect underlying mechanisms masked by biologic noise, therefore catching a glimpse of these variations via ECPT could inspire novel experiments to specifically address their full biologic significance.

To the interest of better understanding of the current manuscript we will re elaborate our data to provide more immediate metrics and highlight outstanding features.

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Use of arrows and further description in Figure 1 would help the reader understand what specific features are different in the various EC subtypes. As well, the representative micrographs for HPMEC appear blurry compared to other panels (Fig. 1).

In Figure 2, the panels in A, B and C do not correspond horizontally, and it may be cleared to demonstrate "Segmentation & features extraction" overlays from the same representative micrographs shown in panel A. Labeling of the individual panels and software used for panel B would help the readership understand what is being quantified and how. The second panel in "C" appears blurry.

In Figure 3, labelling the color code for quiescent, activated and stressed categories on graphs and in legend would be helpful to easily identify populations.

R4-6: Thanks, we will fix these in updated version of the manuscript.

For Figure 4, line separators or more obvious grouping to distinguish discontinuous, linear and stabilized junction types in panel A. What proportion of the different EC subtypes contains discontinuous, linear and stabilized junctions at confluence/quiescence? Is there a correlation between discontinuous junctions and proliferating cells?

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R7: We will perform new analyses to address correlation between proliferation and junctions and proliferation vs HES1. We will restructure data presentation on junctions to display different proportion of junctions per cell or per cell type rather than a unified value (STB index).

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It would be useful to distinguish the effects of published mediators on junctional integrity in intact EC monolayers (i.e. histamine; VEGF) from those shown in this automated quantitation. It appears that 50 ng/mL of VEGF treatment for 48h only slightly increases STB index based on panel C.

R7c__: __We agree that increase of STB index in HAoEC and HPMEC upon VEGF treatment might not be highly biologically meaningful, save consideration in point 3 above. However, difference in HUVEC (+- VEGF) is visually appreciable in images (i.e., VEGF treated HUVEC seem to have more linear junctions) therefore we believe that the ~16 units difference in STB index is biologically meaningful. As discussed in point 7 above, we will restructure data presentation to better clarify these aspects.

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Figure 5 panel B should provide legend in graphs/figures or figure legends to highlight the color-coding matching the OFF, Low, High and ON groups. Further, it is unclear the difference between "High" and "ON" groups. The authors state that "thresholds were selected empirically", however, it is unclear whether this was derived through utilization of known Notch activators or inhibitors, and how this relates to the threshold of Notch activity necessary to enhance proliferation or maintain quiescence. In Supplementary Figure 4 (which I believe is mislabelled as Supplementary Figure 5), shows only a weak positive correlation between nuclear NICD intensity and mean STB index. It would be of interest to see the plot from Supplementary Figure 5 for each of the EC subtypes, in the presence and absence of VEGF. As well, for Figure 5, on C and D panels, it would improve clarity to revise "Low" and "High" descriptors with "Low NICD activity" and "High NICD activity".

R8: As discussed above we will revise our analyses to remove NOTCH categories and instead show spatial autocorrelation analyses which work on continuous data.

In Supplementary Table 1, "Widt/length" should be "Width/length"

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R9: Thanks, we will fix this in updated version of the manuscript.

For Supplementary Figure 3, it would be of use to show DNA distribution intensities from proliferating, non-confluent EC subtypes to demonstrate the validity of this methodology to identify cells in G0/G1, S and G2/M phases, as highlighted in panel A. Could the authors comment on the discrepancy between the percentage of cells identified as quiescent by ECPT and the percentage of cells in G0/G1? The comment that "VEGF induced a small detectable increase in proliferation rate in all EC" is curious, as a dose of 50 ng/mL of VEGF should be a relatively strong stimulator of proliferation/migration in ECs.

R10: We will perform ECPT analysis on sub-confluent or sparse cells to further validate our analysis. Qualitative data on preliminary images seems to confirm that the proliferation rate in sparse cells is very high (>70%). To perform the evaluation we followed and improved a previously published method (Roukos et al, Nat Prot, 2015)

Regarding the relation between cell in G0/G1 and assessment of “quiescent” phenotype (which nomenclature will be revised as discussed above), it is important to highlight that we reported data on stress fibres analysis (i.e., classification into “quiescent”, “activated” and “stressed” cells) only on the cells in G0/G1 (i.e., we excluded proliferating cells from this analysis as we assumed that all proliferating cells would be “not quiescent” and bias our estimation).

For Supplementary Figure 5, "Nuclear NOTCH intensity" on the Y-axis should read "Nuclear NICD intensity", as it does not appear that Notch was stained. It would also be of benefit to overlay the ranges for "OFF, Low, High and "ON" to appreciate ranges of activation. Is there any correlation between NICD nuclear intensity and proliferative index?

R11: We will present correlation between NICD or HES1 and proliferation in revised version of the manuscript.

Definitions should be provided for many terms. i.e. vascular endothelial-cadherin (VE-CAD; CDH5); HUVEC (human umbilical vein endothelial cell); HAoEC (human aortic endothelial cell); HDMEC (human dermal microvascular endothelial cell); NICD (NOTCH intracellular domain); VEGF (vascular endothelial growth factor); etc. at first appearance.

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R12: We will add this information in revised version of the manuscript.

For EC subtypes purchased from commercial vendor, it would be of interest to understand how many unique donors these cells/data were derived from, and whether there are any differences in basic donor information such as age, sex, etc. Further, Promocell catalogs proliferative rate for each of their lot numbers, and it would be of interest how this compares to the values determined using the ECPT software analysis package.

R13: We will add this information in revised version of the manuscript.

1 In the "Cell culture" section of the methods, HDMEC from Promocell are listed, however, the manuscript and figures show data from HPMEC. Both EC subtypes are available from Promocell, however, HDMEC are from dermal origin.

1 Vascular endothelial-cadherin should be abbreviated "VE-CAD" or "CDH5" and not "VEC", as this is not a standard or gene notation, and will likely be confused with the more common abbreviations for venous or vascular EC. It seems as though "CDH5" is used most commonly throughout manuscript, so this should be used throughout.

1 The authors refer to "activated NOTCH" when describing antibodies in the methods, however, it would be clearer to the reader to simply refer to the antibody target (NICD), and mention that this reflects canonical NOTCH downstream activation.

The sentence in the "Immunostaining" methods "CDH5 is a lineage marker..." should be moved to results/discussion as these details are out of place in methods.

How were the 3 areas captured per wells designated? Were these locations the automated, and the same for all wells?

"Appendix - Figure" notation should be revised to "Appendix Figure" for consistency and to avoid confusion.

R14-19: Thanks, we will fix these in updated version of the manuscript.

How were artifacts and mis-segmented cell objects excluded?

R20: We will add this information in the revised appendix. As general rules, cells containing NaNs values in any of the parameters, cells fragments or merged cells (evaluated using area measurements) and cells with no detectable junctions were all excluded (total cell excluded from analysis were ~ 2.5 % of the initial dataset).

• *

In "Statistical analysis" "Tuckey's" should be "Tukey's". "HSD" should be defined "honestly significant difference" or simply removed, as Tukey's is most common name.

In "Statistical analysis", "significative" should be "significant" or "statistically significant".

Scale bars should be added to micrographs.

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R21-23: Thanks, we will fix these in updated version of the manuscript.

Could the authors comment on the necessity of µclear plates, which substantially increases the cost per plate/experiment.

R24: m**clear plates were used to allow image acquisition with a 40x water immersion objective in the Operetta CLS (impossible with standard 96 well plates). Cell grown on coverslips and mounted on microscopy slides could be used as well with significant increase in acquisition time (Wiseman et al, 2019).

• *

Were other seeding densities and times investigated?

R25: We will evaluate sparse cells in revised version of the manuscript as discussed above.

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More description on potentially novel observations between these three primary EC subtypes would be informative for the readership to appreciate

The references do not appear in chronological order. Further, consistency of reference formatting should be reviewed, and appropriate journal name abbreviations should be used.

R26-27: Thanks, we will fix these in updated version of the manuscript.

Reviewer #3 (Significance (Required)):

• This manuscript presents a conceptual and technical advance, introducing a high throughput imaging platform to assess endothelial phenotypes
• Within the field of angiogenesis, several tools exist, either proprietary, or leveraging ImageJ software to assist in assessment of cells. The ECPT provides a more complex analysis platform to integrate analysis of multiple endpoints
• This work would be of interest to vascular biology laboratories to adopt a more comprehensive view of heterogeneous endothelial phenotypes in vitro
• As a vascular biology researcher, I have had extensive experience with in vitro culture of various endothelial cell subtypes from human and mouse. My field of expertise gives me the perspective of the nuances of the direct handling and phenotyping of ECs, and have worked specifically worked with HUVEC, HAoEC and HPMEC, and assessed the impact of key factors relevant in angiogenesis such as VEGF, Notch and other mediators.

R: We thank the reviewer for the very appreciative comments, and we hope that with the revised version of the manuscript we will be able to fully address remaining concerns.

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Referee #3

Evidence, reproducibility and clarity

SUMMARY:

The manuscript by Chesnais et al. presents a novel endothelial cell (EC) profiling tool (ECPT) which provides spatial and phenotypic information from individual ECs, and was tested with a variety of specialized EC subtypes (arterial, venous, microvascular). They present a high throughput immunostaining and imaging-based platform using culture of human ECs on 96-well plates and capture of fixed, stained samples on a Perkin Elmer Operetta CLS system. The authors report the use of this ECPT tool to investigate EC phenotypes from human umbilical vein ECs (HUVEC), human aortic ECs (HAoEC) and human pulmonary microvascular (HPMEC) in relation to 50 ng/mL VEGF stimulation for 48 hours, and the general parameters of proliferation, Notch activation and stress fiber rearrangement (F-actin), and present this as a prospective platform to examine differences in EC phenotypes and responses at a more individualized level.

MAJOR COMMENTS:

1. Fundamentally, the advantage of single cell technologies is the ability to segregate populations to make novel observations. One area that would be of interest to explore in this manuscript using this ECPT platform would be reporting the results from single cell analysis that is then subsequently pooled within a sub-population, rather than sub-stratifying populations to reflect the multiple phenotypes that may be present within a single "confluent" well. With analysis of EC heterogeneity, it would be of interest to differentiate heterogeneity within EC subtypes at the culture/treatment conditions presented, and heterogeneity between EC subtypes.
2. The term "stable IEJ" is used and refers to 48h after seeding 40,000 cells on a 96-well plate, but it is unclear how the authors defined or demonstrated a "stable" junction. In previous reports, longer-term culturing of EC monolayers well beyond the point of confluence has been shown to result in junctional complex rearrangement (Andriopoulou P et al. Arterioscler Thromb Vasc Biol. 1999; reviewed in Bazzoni G & Dejana E. Physiol Rev. 2004). To this point, the fact that the different EC subtypes investigated had different percentages of "quiescent cells" suggests that the monolayers were not completely quiescent. The statement that the IEJ classification is "an immediate index of EC activation in contrast to quiescence" should be further supported by references or data. The definition of quiescent EC as simply non-proliferating, non-migrating is somewhat reductionist, and oversimplifies EC states. The authors state that HAoEC and HUVEC "...appeared more active...", but it is unclear what "active" means, and whether this may simply reflect that these cells had not yet reached confluence or quiescence in the 48h total culture time. As well, it is unclear how "migratory phenotypes" could occur in confluent monolayers. It would be helpful to see the data for these observations. If leaving ECs longer in culture, are the authors able to achieve a higher percentage of quiescent cells?
3. Could the authors comment on the baseline NICD immunoreactivity in the nuclei in HAoEC and HPMEC compared to HUVEC? Is this a reflection of active NOTCH signaling? Or rather, is it possible contact-inhibition (and downregulation of NOTCH) may not have occurred? Demonstration of EC quiescence would help to ensure similar cell cycle states. The definition of "Notch-positive" and "Notch-negative" cells is a bit misleading, as NICD levels and localization are a better indication of canonical Notch activation, and not the presence or absence of Notch protein(s). Further, NICD activation is also dependent on the levels of Notch ligands, which was not addressed. Are the authors able to confirm "OFF", "Low", "High", and "ON" classifications based on NICD intensity and localization with downstream Notch gene activation at a single-cell level? Or correlation between NICD status and the phase of cell cycle or proliferation status?
4. The existing workflow/platform is adapted for images obtained from the Operetta CLS system (Perkin Elmer) and Harmony software (proprietary), which may not be available for broader users in the EC field. It would be helpful to include ImageJ macros for the bulk automatic import of TIFF, renaming and upscaling of resolution/bit quality to match the formats that are compatible with the software.
5. Could the authors comment on the manpower (hours from start to finish for experiments, staining, imaging, analysis, etc.) and cost of the ECPT pipeline relative to emerging single cell technologies such as single cell-RNA sequencing. Further, one major advantage of imaging technologies is the ability to assess live cell dynamics, which are particularly relevant in response to stimuli and agonists. Have the authors utilized the ECPT platform for these approaches, in particular, to assess the differential EC subtype dynamics in proliferative conditions?
6. The authors should discuss the ability to amend or revise of the ECPT platform to incorporate analysis of additional markers that may be obtained through imaging, and discuss greater implications and utility to specifically tailor the workflow for other researchers in vascular biology, or to other monolayer culture systems. Further, they should better highlight the novel observations obtained with the ECPT compared to traditional methodology.

MINOR COMMENTS:

1. There are minor typographical, capitalization and grammatical errors throughout.
2. Why was fibronectin used to coat plates, and what was rationale for using this ECM substrate versus gelatin (most commonly used in EC cultures) or type I collagen?
3. Based on the various box plots present throughout the figures, it appears that some parameters have a large range of values. Is it possible or helpful to set minimum and maximum exclusionary criteria? Further, in the way that these data are presented, it is difficult to appreciate the effects of a treatment such as 48h of VEGF, as the magnitude of STB Index difference, for example, appears small, and it is difficult to understand whether these significant differences are biologically relevant, as assessed.
4. Use of arrows and further description in Figure 1 would help the reader understand what specific features are different in the various EC subtypes. As well, the representative micrographs for HPMEC appear blurry compared to other panels (Fig. 1).
5. In Figure 2, the panels in A, B and C do not correspond horizontally, and it may be cleared to demonstrate "Segmentation & features extraction" overlays from the same representative micrographs shown in panel A. Labeling of the individual panels and software used for panel B would help the readership understand what is being quantified and how. The second panel in "C" appears blurry.
6. In Figure 3, labelling the color code for quiescent, activated and stressed categories on graphs and in legend would be helpful to easily identify populations.
7. For Figure 4, line separators or more obvious grouping to distinguish discontinuous, linear and stabilized junction types in panel A. What proportion of the different EC subtypes contains discontinuous, linear and stabilized junctions at confluence/quiescence? Is there a correlation between discontinuous junctions and proliferating cells? It would be useful to distinguish the effects of published mediators on junctional integrity in intact EC monolayers (i.e. histamine; VEGF) from those shown in this automated quantitation. It appears that 50 ng/mL of VEGF treatment for 48h only slightly increases STB index based on panel C.
8. Figure 5 panel B should provide legend in graphs/figures or figure legends to highlight the color-coding matching the OFF, Low, High and ON groups. Further, it is unclear the difference between "High" and "ON" groups. The authors state that "thresholds were selected empirically", however, it is unclear whether this was derived through utilization of known Notch activators or inhibitors, and how this relates to the threshold of Notch activity necessary to enhance proliferation or maintain quiescence. In Supplementary Figure 4 (which I believe is mislabelled as Supplementary Figure 5), shows only a weak positive correlation between nuclear NICD intensity and mean STB index. It would be of interest to see the plot from Supplementary Figure 5 for each of the EC subtypes, in the presence and absence of VEGF. As well, for Figure 5, on C and D panels, it would improve clarity to revise "Low" and "High" descriptors with "Low NICD activity" and "High NICD activity".
9. In Supplementary Table 1, "Widt/length" should be "Width/length"
10. For Supplementary Figure 3, it would be of use to show DNA distribution intensities from proliferating, non-confluent EC subtypes to demonstrate the validity of this methodology to identify cells in G0/G1, S and G2/M phases, as highlighted in panel A. Could the authors comment on the discrepancy between the percentage of cells identified as quiescent by ECPT and the percentage of cells in G0/G1? The comment that "VEGF induced a small detectable increase in proliferation rate in all EC" is curious, as a dose of 50 ng/mL of VEGF should be a relatively strong stimulator of proliferation/migration in ECs.
11. For Supplementary Figure 5, "Nuclear NOTCH intensity" on the Y-axis should read "Nuclear NICD intensity", as it does not appear that Notch was stained. It would also be of benefit to overlay the ranges for "OFF, Low, High and "ON" to appreciate ranges of activation. Is there any correlation between NICD nuclear intensity and proliferative index?
12. Definitions should be provided for many terms. i.e. vascular endothelial-cadherin (VE-CAD; CDH5); HUVEC (human umbilical vein endothelial cell); HAoEC (human aortic endothelial cell); HDMEC (human dermal microvascular endothelial cell); NICD (NOTCH intracellular domain); VEGF (vascular endothelial growth factor); etc. at first appearance.
13. For EC subtypes purchased from commercial vendor, it would be of interest to understand how many unique donors these cells/data were derived from, and whether there are any differences in basic donor information such as age, sex, etc. Further, Promocell catalogs proliferative rate for each of their lot numbers, and it would be of interest how this compares to the values determined using the ECPT software analysis package.
14. In the "Cell culture" section of the methods, HDMEC from Promocell are listed, however, the manuscript and figures show data from HPMEC. Both EC subtypes are available from Promocell, however, HDMEC are from dermal origin.
15. Vascular endothelial-cadherin should be abbreviated "VE-CAD" or "CDH5" and not "VEC", as this is not a standard or gene notation, and will likely be confused with the more common abbreviations for venous or vascular EC. It seems as though "CDH5" is used most commonly throughout manuscript, so this should be used throughout.
16. The authors refer to "activated NOTCH" when describing antibodies in the methods, however, it would be clearer to the reader to simply refer to the antibody target (NICD), and mention that this reflects canonical NOTCH downstream activation.
17. The sentence in the "Immunostaining" methods "CDH5 is a lineage marker..." should be moved to results/discussion as these details are out of place in methods.
18. How were the 3 areas captured per wells designated? Were these locations the automated, and the same for all wells?
19. "Appendix - Figure" notation should be revised to "Appendix Figure" for consistency and to avoid confusion.
20. How were artifacts and mis-segmented cell objects excluded?
21. In "Statistical analysis" "Tuckey's" should be "Tukey's". "HSD" should be defined "honestly significant difference" or simply removed, as Tukey's is most common name.
22. In "Statistical analysis", "significative" should be "significant" or "statistically significant".
23. Scale bars should be added to micrographs.
24. Could the authors comment on the necessity of µclear plates, which substantially increases the cost per plate/experiment.
25. Were other seeding densities and times investigated?
26. More description on potentially novel observations between these three primary EC subtypes would be informative for the readership to appreciate
27. The references do not appear in chronological order. Further, consistency of reference formatting should be reviewed, and appropriate journal name abbreviations should be used.

Significance

• This manuscript presents a conceptual and technical advance, introducing a high throughput imaging platform to assess endothelial phenotypes
  • Within the field of angiogenesis, several tools exist, either proprietary, or leveraging ImageJ software to assist in assessment of cells. The ECPT provides a more complex analysis platform to integrate analysis of multiple endpoints
  • This work would be of interest to vascular biology laboratories to adopt a more comprehensive view of heterogeneous endothelial phenotypes in vitro
  • As a vascular biology researcher, I have had extensive experience with in vitro culture of various endothelial cell subtypes from human and mouse. My field of expertise gives me the perspective of the nuances of the direct handling and phenotyping of ECs, and have worked specifically worked with HUVEC, HAoEC and HPMEC, and assessed the impact of key factors relevant in angiogenesis such as VEGF, Notch and other mediators.

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

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Referee #2

Evidence, reproducibility and clarity

The manuscript by Chesnais et al reports development of workflow for analysis of cultured endothelial cells , which they call Endothelial Cell Profiling tool (ECPT). Using ECPT they analyse several parameters in three different endothelial cell types (HuAEC, HUVEC and HPMEC), such as cell morphology, activation of cytoskeleton, VE-cadherin junctions, cell proliferation and Notch activation, under steady conditions and upon treatment with VEGF. The analysis allows to observe some predicted changes, such as increase in cell cycle and junctional activation in cells treated with VEGF-A, and such changes are highly heterogeneous. Overall, this is a potentially useful albeit not revolutionary tool for batch analysis of cultured endothelial cell phenotypes.

I have the following comments:

1. To make their case the authors should provide a comparison with other currently used approaches for EC phenotypic analysis in vitro - what is the advantage of using ECPT? The authors repeatedly use the term "single-cell level of analysis ", but this is in fact the case of any IF based analysis of cultured cells.
2. I strongly recommend to stain HPMECs for PROX1, these cells are frequently 100% lymphatic endothelial cells. In this case the authors compare different lineages and not blood endothelial cells from different locations.
3. Please provide evidence for specificity of NICD antibody.
4. Figure 1: HPMEC picture appears out of focus
5. Figure 3 A - it is not entirely clear what is the difference between activated and stressed phenotype, they look quite similar.
6. Figure 5 - what is the difference in NICD localization between "high" and "On" conditions?
7. Since the authors make a correlation between Notch activity and junctional stabilization, it would be important to confirm this by other means, such as analysis of Notch target genes.

Technical and minor

1. Methods mentions HDMECs (human dermal microvascular endothelial cells) but the authors discuss HPMEC throughout the text
2. Please add scale bars on all microscopy pictures.
3. Please provide the information on what isoform of VEGF-A was used for stimulation and the rationale for selecting the concentration.

Significance

The authors provide a workflow for the phenotypic analysis of cultured cells. Such tool is potentially useful, although the examples the authors show do not reveal striking examples of why such analysis is better in comparison to existing approaches. My guess is that the analysis may be faster and less tedious, once the training sets are generated, but this is not specified. My speciality is endothelial cells biology.

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Referee #1

Evidence, reproducibility and clarity

The authors highlight the importance of endothelial heterogeneity using endothelial cells from different tissues. They examined aortic and pulmonary endothelium as well as HUVECs. They cultured the cells in identical conditions and also stimulated them with a physiological concentration of vascular endothelial growth factor as well high concentrations as would be found in cancers. They developed a profiling tool that allowed analysis of individual endothelial cells within a monolayer and quantification of inter-endothelial junctions, Notch activation, proliferation and other features.

Major comments

1. It would be useful to apply this technology one step beyond two-dimensional culture, to use vessels opened up longitudinally so that one can see the monolayer of endothelial cells and assess whether it is relevant in primary material in situ. I think this would be a major utility of the whole approach.
2. There are some very nice images here but disappointed not see a field that could show staining and markers for several of the target proteins and thus show the heterogeneity and randomness or organisation of the endothelial cells. For example are any clusters of a subtype of endothelial cells around proliferating cells.
3. The Notch signalling is an important aspect of this work, particularly evidence of lateral inhibition would have been of value. For example, one might expect cells adjacent to each other to have alternating high and low NICD. NICD staining alone does score the extent of the signalling because of many factors that can influence the transport of the cleaved NICD. Really a marker of Notch signalling downstream e.g. HES or HEY family ,DLL4 fis needed to give more information about this critical aspect.
4. I really do not think that in Figure 5 it is justified to have a red line drawn through the cloud of points. The correlation coefficient is so low that this is meaningless. The failure to distinguish a P value from biological relevant is worrying. Much better comparison would have been between NICD staining and a downstream gene regulated by notch.
5. It is important to know that the antibodies used for staining have be validated by the investigators. They would need to show a single band on Western blots or be able to block staining on immunohistochemistry. We all know the manufacturers can be unreliable and use high concentrations of proteins for Western blots. These should be added as a supplementary figure.

Significance

This represents a valuable and thorough methodology likely to be highly useful to many groups and show new insights into endothelial biology.

Wide audience, cancer, cardiology, vascular disease-covid.

My expertise >100 papers on angiogenis in cancer, basic mechanism, therapy models, bioinformatics IHC, patients, clinical trial. H score 190 Google Scholar

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Reply to the reviewers

Point-by-point response, comments in (blue), our response in (black)

Note: we included 6 Figures in our response, yet the ReviewCommons system does not appear to support including images as part of the response. These Figures are in the original "Initial Response" file available to ReviewCommons. We requested that Review Commons post our "Initial Response" file that contains these figures so that this information is available.

Reviewer #1

*In the paper by Gowthaman et al., the authors aim at better understanding the molecular mechanisms controlling divergent non-coding transcription (DNC). They describe a high-throughput yeast genetic screen using two strains in which two loci consisting of a coding and a divergent non-coding transcription unit (CGC1-SUT098 or ORC2-SUT014) were replaced by a bidirectional fluorescent reporter construct encoding mCherry in the coding direction and YFP in the non-coding direction. The two reporter strains were crossed with the yeast deletion library and mutants leading to increased or decreased YFP signal were selected as potential DNC repressors or activators. The two screens identified a number of common potential repressors and activators. Components of the Hda1C histone deacetylase complex were identified as DNC repressors in both screens. This phenomenon was confirmed genome-wide by performing NET-Seq in WT as well as hda1D and hda3D strains. This experiment allowed to identify 1517 DNC transcripts repressed by Hda1. Further analyses indicate that Hda1C represses DNC genome-wide independently of expression levels and that loss of Hda1 does not substantially affect coding transcription.

Live-cell imaging of transcription was then used to show that loss of Hda1 increases DNC transcription frequency rather than duration providing novel information on the link between DNC transcription initiation kinetics and chromatin regulation. Finally, using Chip-seq, the authors show that the level of acetylation over the divergent non-coding units is increased in the absence of Hda1 and some experiments suggest that H3K56 acetylation also contributes to DNC regulation, further strengthening the importance of elevated histone acetylation in efficient DNC.

Importantly, several components of the SWI/SNF chromatin remodeling complex were identified as activators confirming earlier observations (Marquardt et al., 2014). SAGA subunits were also among potential DNC activators, however these effects could not be confirmed through validation experiments. The authors conclude that DNC may be independent of specific activators and mainly due to transcriptional noise resulting from the adjacent NDR.

Overall this paper is very well structured, clearly written and the experiments are well controlled. The genetic screen identifies novel factors involved in the regulation of DNC. The study clearly demonstrates that the level of acetylation is a key regulator of divergent non-coding transcription and that histone deacetylation by Hda1 reduces the frequency of DNC initiation events. While this conclusion is strongly supported by the Net-Seq and Chip-seq metagene analyses, the fluorescence mCherry and YFP values or qRP-PCR analyses of specific genes do not always behave as expected when looking at absolute values rather than mCherry/YFP or GCG1/SUT098 ratios, which is sometimes disturbing when reading the paper. Therefore, the following points should be clarified.*

We are grateful for the kind appreciation of our manuscript and clarify the remaining questions in the revised manuscript.

**Major points**

#1.1: Figures 2 and S2A: Figures 2C and D show the mCherry/YFP fluorescence and GCG1/SUT098 RT-qPCR gene expression ratios respectively, which are consistent with a repressive effect of Hda1C on DNC transcription and a potential DNC activating effect of SAGA components. However, the absolute mCherry and YFP or GCG1 and SUT098 expression values presented in Figures S2A and S2B show the opposite: loss of Hda1C subunits rather leads to a decrease in mCherry with not much effect on YFP; moreover loss of Hda3 results in decreased SUT098, which is inconsistent with the whole model. The same comment is valid for the SAGA mutants. It would be good to provide some explanation for these a priori contradictory observations, especially for the Hda1c mutants, which are the major focus of the study. The Net-Seq analyses are certainly more reliable since less subject to protein or RNA stability effects, which may underlie some of the inconsistencies between protein and RNA absolute levels.

Thank you for this comment. We offer enhanced clarity in the revised manuscript.

In general, transcription in each direction shows a weak yet highly statistically relevant positive correlation (Spearman rho = 0.26, p-value = 4.94e-24). We are enclosing a plot based on NET-seq data that supports the correlation in each direction of a NDR as part of our response below (RFig.1). To unpick relative effects the ratio captures these effects well, in our experience better than the individual fluorescence measurements or RT-qPCR. Of course, we are ultimately interested in transcription and fluorescence measurements or RT-qPCR of steady-state RNA are only an approximation. Resources and time constraints limit how many mutations we can examine by techniques such as NET-seq, which are arguably most informative. The positive correlation between transcription in each direction has the effect that relative differences can manifest themselves through detectable effects of the other fluorophore. As this reviewer mentions, we can be most confident of results that we could further validate by NET-seq or live-cell imaging.

(INSERT Rfig1)

RFig1: Scatterplot of NET-seq data for DNC/host gene pairs. Each point corresponds to a bidirectional gene promoter overlapping with a nucleosome-depleted region (NDR). The values represent NET-seq FPKM values in protein-coding (x-axis) vs non-coding (y-axis) directions. These data support a statistically significant correlation (Spearman test: rho = 0.2554876, p-value = 4.939658e-24).

#1.2: Figure 3: this figure examines the effect of Hda1 and Hda3 on the 1517 DNC transcripts. Does loss of this HDAC also increase the expression of all the other 2219 non-coding transcripts identified by Net-Seq, which would make Hda1C a more general repressor of non-coding transcription?

We have performed the analysis for all other non-coding transcripts in Hda1C mutant NET-seq data and added it as part of this response RFig2. Quantification of CUTs, SUTs and other lncRNAs that are not resulting from DNC in Hda1C mutants results in a slight increase in the nascent transcription that is not statistically significant. These data do not offer strong support for the idea that Hda1C represents a more general repressor. We added this plot as novel supplementary figure S3D and adjusted the text of the revised manuscript (line 214).

(INSERT Rfig2)

RFig2: Metagene plot of NET-seq data for non-coding RNA that are not classified as DNC. Metagene plot shows genomic windows [TSS - 100 bp, TSS + 500 bp] relative to the annotated starts of ncRNA transcripts.

#1.3: Moreover, does loss of Hda1 or Hda3 reveal DNC transcripts that were not detected in wild-type? This may increase even more the number of genes with divergent transcription.

We are grateful for the opportunity to clarify this point. We noticed that the yeast genome shows evidence for much more non-coding transcription than annotated. In this paper, we used TranscriptomeReconstructoR for a data-driven annotation of yeast non-coding transcripts, with an emphasis on the boundaries. See also:__ ( DOI: 10.1186/s12859-021-04208-2 ). The set of non-coding transcripts was for example informed by the previously published NET-seq data on wild-type samples (Churchman et al., 2009; Marquardt et al., 2014; Harlen et al., 2016; Fischl et al., 2017). We have clarified relevant Methods sections to make this point more accessible (line 733). The combination of these NET-seq datasets gives a very good sequencing coverage. The Hda1C mutant NET-seq data does not have a better coverage than this combined reference set, so it would be very hard to find new transcripts without prior evidence in our exhaustive set of combined NET-seq data. However, our Supplementary table S3 contains the fold-change values for all DNC transcripts in mutant compared to wild type. Loci with a high fold-change could arguably be regarded as hda-specific. __

#1.4: Figures S3A, B, C: are the 3 groups of DNCs derepressed to the same extent by loss of Hda1 or Hda3? This is difficult to judge given the differences in y-axis scales. Figures S3D, E: the authors show the Net-Seq snapshots for the GCG1 and ORC2 loci. It would be good to add the quantifications as presented in Figure 3 for YPL172C and YDRr216C.

Thank you for the suggestion. We replaced S3A-C with plots that show the same range of the y-axis in the supplementary figure. Hda1C represses DNC in all three cohorts stratified by DNC expression strength. We also added a quantification boxplot for NET-seq signal in the GCG1 and ORC2 loci in revised S3F-I.

#1.5: Figures S4A, B, C and D are not well explained. What does the y axis frequency correspond to? Is it the % of cells showing a signal? Is the intensity of SUT098 higher because the transcription initiation frequency is higher and therefore the transcription site signal is more intense?

We improved the annotation for the supplementary figure S4. We clarified in the legend that the y-axis frequency represents the percentage of frames recorded for transcription initiation spots (TS). The bars represent transcription intensity in all the frames recorded, with active transcription ‘ON’ and without TS ‘OFF’. The intensity increases with higher initiation rates and thus the intensity of SUT098 transcription initiation is high.

#1.6: Figures S4 A-I should be more specifically cited in the text.

We have cited the figures in the text in the revised version.

#1.7: Figure 5A: it is really unexpected and unclear why the mCherry/YFP in the WTH3/hda1D and WTH3/hda1D/H3K56mut is increasing compared to WTH3, since DNC is supposed to increase. Similar comment for Figure S5C. This should be clarified in the text.

Thank you for pointing this out. We missed to address this in the text. The isogenic control “H3 wild type” carries only one copy of the two genes coding for H3, which has a general effect on transcription. We added data showing this as part of our response (RFig3.), and explained this part more clearly in the revised text (line 263). Essentially, the genetic background of the yeast synthetic histone mutant collection sensitizes for a decreased ratio of mCherry/YFP (RFig3.). This result is also included in table S2, where deletions of the histone genes HHT2 (H3) and HHF2 (H4) are listed as shared repressors in both screens. Hda1C mutations show the increased ratio in the sensitized “H3 wild type” background, but not in backgrounds we tested that contain a wild-type dosage of histone genes.

These data remain valid to support the genetic interaction of hda1D along with the substitution mutants of H3K56.

(INSERT Rfig3)

RFig3. Fluorescence signal values of H3WT and BY4741 strains with GCG1pr FPR. The H3WT affects general transcription of coding transcript and decreases the ratio of mCherry/YFP fluorescence.

#1.8: More generally, as already mentioned above, the fluorescence data are expressed either as mCherry/YFP ratio or as absolute values. It would be good to systematically show the ratios and the absolute values of mCherry and YFP signal; the same for coding and DNC RT-qPCR as well as Net-Seq values when available.

We ensured that the absolute data values for flow cytometry and qPCR have been represented in the supplementary figures S2 and S5. The FPKM values for NET-seq data for individual transcript units are provided in the supplementary table S3.

#1.9: Figures S5A and B are not referred to in the text. It should be mentioned and explained how normalization to H3 affects the levels of acetylated H3 over the NDR.

We now refer to the figures in the main text and explained the rationale for normalization.

#1.10:* p. 12 "Our data thus suggest to extend the transcriptional noise hypothesis with activities limiting DNC transcription to account for genome-wide variation in non-coding transcription".

If DNC is the result of "transcriptional noise", it is surprising that in the case of CGC1-SUT098, the transcription frequency is higher in the non-coding versus the coding direction. Is the SUT098 behaving like the coding unit in this case? The authors should comment on that. *

This is very interesting point. One interpretation of the “transcriptional noise” hypothesis is indeed that non-coding transcription is at low level. We selected loci with high DNC expression, so these loci are somewhat contradictory to this idea a priori. Nevertheless, identifying a biological function of non-coding RNAs is challenging, and it remains to be tested if SUT098 represents particularly “loud noise” or if the high transcription indicates that it carries a yet unknown cellular function. In theory, this screen is suitable to identify factors that may be required to induce DNC, perhaps even specifically. To identify such factors a locus with high DNC is needed to facilitate detection, since our previous screen using the PPT1/SUT129 system had lower SUT expression and failed to identify such mutants systematically. This is important, since a mutation lowering DNC needs to start from a sufficiently high fluorescence signal to distinguish it from background fluorescence. Since the results presented did not clearly uncover such factors, we favor the hypothesis of DNC arising due to the promoter architecture at NDRs, see also positive correlation plot in RFig1. The many repressive pathways are also acting on highly expressed DNCs, which is certainly an interesting information provided by this manuscript.

**Minor comments**

#1.11: p. 4 should one talk about Hda1C-linked histone acetylation facilitates... (should be deacetylation...??)

Done.

#1.12: The authors should explain why they chose two coding/non-coding pairs that are cac2D insensitive and whether other criteria, such as level of DNC transcription, were also considered, since GCG1-SUT098 represents one of the most highly expressed divergent non-coding transcripts.

The GCG1 and ORC2 loci were chosen based on i) high DNC levels, ii) a low fold-change of NET-seq data in the cac2∆ and iii) a DNC region free from other transcriptional units. However, this was based on the state-of-the-art annotation in 2015 when we started this project. Also, when we categorized genes as affected by cac2∆, we used a fold-change expression cut-off that suggested that about a third of DNCs are repressed by CAF-I. It appears that we still underestimated the effect of CAF-I, since our data show that the target regions of our new screens are also affected by CAF-I. DNC expression at these loci is high, which would result in a low fold-change in mutants that further increased DNC here.

#1.13: It is hard to understand why both the H3K56A and H3K56Q mutations lead to increased DNC, a result already presented in the Marquardt et al. 2014 paper. It would be helpful to provide a more extensive explanation or hypothesis.

The H3K56 substitution mutant Q is expected to mimic the acetylation state and A is devoid of post-translational modifications. We observe an increase of signal ratio in the mutants because the H3K56ac is both responsible for incorporation and eviction of -1 nucleosomes (Marquardt et al., 2014). Mutations affecting H3K56 can thus result in less -1 nucleosome density and more DNC through reducing incorporation or enhancing eviction. We have improved the revised text to highlight this. We have clarified this in the text (line 271).

#1.14: What defines the level of DNC repression? How does the level of repression correlate with the level of coding transcription?

We have added RFig.1 to address the question about correlation. There is a statistically significant positive correlation between transcription in each direction by NET-seq data in wild type samples genome-wide. However, the correlation is weak (rho = 0.26), which is consistent with locus-specific adjustments of transcriptional strength in each direction. For DNC, several chromatin-based pathways contribute to repression. The resulting level of DNC transcription thus reflects the combined action of several pathways. Here, we characterize Hda1C as a novel player with a genome-wide effect on this phenomenon. Elucidating the mechanistic interplay at specific target DNC loci will be an exciting future research question.

Reviewer #1 (Significance (Required)):

This is a very interesting and innovative study using cutting edge genetic approaches, genome-wide sequencing as well as single cell imaging to extend our understanding of non-coding transcription regulation and its potential impact on gene expression. It is a nice continuation and complement of an earlier study from the same author (Marquardt et al., 2014) and will certainly be of interest to a large chromatin biology audience.

We are grateful for the appreciation of our research on this topic.

Reviewer #2

Promotors are frequently transcribed in both directions. The divergent, \upstream' transcript is frequently unstable. Transcription initiation is regulated through the acetylation of promoter-proximal nucleosomes, where HDAC-dependent deacetylation of histones typically represses transcription initiation.*

*The current manuscript addresses the question whether initiation of coding and divergent, non-coding (DNC) transcription is regulated by the same factors. Previously Marquardt and others showed that H3K56ac-mediated histone exchange has a differential effect on coding and DNC transcription.

Using a clever reporter system, the authors screened for positive and negative regulators that preferentially affect DNC transcription. They discover the Hda1 deacetylase complex as a DNC-biased repressor and diverse HATs as DNC-biased activators. The role of activators could not be validated, presumably due to high variability of the system.*

Focusing on Hda1c the authors present data suggesting a larger effect of Hda1c on 'upstream' nucleosomes associated with DNC transcription than in coding transcription. Genome-wide NET-seq mapping was consistent with this differential regulation. Life cell imaging of one specific case argues that Hda1-mediated repression reduced the time between initiation events. The authors employ state of the art methods and in general the data are of very good quality. The effect size is very small, which raises the broader question whether the results, while statistically significant is biological relevant. I have a few comments that the authors may use to revise their manuscript.

Thank you for the appreciation of our very good data quality. We hope our revision plan will help to clarify some confusion about the scope and effect size.

#2.1) The differentially regulated coding and DNC transcription are defined by a directionality score. The screen was performed with two reporter loci that are strongly biased for DNC transcription (the idea to detect activators did not work out). Considering that coding and DNC transcription may not be totally independent because of the proximity of target nucleosomes, and sense and antisense transcription may compete for regulators, the question arises how levels of coding transcription affect DNC transcription in wildtype and mutants. The authors stratified their results according to levels of DNC transcription, but discussion and data analysis of the effect of coding transcription on the directionality score may be relevant.

We added the plot in RFig.1 above to address the question of correlation between transcription in each direction. NET-seq data supports a weak but highly statistically significant positive correlation between transcription in each direction genome-wide (rho = 0.26, p-value = 4.94e-24). We agree that it is relevant to discuss the effect of coding transcription on the directionality scores and revised the discussion accordingly (line 315). We have used both the coding and DNC signal values to create the comprehensive quadrant scatter plot in Fig. 1D-E. Analysis of mutants along the diagonal illustrates that many mutations affect coding transcription as well as DNC. The directionality score measures deviations from the axis of positive correlation, which requires us to use the information of both fluorophores.

#2.2) The study is strong where the findings can be generalized. The single-molecule live-cell imaging analysis, while done properly, has only limiting impact, because the corresponding coding transcript could not be detected. This si more an anecdotal finding.

There seems to be a misunderstanding, the live-cell imaging measurements of transcription for SUT098 are stand-alone data. SUT098 by itself is a transcription unit, so we measure DNC of this unit independently from GCG1 that has much lower expression. The measurements are specific to SUT098 transcription and the quantification provides new information about the mechanisms involved in the regulation of DNC. We clarified the text in this regard (line 233).

#2.3) The effect size is small (20%, on average) and the variability is high. The fact that the HATs that emerged as very robust activators of DNC transcription could not be validated and that the Hda2 subunit of the HDAC complex was not found statistically significant show the limitations of the study. To their credit, the authors discuss these limitations appropriately.

We have worked on the Methods in the revised manuscript to clarify this confusion (line 712). For the screen, the median signal values represent data from up to 50,000 individual cells. These experiments are remarkably accurate and highly reproducible, especially for molecular biology where n=3 is common. We have uploaded these data to the FlowCore public repository. We encourage any colleague to exploit the opportunity to analyze these data independently to experience the high data quality. With high number of observations, 20% average is a large effect and reflects a rather big shift of the population. As is standard for genetic screens, resource constraints are prohibitive to pursue all hits. In addition, it is expected that only some hits will be affecting transcription of DNC since the fluorescence reporter can be affected by many other cellular events. We focused on the effects on DNC in this manuscript.

There seems to be some misunderstanding, Hda2 is a statistically significant hit in the ORC2/SUT14pr screen; this information is in Fig. 1E. The Hda1C subunits are labeled in purple.

#2.4) Figure S3C suggests that the Hda effect is largest at genes that are poorly expressed, and smaller at more average expression levels. Are we looking at a phenomenon that mainly applies to repressed genes?

Thank you very much for this suggestion. We replaced S3A-C with revised panels where the data is shown with the same y-axis scale, please see also #1.4. We believe the revised presentation also helps to clarify that the mutations increase DNC for all cohorts stratified by DNC expression.

**Minor issues**

#2.5) The NET-seq study involves two replicates. How well did they correlate?

The WT and mutant NET-seq replicates have good correlation (Spearman’s correlation coefficient was above 0.6 for WT and above 0.8 for the mutants).

(INSERT Rfig4)

RFig4. Correlation scatter plot of individual NET-seq replicates of WT, hda1D and hda3D. Spearman correlation coefficients of WT, hda1D and hda3D are 0.677, 0.8 and 0.825, respectively.

#2.6) For the live-cell imaging replicates were not mentioned. Were replicate studies performed?

We have updated the text to make this important point more accessible (line 230). For live-cell imaging studies, transcription is recorded as movies of cells over time. We took multiple movies, and pooled the data from all the cells to improve statistical power. Data from each movie represent individual repeats. We monitored 130 cells on average for the WT and mutant strains over time.

#2.7) Fig 4E is not mentioned in the text (mislabeled as 4D)

Done.

#2.8) Fig S5 is not mentioned in the main text.

__Done.

__Reviewer #2 (Significance (Required)):

In summary, this is a high-quality study that presents the results of a genome-wide screen that will be of interest to colleagues in the narrower field. Due to the small effects the results may appeal less to a general readership.

We are grateful for appreciating our manuscript as a high-quality study. We hope our revisions help to clarify confusion concerning effect size.

Reviewer #3

In this manuscript, Gowthaman et al describe the results and follow up of their screen aimed at identifying regulators of divergent noncoding (DNC) transcription in S. cerevisiae. From this screen, they identify Hda1C as a repressor of DNC transcription, and perform follow experiments to support and detail this finding. In addition to RTqPCR to confirm the reporter and endogenous changes, the authors perform NET-seq to look at global DNC alteration upon Hda1C subunit deletion and identify a number of non-coding transcripts with altered expression levels. In addition, the authors perform live cell imaging to demonstrate that there is a modest restriction of initiation frequency when one of the subunits of Hda1C is deleted. Finally, the authors explore changes to pan-H3 acetylation and the genetic overlap between Hda1C and H3K56ac demonstrating independent genetic pathways, but overall increases in H3 acetylation over DNCs when Hda1C is deleted. Overall, the screen and results are of interest, but the authors overstate some of the conclusions (perhaps most importantly within the title!). I have the following suggestions to improve the manuscript:

Thank you for recognizing the interest in our results. We have revised the manuscript to state the conclusions more cautiously.

**Major comments**

#3.1. The title of the manuscript is based on the single molecule live cell imagining experiments presented in Figure 4. While there is a statistically significant decrease in initiation frequency from deletion of one Hda1C subunit, there is no statistical decrease in deletion of the other two. Furthermore, these experiments were performed at one locus. As a result, I find the title to be an overstatement of the findings of the paper and suggest the authors refocus on the more robust findings of the manuscript.

Live-cell imaging requires extensive engineering of the target loci. Perhaps this was lost in the Methods, but it is a 5-step process to integrate the stem-loops. We tried to engineer other loci, but this is far from trivial and this technique does not work for all loci tested. The hairpins are also unstable, and need to be carefully checked prior to experimentation, which challenges scaling this approach up to a higher-throughput. It appears that we undersold this point, but the fact that we now provide a locus and strains for the community that makes such studies possible for DNC represent a tremendous achievement. Since hda1D also decreases time between initiations, we generalized the finding to Hda1C.

However, we recognized that the reviewer makes a helpful suggestion to choose a more careful title since there is no statistically significant reduction of initiation frequency in some mutants. We have revised the title to “__Hda1C limits divergent non-coding transcription and restricts transcription initiation frequency__” in the revised manuscript to address this point.

#3.2. Relatedly, in Figure 4, the authors present the findings from the single molecule live cell imaging experiments. Within this experiment, the authors include a cac2 deletion (CAF-1 subunit) strain, and observe a modest effect, similar to hda1 deletion. This is surprising as the authors mentioned this location (GCG1/SUT098) was selected as CAF-1 was NOT shown to regulate the DNC previously (Marquardt et al 2014; as mentioned at the beginning of the Results section). The similar decrease in initiation frequency between cac2 deletion and hda1 deletion further concerns me regarding the use of these data as the headlining finding.

We believe there is a misunderstanding. We clarify that selection of the GCG1 locus was based on a cut-off value for cac2D effect, as is also shown in Fig S1C. The fold-change is small, but since DNC transcription of the chosen loci is high in wild type, an increase in a mutant would not necessarily give a high fold-change. Hence, we need to be cautious to conclude that CAF-I does not regulate DNC at this locus. The fold-change analysis suggested it, but it remained possible. CAF-I appears to affect even more loci than initially identified with the chosen cut-off. We see the same trend as in Hda1C mutants as in cac2, which offers support to the exciting idea that modulation of the initiation frequency may be a shared mechanism by chromatin-based regulators acting on DNC.

#3.3. It is unclear to me why the change in mRNA expression is included within the screen. Why not solely look at the expression change of the DNC? Importantly, the authors note in the discussion that perhaps the reason the SAGA complex was identified was due to regulating mRNA expression and not DNC expression and therefore was identified in the screen. Could the authors not just present the fold change in DNC expression using their YFP reporter, and not the YFP vs mCherry?

The regulation of initiation frequency in each direction is super-imposed on a general positive correlation __(rho = 0.26, p-value = 4.94e-24) between the coding and non-coding directions__, please see also RFig.1. For the purpose of this study about selective effects on the direction of transcription, it is vital to incorporate both sides of the reporter. Otherwise, we would select for factors that activate or repress the transcription from the target promoter NDR. This point is accessible in Fig.1D-E, where mutations that affect YFP usually also have an effect on mCherry. The aim of this study was to identify mutants that affect the relative expression, and therefore a focus on one fluorophore would not improve the analysis. We clarified this important point more accessibly in the revised manuscript (line 315).

Please also note that all the raw data are available, so colleagues are in the position to perform their independent analyses. We believe that it is very valuable for the community to have access to these data since they may be useful for other purposes and could be analyzed in many different ways. In fact, we have tried several methods and approaches over the years and present what we believe is most appropriate in this manuscript. For example, Hda1C comes out as a convincing hit with a range of different approaches to analyze the data, which is also a reason we feel confident about the characterization of Hda1C.

#3.4. This is absolutely beyond the scope of the paper, but limiting the screen to only nonessential proteins likely misses important regulators. In the future, perhaps the authors could pursue a SATAY screen to look for essential proteins as well? Again, the findings of this paper are appropriate, and the screen is a great undertaking, but I want to suggest this to the authors for potential future projects.

Thank you for this excellent suggestion. We agree that capturing the role of essential factors would be very informative, and the saturated transposition approach would be promising. However, as the reviewer points out, performing these analyses is beyond the scope of the current manuscript.

#3.5. The authors perform NETseq experiments in deletion strains and identify ~1500 DNC transcripts with altered expression. Later the authors look into the mechanism and demonstrate an increased H3ac in hda1 deletion strains. The authors could enhance the representation of these datasets by correlating the change in H3ac with the change in DNC transcription - do they correlate?

Thank you for bringing up this excellent point. We present the correlation data of change in H3ac and DNC transcription in the hda1D mutant (RFig5.). The ChIP-seq and NET-seq values of hda1D were divided by respective WT values in order to quantify the relative increase of H3 acetylation or nascent transcription in hda1D). The data showed a weak (Spearman rho= 0.23) but significant (pval=3.0e-20) positive correlation between the ratio values. The hda1D-dependent increase in H3 acetylation correlates with hda1D-dependent increase of RNAPII occupancy in DNC transcripts. We enhanced our representation of these data by including this plot as S5D in the revised manuscript as suggested.

(INSERT Rfig5)

RFig5__: Scatterplot of hda1D/WT NET-seq (y-axis) and ChIP-seq (x-axis) ratios. Each point corresponds to a bidirectional gene promoter overlapping with an NDR. The x-axis shows ChIP-seq ratios, and the y-axis shows the NET-seq ratios. These data support Spearman correlation test: rho = 0.234 and a statistically significant p-value = 3.0e-20.__

#3.6. In Figure 5, the authors argue that Hda1C works non-redundantly with K56ac, using point mutants to mutate K56 to A or Q. Did the screen identify anything else in the K56ac pathway? Rtt109 or Asf1, for example? Because Hda1C deacetylates H3, including but not limited to K56, it is a bit surprising the K56 point mutations result in a larger increase in SUT098-YFP levels. The authors discuss within the text that Hda1C has multiple targets; but coming back to my previous point that CAF-I was not supposed to impact this location, I am having a hard time understanding these results.

This is an excellent point. We improved the manuscript by highlighting other factors with links to H3K56ac in our scatter plots, for example Rtt109 in Fig 2A. Nevertheless, the reviewer may wish to satisfy his/her curiosity by exploring table S2 in more detail. Table S2 lists the top candidates from both screens.

We hope our answer to point #3.2 helped to clarify the aspect of this comment related to CAF-I.

**Minor comments**

#3.7. The authors follow up the screen using RTqPCR for GCG1/SUT098 in newly made deletion strains. I was surprised the authors choose this locus rather than the ORC2/SUT014 locus, as the screen showed a strong increase for this reporter. While I appreciate generating the deletion strains within the reporter is beyond necessary, assessing the endogenous locus within the deletion strains by RTqPCR seems reasonable.

We chose GCG1 locus since the fold change in directionality by genetic screen was high for the activator mutants. We will perform this experiment and add the missing validation experiment for the ORC2 locus in the revised manuscript.

#3.8. The authors tend to show their genomic data as metaplots; it would be nice to see heatmaps where more can be gleaned from the display of all the loci. This applies to the NET-seq data (Figure 3) and the ChIP-seq data (Figure 5).

We appreciate the suggestion and generated the requested heatmaps using the NET-seq tracks of WT and hda mutants (RFig6.). The heatmap represents the same genomic intervals as on the corresponding metagene plot (Figure 3A). We find that the differences between WT and hda samples are more clearly accessible at first glance on the metagene plot rather than on the heatmap. We believe that this could be because the heatmaps do not represent what transcripts have in common and rather underlines the differences. In contrast, the metagene plots reveal the common trends by taking the average of signal. We thus prefer showing metagene plots in the manuscript, as they allow for overlay of multiple tracks on the same plot, thus enhancing visual comparison for the readers.

(INSERT Rfig6)

RFig6. Heatmap representing NET-seq data in WT, hda1D and hda3D. Genomic intervals covering [TSS - 100 bp, TSS + 500 bp] of DNC transcripts (n=1517) are shown. The color indicates the log2-transformed NET-seq values.

#3.9. In Figure 5B, the authors present H3ac ChIP-seq data, presented as a ratio of H3ac/total H3. While this is a perfectly acceptable way to present the data, I was surprised to see a decrease in total H3 levels when examining the supplemental data. Has this decrease in H3 occupancy upon hda1 deletion been shown previously? This finding should be discussed within the manuscript.

We appreciate that the reviewer noticed this. We do not think this has been explicitly stated before, as the focus thus far had been on the effects towards the mRNA. However, the effect is not statistically significant between the WT and hda1D as observed in S5B. We thus prefer to remain cautious about this conclusion.

#3.10. In Supplemental Figure S3, the authors break down the NET-seq data by DNC FPKM, which is very nice. Very minor point that the font here is quite small.

Thanks, we improved the font size. Note that we also revised the y-axis scale in response to comment #1.4.

Reviewer #3 (Significance (Required)):

\*Significance:** *

The regulation of divergent non-coding RNAs is an understudied field. In this paper, the authors perform a screen for all non-essential yeast proteins in regulating the expression of these ncRNAs. The screen results and follow up defining the role of Hda1C in broadly repressing the expression of these ncRNAs is of interest to the field.

We are grateful to the reviewer for highlighting the interest of our work to the field.

\*Context:** *

This work follows from Marquardt's previous 2014 study that identify Caf1 as regulating DNCs in S. cerevisiae.

\*Audience:** *

Broadly, the chromatin and transcription field. Anyone interested in how chromatin regulates transcription, regulation of ncRNAs, and functions of histone modifying enzymes.

\*Expertise:** *

I am a member of the chromatin and transcription field, largely performing genomic experiments. We do not perform microscopy, although sufficiently understand the experiments and results presented here.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this manuscript, Gowthaman et al describe the results and follow up of their screen aimed at identifying regulators of divergent noncoding (DNC) transcription in S. cerevisiae. From this screen, they identify Hda1C as a repressor of DNC transcription, and perform follow experiments to support and detail this finding. In addition to RTqPCR to confirm the reporter and endogenous changes, the authors perform NET-seq to look at global DNC alteration upon Hda1C subunit deletion and identify a number of non-coding transcripts with altered expression levels. In addition, the authors perform live cell imaging to demonstrate that there is a modest restriction of initiation frequency when one of the subunits of Hda1C is deleted. Finally, the authors explore changes to pan-H3 acetylation and the genetic overlap between Hda1C and H3K56ac demonstrating independent genetic pathways, but overall increases in H3 acetylation over DNCs when Hda1C is deleted. Overall, the screen and results are of interest, but the authors overstate some of the conclusions (perhaps most importantly within the title!). I have the following suggestions to improve the manuscript:

Major comments:

1. The title of the manuscript is based on the single molecule live cell imagining experiments presented in Figure 4. While there is a statistically significant decrease in initiation frequency from deletion of one Hda1C subunit, there is no statistical decrease in deletion of the other two. Furthermore, these experiments were performed at one locus. As a result, I find the title to be an overstatement of the findings of the paper and suggest the authors refocus on the more robust findings of the manuscript.
2. Relatedly, in Figure 4, the authors present the findings from the single molecule live cell imaging experiments. Within this experiment, the authors include a cac2 deletion (CAF-1 subunit) strain, and observe a modest effect, similar to hda1 deletion. This is surprising as the authors mentioned this location (GCG1/SUT098) was selected as CAF-1 was NOT shown to regulate the DNC previously (Marquardt et al 2014; as mentioned at the beginning of the Results section). The similar decrease in initiation frequency between cac2 deletion and hda1 deletion further concerns me regarding the use of these data as the headlining finding.
3. It is unclear to me why the change in mRNA expression is included within the screen. Why not solely look at the expression change of the DNC? Importantly, the authors note in the discussion that perhaps the reason the SAGA complex was identified was due to regulating mRNA expression and not DNC expression and therefore was identified in the screen. Could the authors not just present the fold change in DNC expression using their YFP reporter, and not the YFP vs mCherry?
4. This is absolutely beyond the scope of the paper, but limiting the screen to only nonessential proteins likely misses important regulators. In the future, perhaps the authors could pursue a SATAY screen to look for essential proteins as well? Again, the findings of this paper are appropriate, and the screen is a great undertaking, but I want to suggest this to the authors for potential future projects.
5. The authors perform NETseq experiments in deletion strains and identify ~1500 DNC transcripts with altered expression. Later the authors look into the mechanism and demonstrate an increased H3ac in hda1 deletion strains. The authors could enhance the representation of these datasets by correlating the change in H3ac with the change in DNC transcription - do they correlate?
6. In Figure 5, the authors argue that Hda1C works non-redundantly with K56ac, using point mutants to mutate K56 to A or Q. Did the screen identify anything else in the K56ac pathway? Rtt109 or Asf1, for example? Because Hda1C deacetylates H3, including but not limited to K56, it is a bit surprising the K56 point mutations result in a larger increase in SUT098-YFP levels. The authors discuss within the text that Hda1C has multiple targets; but coming back to my previous point that CAF-I was not supposed to impact this location, I am having a hard time understanding these results.

Minor comments:

1. The authors follow up the screen using RTqPCR for GCG1/SUT098 in newly made deletion strains. I was surprised the authors choose this locus rather than the ORC2/SUT014 locus, as the screen showed a strong increase for this reporter. While I appreciate generating the deletion strains within the reporter is beyond necessary, assessing the endogenous locus within the deletion strains by RTqPCR seems reasonable.
2. The authors tend to show their genomic data as metaplots; it would be nice to see heatmaps where more can be gleaned from the display of all the loci. This applies to the NET-seq data (Figure 3) and the ChIP-seq data (Figure 5).
3. In Figure 5B, the authors present H3ac ChIP-seq data, presented as a ratio of H3ac/total H3. While this is a perfectly acceptable way to present the data, I was surprised to see a decrease in total H3 levels when examining the supplemental data. Has this decrease in H3 occupancy upon hda1 deletion been shown previously? This finding should be discussed within the manuscript.
4. In Supplemental Figure S3, the authors break down the NET-seq data by DNC FPKM, which is very nice. Very minor point that the font here is quite small.

Significance

Significance:

The regulation of divergent non-coding RNAs is an understudied field. In this paper, the authors perform a screen for all non-essential yeast proteins in regulating the expression of these ncRNAs. The screen results and follow up defining the role of Hda1C in broadly repressing the expression of these ncRNAs is of interest to the field.

Context:

This work follows from Marquardt's previous 2014 study that identify Caf1 as regulating DNCs in S. cerevisiae.

Audience:

Broadly, the chromatin and transcription field. Anyone interested in how chromatin regulates transcription, regulation of ncRNAs, and functions of histone modifying enzymes.

Expertise:

I am a member of the chromatin and transcription field, largely performing genomic experiments. We do not perform microscopy, although sufficiently understand the experiments and results presented here.

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Referee #2

Evidence, reproducibility and clarity

This reviewer considers himself a generalist with insight into chromatin-based gene regulation, but no first-hand experience with the yeast system or single-molecule imaging.

Promotors are frequently transcribed in both directions. The divergent, *upstream' transcript is frequently unstable. Transcription initiation is regulated through the acetylation of promoter-proximal nucleosomes, where HDAC-dependent deacetylation of histones typically represses transcription initiation. The current manuscript addresses the question whether initiation of coding and divergent, non-coding (DNC) transcription is regulated by the same factors. Previously Marquardt and others showed that H3K56ac-mediated histone exchange has a differential effect on coding and DNC transcription.

Using a clever reporter system, the authors screened for positive and negative regulators that preferentially affect DNC transcription. They discover the Hda1 deacetylase complex as a DNC-biased repressor and diverse HATs as DNC-biased activators. The role of activators could not be validated, presumably due to high variability of the system.

Focusing on Hda1c the authors present data suggesting a larger effect of Hda1c on 'upstream' nucleosomes associated with DNC transcription than in coding transcription. Genome-wide NET-seq mapping was consistent with this differential regulation. Life cell imaging of one specific case argues that Hda1-mediated repression reduced the time between initiation events. The authors employ state of the art methods and in general the data are of very good quality. The effect size is very small, which raises the broader question whether the results, while statistically significant is biological relevant. I have a few comments that the authors may use to revise their manuscript.

1) The differentially regulated coding and DNC transcription are defined by a directionality score. The screen was performed with two reporter loci that are strongly biased for DNC transcription (the idea to detect activators did not work out). Considering that coding and DNC transcription may not be totally independent because of the proximity of target nucleosomes, and sense and antisense transcription may compete for regulators, the question arises how levels of coding transcription affect DNC transcription in wildtype and mutants. The authors stratified their results according to levels of DNC transcription, but discussion and data analysis of the effect of coding transcription on the directionality score may be relevant.

2) The study is strong where the findings can be generalized. The single-molecule live-cell imaging analysis, while done properly, has only limiting impact, because the corresponding coding transcript could not be detected. This si more an anecdotal finding.

3) The effect size is small (20%, on average) and the variability is high. The fact that the HATs that emerged as very robust activators of DNC transcription could not be validated and that the Hda2 subunit of the HDAC complex was not found statistically significant show the limitations of the study. To their credit, the authors discuss these limitations appropriately.

4) Figure S3C suggests that the Hda effect is largest at genes that are poorly expressed, and smaller at more average expression levels. Are we looking at a phenomenon that mainly applies to repressed genes?

Minor issues

5) The NET-seq study involves two replicates. How well did they correlate?

6) For the live-cell imaging replicates were not mentioned. Were replicate studies performed?

7) Fig 4E is not mentioned in the text (mislabeled as 4D)

8) Fig S5 is not mentioned in the main text.

Significance

In summary, this is a high-quality study that presents the results of a genome-wide screen that will be of interest to colleagues in the narrower field. Due to the small effects the results may appeal less to a general readership.

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Referee #1

Evidence, reproducibility and clarity

In the paper by Gowthaman et al., the authors aim at better understanding the molecular mechanisms controlling divergent non-coding transcription (DNC). They describe a high-throughput yeast genetic screen using two strains in which two loci consisting of a coding and a divergent non-coding transcription unit (CGC1-SUT098 or ORC2-SUT014) were replaced by a bidirectional fluorescent reporter construct encoding mCherry in the coding direction and YFP in the non-coding direction. The two reporter strains were crossed with the yeast deletion library and mutants leading to increased or decreased YFP signal were selected as potential DNC repressors or activators. The two screens identified a number of common potential repressors and activators. Components of the Hda1C histone deacetylase complex were identified as DNC repressors in both screens. This phenomenon was confirmed genome-wide by performing NET-Seq in WT as well as hda1D and hda3D strains. This experiment allowed to identify 1517 DNC transcripts repressed by Hda1. Further analyses indicate that Hda1C represses DNC genome-wide independently of expression levels and that loss of Hda1 does not substantially affect coding transcription.

Live-cell imaging of transcription was then used to show that loss of Hda1 increases DNC transcription frequency rather than duration providing novel information on the link between DNC transcription initiation kinetics and chromatin regulation. Finally, using Chip-seq, the authors show that the level of acetylation over the divergent non-coding units is increased in the absence of Hda1 and some experiments suggest that H3K56 acetylation also contributes to DNC regulation, further strengthening the importance of elevated histone acetylation in efficient DNC.

Importantly, several components of the SWI/SNF chromatin remodeling complex were identified as activators confirming earlier observations (Marquardt et al., 2014). SAGA subunits were also among potential DNC activators, however these effects could not be confirmed through validation experiments. The authors conclude that DNC may be independent of specific activators and mainly due to transcriptional noise resulting from the adjacent NDR.

Overall this paper is very well structured, clearly written and the experiments are well controlled. The genetic screen identifies novel factors involved in the regulation of DNC. The study clearly demonstrates that the level of acetylation is a key regulator of divergent non-coding transcription and that histone deacetylation by Hda1 reduces the frequency of DNC initiation events. While this conclusion is strongly supported by the Net-Seq and Chip-seq metagene analyses, the fluorescence mCherry and YFP values or qRP-PCR analyses of specific genes do not always behave as expected when looking at absolute values rather than mCherry/YFP or GCG1/SUT098 ratios, which is sometimes disturbing when reading the paper. Therefore, the following points should be clarified.

Major points:

Figures 2 and S2A: Figures 2C and D show the mCherry/YFP fluorescence and GCG1/SUT098 RT-qPCR gene expression ratios respectively, which are consistent with a repressive effect of Hda1C on DNC transcription and a potential DNC activating effect of SAGA components. However, the absolute mCherry and YFP or GCG1 and SUT098 expression values presented in Figures S2A and S2B show the opposite: loss of Hda1C subunits rather leads to a decrease in mCherry with not much effect on YFP; moreover loss of Hda3 results in decreased SUT098, which is inconsistent with the whole model. The same comment is valid for the SAGA mutants. It would be good to provide some explanation for these a priori contradictory observations, especially for the Hda1c mutants, which are the major focus of the study. The Net-Seq analyses are certainly more reliable since less subject to protein or RNA stability effects, which may underlie some of the inconsistencies between protein and RNA absolute levels.

Figure 3: this figure examines the effect of Hda1 and Hda3 on the 1517 DNC transcripts. Does loss of this HDAC also increase the expression of all the other 2219 non-coding transcripts identified by Net-Seq, which would make Hda1C a more general repressor of non-coding transcription?

Moreover, does loss of Hda1 or Hda3 reveal DNC transcripts that were not detected in wild-type? This may increase even more the number of genes with divergent transcription.

Figures S3A, B, C: are the 3 groups of DNCs derepressed to the same extent by loss of Hda1 or Hda3? This is difficult to judge given the differences in y-axis scales. Figures S3D, E: the authors show the Net-Seq snapshots for the GCG1 and ORC2 loci. It would be good to add the quantifications as presented in Figure 3 for YPL172C and YDRr216C.

Figures S4A, B, C and D are not well explained. What does the y axis frequency correspond to? Is it the % of cells showing a signal? Is the intensity of SUT098 higher because the transcription initiation frequency is higher and therefore the transcription site signal is more intense?

Figures S4 A-I should be more specifically cited in the text.

Figure 5A: it is really unexpected and unclear why the mCherry/YFP in the WTH3/hda1D and WTH3/hda1D/H3K56mut is increasing compared to WTH3, since DNC is supposed to increase. Similar comment for Figure S5C. This should be clarified in the text.

More generally, as already mentioned above, the fluorescence data are expressed either as mCherry/YFP ratio or as absolute values. It would be good to systematically show the ratios and the absolute values of mCherry and YFP signal; the same for coding and DNC RT-qPCR as well as Net-Seq values when available.

Figures S5A and B are not referred to in the text. It should be mentioned and explained how normalization to H3 affects the levels of acetylated H3 over the NDR. p. 12 "Our data thus suggest to extend the transcriptional noise hypothesis with activities limiting DNC transcription to account for genome-wide variation in non-coding transcription".

If DNC is the result of "transcriptional noise", it is surprising that in the case of CGC1-SUT098, the transcription frequency is higher in the non-coding versus the coding direction. Is the SUT098 behaving like the coding unit in this case? The authors should comment on that.

Minor comments:

p. 4 should one talk about Hda1C-linked histone acetylation facilitates... (should be deacetylation...??) The authors should explain why they chose two coding/non-coding pairs that are cac2D insensitive and whether other criteria, such as level of DNC transcription, were also considered, since GCG1-SUT098 represents one of the most highly expressed divergent non-coding transcripts.

It is hard to understand why both the H3K56A and H3K56Q mutations lead to increased DNC, a result already presented in the Marquardt et al. 2014 paper. It would be helpful to provide a more extensive explanation or hypothesis.

What defines the level of DNC repression? How does the level of repression correlate with the level of coding transcription?

Significance

This is a very interesting and innovative study using cutting edge genetic approaches, genome-wide sequencing as well as single cell imaging to extend our understanding of non-coding transcription regulation and its potential impact on gene expression. It is a nice continuation and complement of an earlier study from the same author (Marquardt et al., 2014) and will certainly be of interest to a large chromatin biology audience.

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Reply to the reviewers

Point-by-point response:

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

**SUMMARY**

This MS tackles a largely unknown topic of vessel formation: how vessels anastomose and lumenise. The authors demonstrate that a matrix protein svep1 produced by neural tube during zebrafish embryogenesis plays a key role with blood flow to orchestrate anastomose formation. Actually in absence of this protein concomitantly with blood flow reduction results in significant decrease of lumenised DLAV segments.

In absence of svep1 they observed an expansion of apelin positive endothelial cells connected with a defect in tip/stalk cell specification. Interestingly the phenotype is amplified by blocking the kinase activity of VEGFR2

**MAJOR COMMENTS**

The most solid evidence on the role of blood flow in cooperating with svep1 relies on the use of tricaine, which reduces heart contractility. Interestingly the authors report some data by using embryo lacking cardiac troponin T2. In my opinion I suggest the author to better analyze the phenotype obtained by the deletion of svep1 together a dose-dependent reduction of tnnt2. This approach is more elegant and physiologic than the use of a chemical compound. Furthermore this approach will allow to better analyze the relations ship between blood flow and the expression of svep1 in neural tube. It should be relevant to establish a sort of flow threshold required to dampen lumenisation. *

Response: We appreciate the comment and have previously attempted to titrate the tnnt2 morpholino as published to have a graded reduction in blood flow. In our hands, this has not proved to be a robust approach, but we are willing to give it another try. In addition, we propose use alternative compounds to tricaine for blood flow reduction without affecting neural physiology. Alternatively we will use a-bungarotoxin mRNA injection to selectively affect neural activity to immobilize the embryos without effects on heart rate and blood flow (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4526548/)

To further improve the findings here reported I suggest to analyze the expression of klf2, which is a well known mechano-sensor of blood flow in several animal species including zebrafish.

Response: We will perform klf2 expression analysis

It's likely that apelin is relevant in the observed phenotype. Which is the phenotype of a double mutant lacking both apl and svep1? Is there a direct influence of blood flow on apl expression?

Response: We will investigate the double loss of function. However, double mutants would take some time, and a combination of morpholino and mutant would likely be the first and best option to answer this question in a reasonable time frame. The effect of flow on apl expression can be tested.

Is there any suggestion that this mechanism is oprative in mammalian?

Response: This is an interesting question and certainly relevant for follow up studies. At present, we can only speculate on a possible connection with flow, given that Svep1 mutations have recently been associated with artherosclerosis. However, whether the anastomosis defect we identify is conserved remains to be seen.

*Reviewer #1 (Significance (Required)):

The data here reported might represent a step forward in the field because a new mechanism is suggested.

The interest is sufficiently broad.

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

**Summary:**

The authors demonstrated that loss of svep1 in zebrafish contributed to defective anastomosis of intersegmental vessels, in addition, such Svep1 acted synergistically with blood flow to modulate vascular network formation in the zebrafish trunk.

**Major comments:**

The expression of svep1 is localized in neurons of neural tube, dorsal epithelial cells (as indicated by transgenic zebrafish) and ventral somite boundary (as indicated by in situ) but is excluded from endothelial cells nor the vasculature. It remains puzzling and the authors have not addressed this very reason of how a gene that is expressed in non-vascular tissue play a crucial role in vessel anastomosis, ie DLAV, ISV lumenization, during angiogenesis. As the entire story of this svep1 is related to its function in angiogenic sprout and lumen formation of vascular tissues, it will be helpful for reader to be able to put the pieces together of how such gene may be functionally involved in such angiogenic process. Previous publication of this gene involved in lymphoangiogenesis, as in this manuscript the authors could provide more evidence of how such gene and its localized expression contribute to different tissue in the vascular system, ie DLAV, instead of the neural tube, dorsal epidermis or ventral somite boundary.*

Response: We appreciate the wish to understand exactly how non-endothelial expression of Svep1 causes an endothelial phenotype selectively under reduced flow conditions. The very nature of this new phenotype requires analysis in vivo, and can not easily be transferred to an ex vivo assay. Therefore, selective loss of function in different cell populations is not easily available. More importantly, the interpretation of such efforts, when mosaic, are marred with issues. At this point, we feel that full molecular characterization of how Svep1 affects endothelial cells during anastomosis will require entirely new approaches and lies beyond what can be achieved in this manuscript.

We will however attempt to clarify the findings and the potential mechanisms in the discussion.

Another puzzling point is that tricaine is the center of the subject in this study. As the authors claim that tricaine-dependent blood flow reduction synergistically augmented the effect of svep1 deficiency. However, tricaine is known acting on neural voltage-gated sodium channels, whether svep1 function was affected by tricaine in the neural tissues and possibly its expression, the authors could provide more explanation and argument in the discussion.

Response: As mentioned in our response to reviewer 1, we will perform additional experiments to try to clarify whether an effect of tricaine on neuronal sodium channels contributes to the phenotype.

It is unclear on p12 "These results suggest that while svep1 loss-of-function produces a cardiac defect that enhances the effect of tricaine on reducing blood flow, svep1 has an additive effect in modulating blood vessels anastomosis" that svep1 deficiency enhances the effect of tricaine leading to reduced blood flow, however, it is not accurate to state that svep1 loss-of-function produces a cardiac defect. It is not sure if the effect of svep1 was actually neural rather than cardiovascular tissue, for example, tricaine acts on neural voltage-gated sodium channel that slowing down heart beat. Whether the authors can explore the possibility that svep1 function in neural rather than cardiovascular tissues, may be discuss why the authors think svep1 enhances the blood flow defect (tnnt2a knockdown or tricaine) on angiogenesis such as DLAV phenotype.

Response: We will attempt to dissect potential contributions by neural effects from cardiac and flow related effects as stated above. Tnnt2 MO and alternative drugs to reduce heart function selectively will be used. We will also clarify the discussion.

On p13, the authors stated that svep1 expression was inhibited by reduced blood flow, however, is it really the effect of reduced blood flow or caused by the chemical tricaine? If tnnt2a knockdown showed a similar phenotype, then it may be more convincing.

Response: see above

\*Minor comments:**

The work on "svep1 loss-of-function and knockdown are rescued by flt1 knockdown" was beautifully done and it is very clear and convincing.

The last two sections, "Vegfa/Vegfr signalling is necessary for ISV lumenisation maintenance and DLAV formation" and "Vegfa/Vegfr signalling inhibition exacerbates svep1 loss-of-function DLAV phenotype in reduced flow conditions" are more related to the flt1 knockdown phenotype. These 3 different sections are actually related in the sense that the rescue phenotype should be explained in the vegf signaling pathway. They are better off to discuss more cohesively about this vegf pathway that will help readers to appreciate more their work in svep1. *

Answer: We agree and will do so.

*Reviewer #2 (Significance (Required)):

This manuscript of svep1 in zebrafish provides new insight in angiogenesis, particularly in development of vessel anastomosis in zebrafish embryo, is very significant in the field and readers who are interested in angiogenesis and zebrafish development, including myself.

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

This manuscript reports that the secreted extra-cellular matrix protein Svep1 plays a role in vascular anastomosis during developmental angiogenesis in zebrafish. Further, the study demonstrates that flow and Svep1 modulate the vascular network in a synergistic fashion. This is a high quality manuscript presenting novel data which compellingly support the conclusions that are made. I have no suggestions for further experimentation but list minor points below.

1. The final paragraph of Discussion is underdeveloped in that it claims regulation of phenotypic robustness in angiogenesis and its failure promises crucial insights into the mechanisms causing breakdown of vascular homeostasis in human disease. However, this issue is not pursued in any substantial way in Discussion. For example, are there known mutations in humans which lead to anastomosis defects and, if so, do any of them relate to the molecules or signaling pathways which are the subject of this manuscript? *

Response: We agree with the wish to see more substantial discussion of the issue of phenotypic robustness and potential links to human disease. The question of anastomosis itself is something that has not been addressed in humans, as it is a rather detailed phenotype observable where predictive patterning occurs and can be dynamically studied. As such, there is a lack of literature and knowledge on signalling pathways that drive anastomosis in humans, and also not many that have been identified in experimental systems or animal models. Flt1 and Vegf signalling, junctional molecules and a few other pathways have been shown to be involved, but nothing is known so far about Svep1 and anastomosis in other system. We will attempt to complement the discussion to make this more clear.

• There are typographical errors in the text so a further proof-read is required. *

Response: thank you, these will be corrected

*Reviewer #3 (Significance (Required)):

This manuscript provides an incremental conceptual advance in our understanding of the molecular mechanisms responsible for vascular anastomosis during developmental angiogenesis. The manuscript will be of interest to developmental biologists and vascular biologists.

My field of expertise pertains to angiogenesis and lymphangiogenesis in the setting of cancer and other diseases. *I am not a developmental biologist.

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Referee #3

Evidence, reproducibility and clarity

This manuscript reports that the secreted extra-cellular matrix protein Svep1 plays a role in vascular anastomosis during developmental angiogenesis in zebrafish. Further, the study demonstrates that flow and Svep1 modulate the vascular network in a synergistic fashion. This is a high quality manuscript presenting novel data which compellingly support the conclusions that are made. I have no suggestions for further experimentation but list minor points below.

1. The final paragraph of Discussion is underdeveloped in that it claims regulation of phenotypic robustness in angiogenesis and its failure promises crucial insights into the mechanisms causing breakdown of vascular homeostasis in human disease. However, this issue is not pursued in any substantial way in Discussion. For example, are there known mutations in humans which lead to anastomosis defects and, if so, do any of them relate to the molecules or signaling pathways which are the subject of this manuscript?
2. There are typographical errors in the text so a further proof-read is required.

Significance

This manuscript provides an incremental conceptual advance in our understanding of the molecular mechanisms responsible for vascular anastomosis during developmental angiogenesis. The manuscript will be of interest to developmental biologists and vascular biologists.

My field of expertise pertains to angiogenesis and lymphangiogenesis in the setting of cancer and other diseases. I am not a developmental biologist.

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

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---

Referee #2

Evidence, reproducibility and clarity

Summary:

The authors demonstrated that loss of svep1 in zebrafish contributed to defective anastomosis of intersegmental vessels, in addition, such Svep1 acted synergistically with blood flow to modulate vascular network formation in the zebrafish trunk.

Major comments:

The expression of svep1 is localized in neurons of neural tube, dorsal epithelial cells (as indicated by transgenic zebrafish) and ventral somite boundary (as indicated by in situ) but is excluded from endothelial cells nor the vasculature. It remains puzzling and the authors have not addressed this very reason of how a gene that is expressed in non-vascular tissue play a crucial role in vessel anastomosis, ie DLAV, ISV lumenization, during angiogenesis. As the entire story of this svep1 is related to its function in angiogenic sprout and lumen formation of vascular tissues, it will be helpful for reader to be able to put the pieces together of how such gene may be functionally involved in such angiogenic process. Previous publication of this gene involved in lymphoangiogenesis, as in this manuscript the authors could provide more evidence of how such gene and its localized expression contribute to different tissue in the vascular system, ie DLAV, instead of the neural tube, dorsal epidermis or ventral somite boundary.

Another puzzling point is that tricaine is the center of the subject in this study. As the authors claim that tricaine-dependent blood flow reduction synergistically augmented the effect of svep1 deficiency. However, tricaine is known acting on neural voltage-gated sodium channels, whether svep1 function was affected by tricaine in the neural tissues and possibly its expression, the authors could provide more explanation and argument in the discussion.

It is unclear on p12 "These results suggest that while svep1 loss-of-function produces a cardiac defect that enhances the effect of tricaine on reducing blood flow, svep1 has an additive effect in modulating blood vessels anastomosis" that svep1 deficiency enhances the effect of tricaine leading to reduced blood flow, however, it is not accurate to state that svep1 loss-of-function produces a cardiac defect. It is not sure if the effect of svep1 was actually neural rather than cardiovascular tissue, for example, tricaine acts on neural voltage-gated sodium channel that slowing down heart beat. Whether the authors can explore the possibility that svep1 function in neural rather than cardiovascular tissues, may be discuss why the authors think svep1 enhances the blood flow defect (tnnt2a knockdown or tricaine) on angiogenesis such as DLAV phenotype.

On p13, the authors stated that svep1 expression was inhibited by reduced blood flow, however, is it really the effect of reduced blood flow or caused by the chemical tricaine? If tnnt2a knockdown showed a similar phenotype, then it may be more convincing.

Minor comments:

The work on "svep1 loss-of-function and knockdown are rescued by flt1 knockdown" was beautifully done and it is very clear and convincing.

The last two sections, "Vegfa/Vegfr signalling is necessary for ISV lumenisation maintenance and DLAV formation" and "Vegfa/Vegfr signalling inhibition exacerbates svep1 loss-of-function DLAV phenotype in reduced flow conditions" are more related to the flt1 knockdown phenotype. These 3 different sections are actually related in the sense that the rescue phenotype should be explained in the vegf signaling pathway. They are better off to discuss more cohesively about this vegf pathway that will help readers to appreciate more their work in svep1.

Significance

This manuscript of svep1 in zebrafish provides new insight in angiogenesis, particularly in development of vessel anastomosis in zebrafish embryo, is very significant in the field and readers who are interested in angiogenesis and zebrafish development, including myself.

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Referee #1

Evidence, reproducibility and clarity

SUMMARY

This MS tackles a largely unknown topic of vessel formation: how vessels anastomose and lumenise. The authors demonstrate that a matrix protein svep1 produced by neural tube during zebrafish embryogenesis plays a key role with blood flow to orchestrate anastomose formation. Actually in absence of this protein concomitantly with blood flow reduction results in significant decrease of lumenised DLAV segments.

In absence of svep1 they observed an expansion of apelin positive endothelial cells connected with a defect in tip/stalk cell specification. Interestingly the phenotype is amplified by blocking the kinase activity of VEGFR2

MAJOR COMMENTS

The most solid evidence on the role of blood flow in cooperating with svep1 relies on the use of tricaine, which reduces heart contractility. Interestingly the authors report some data by using embryo lacking cardiac troponin T2. In my opinion I suggest the author to better analyze the phenotype obtained by the deletion of svep1 together a dose-dependent reduction of tnnt2. This approach is more elegant and physiologic than the use of a chemical compound. Furthermore this approach will allow to better analyze the relations ship between blood flow and the expression of svep1 in neural tube. It should be relevant to establish a sort of flow threshold required to dampen lumenisation.

To further improve the findings here reported I suggest to analyze the expression of klf2, which is a well known mechano-sensor of blood flow in several animal species including zebrafish.

It's likely that apelin is relevant in the observed phenotype. Which is the phenotype of a double mutant lacking both apl and svep1? Is there a direct influence of blood flow on apl expression?

Is there any suggestion that this mechanism is oprative in mammalian?

Significance

The data here reported might represent a step forward in the field because a new mechanism is suggested.

The interest is sufficiently broad.

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Reply to the reviewers

We thank the reviewers for their comments, criticisms and suggestions that will help to improve the quality of our manusrcipt.

Please find enclosed in this initial response our answer to each point raised by the reviewers.

Please note that for several answers normally come along with an additional figure that could be added in the full revised version of the manuscript. However, these additional figures could not be added in the way we have to submit our answers but we are ready to send a pdf file including our answers with the additional figures upon request.

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

The paper by Genest et al. describes the effect of flotillins and sphingosine kinase 2 to stabilize AXL as a mechanism to promote epithelial-mesenchymal transition in breast (cancer) cells. The potential role of vesicles trafficking EMT-promoting proteins is of high interest in the field, also for exploring new opportunities of pharmacological targeting. However, the paper fails to convincingly demonstrate that the proposed mechanism is of real importance to support or promote EMT for the following main reasons:

1-a) The role of flotillins is studied only by overexpression and in the context of non-cancerous MCF10A cells, while breast cancer cells of epithelial-like origin are not analyzed.

Regarding the first part of the point raised here, we are not sure to understand correctly the sentence “[…] while breast cancer cells of epithelial-like origin are not analyzed”. Indeed, we used the breast cancer cell line MDA-MB-231 and a derived cell line that we generated by knocking down flotillin expression (MDA-MB-231shFlot2) in the second part of this study (Figure 6C, F and H and S7A, E and F). This previously characterized cell line allowed us to demonstrate that abolishing flotillin overexpression was sufficient to significantly inhibit the invasive properties of MDA-MB-231 cells (Planchon et al, J Cell Science 2018, https://doi.org/10.1242/jcs.218925

Although flotillin upregulation induces some major mechanisms of the EMT process in MCF10A cells, flotillin downregulation was not sufficient to reverse the EMT phenotype in MDA-MB-231 cells. This could be explained by the fact that EMT is a multifactorial process and that MDA-MB-231 cells went through too many irreversible changes leading to this process. By contrast, when we analyzed EMT markers after SphK2 inhibition or knock down in MCF10AF1F2 and in MDA-MB-231 cells (Figure 6A-C), we could observe a significant decrease in ZEB1 expression.

1-b) This is contrast with the purpose of the paper (see abstract, introduction, patients' data) which is to study tumors and EMT. Effect of shRNAs is also not reported, making it difficult to estimate the importance on the EMT phenotype.

As we mentioned in our manuscript, previous studies by other groups who downregulated flotillin expression in different cancer cell lines using siRNA approaches or re-expression of miRNAs that inhibit flotillin expression, already showed flotillin participation in EMT (for review please see, Gauthier-Rouvière et al, Cancer Metastasis Review, 2020, **doi: 10.1007/s10555-020-09873-y).

In this context, the novelty and the first goal of our study was to investigate how strong is the contribution of flotillin upregulation to EMT induction. To achieve this goal, we chose on purpose to use non-tumoral epithelial cells that do not harbor the anomalies already favoring EMT, unlike the cancer cell lines used in previous studies. In these non-tumoral models (the human MCF10A and mouse NMuMG mammary epithelial cell lines), we ectopically overexpressed flotillins (MCF10AF1F2 and NMuMGF1F2) to levels similar to what observed in invasive breast cancer cells. Using this approach, we found that flotillin overexpression is enough to induce EMT.

1-c) Then, alteration of EMT should be concluded also from other non-genetic functional parameters, not just by markers. For instance: was morphology of the cells changed? Was cell migration affected with F1F2?

Our conclusion that flotillin upregulation is sufficient to induce EMT in MCF10AF1F2 and NMuMGF1F2 cells is not based only on genetic functional parameters or markers. For instance, Figure S1 (panels H and I) shows a strong modification of the cell morphology and of the actin cytoskeleton organization in NMuMG cells upon flotillin upregulation. NMuMGF1F2 cells became flat and lost their apical F-actin belt and exhibited an increase in stress fibers.

As shown below (Additional Figure 1), similar modifications of the cell morphology and of the F-actin cytoskeleton organization occur also when flotillins are upregulated in MCF10A cells (see below the comparison of MCF10A and MCF10AF1F2 cells) (these data could be added in the manuscript).

ADDITIONAL FIGURE 1 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST

Additional figure 1: Upregulation of flotillins in MCF10A cells leads to changes in the cell morphology and in F-actin cytoskeleton organization. Comparison of the morphology and of the actin cytoskeleton organization in MCF10AmCh and MCF10AF1F2 cells. Confluent cells were fixed and stained for F-actin (green) using Alexa488-conjugated-Phalloidin and for nuclei (blue) using Hoechst (in panel A flotillin2-mCherry signal is shown). (A) Upper panels show the maximum intensity projection images (MIP) of MCF10AmCh (control) and MCF10AF1F2 (flotillin overexpression) cells obtained from a stack of images acquired by confocal microscopy. Lower panels show magnified images from the boxed areas, including one single plane and the x-z and y-z projections along the indicated axes. (B) 3D reconstruction images obtained from the region in the boxed area from the MIP-images shown in A.

These data show that in MCF10AF1F2 cells the apical actin belt is lost and the height of the cellular monolayer is lower compared with control MCF10AmCh cells.

We also analyzed the migration capacity of these cells (shown in Figure 3G of the submitted manuscript). Briefly, using a Boyden chamber assay, we showed that flotillin upregulation significantly increased migration of MCF10A cells (Figure 3G). We previously demonstrated that flotillin upregulation also promotes cell invasion in 3D using a spheroid assay (Planchon et al, J Cell Science, 2018, https://doi.org/10.1242/jcs.218925**). As shown below (Additional Figure 2), using a wound healing assay, we also observed that cell velocity is higher in flotillin-overexpressing NMuMGF1F2 cells than in control NMuMG cells (this could be added to the manuscript).

ADDITIONAL FIGURE 2 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST

Additional figure 2: Upregulation of flotillins in NMuMG cells increases cell velocity in a 2D migration assay. (A) Representative images of NMuMGmCh (control) and NMuMGF1F2 cells during wound healing. The yellow dashed line indicates the leading edge of the migrating monolayer at the indicated times. The trajectory of 60 individual cells was tracked and the cell velocity and persistence of migration were extracted. The histogram shows the velocity quantification (mean ± SEM of 4 independent experiments). (B) Representative trajectories of individual cells.

2) AXL up-regulation is not very strong (2-fold). What is unclear is if the minimal AXL increase due to F1F2 really provides a significant contribution to the EMT phenotype (as the authors conclude). The siRNA experiment knocks down all AXL, not just the F1F2-induced levels, making it difficult to estimate the real effect of the mechanism proposed.

As shown in figure 3A and D, in MCF10AF1F2 cells compared with MCF10AmCh cells, we measured a significant 2.5 ± 0.7-fold increase in the AXL protein level. We do not think that this can be considered as a minimal increase.

Considering that flotillin upregulation may affect simultaneously different receptors (Figure S2I, Figure S6A-F), we did not expect that downregulating a single receptor would have a major impact on the level of EMT markers and on cell migration. Yet, after knocking down AXL in MCF10AF1F2 cells, we observed a decrease in ZEB1 and N-cadherin expression and the re-expression of E-cadherin (Figure 3D-F) and the inhibition of cell migration (Figure 3G). The fact that we observed such an effect by downregulating AXL, which according to Reviewer #1 is minimally increased, might be explained by its well-known ability to act not alone but through cross-talk with other signaling receptors (Graham et al, Nature Reviews Cancer 2014; Halmos and Haura, Science Signaling 2016; Colavito et al, Journal of Oncology 2020).

As suggested by Reviewer #1, ideally, it would be interesting to bring back AXL to its level in MCF10AmCh cells to better evaluate only the contribution of its increase. However, adjusting so precisely the efficacy of AXL downregulation by siRNA seems quite difficult to achieve.

3) Why didn’t the author focus on EphA4 (or to a lesser extent ALK), which showed better regulation ?

As we mentioned (page 18) “the available tools allowed us to validate this result only for AXL, but not for EphA4 and ALK”**.

Nevertheless, for EphA4, we showed in Figure S6 that it is located in flotillin-positive late endosomes (Figure S6 A and C, for MCF10AF1F2 and NMuMGF1F2 cells, respectively) in a phosphorylated form (using an antibody against P-Y588/Y596-EphA4 that works in NMuMG cells, Figure S6D). However, the signals obtained by western blotting using the same antibody were too low to validate any significant variation of EphA4 Y-phosphorylation status, as suggested by the results from the phospho-RTK array.

Regarding ALK, the increase in its phosphorylation, suggested by the phospho-RTK array, remains puzzling to us. By western blotting of cell lysates and in the presence of positive controls, we did not detect any positive signal for phosphorylated ALK and even for total ALK in MCF10A and MCF10AF1F2 cells. In addition, to our knowledge, ALK expression in MCF10A cells has never been reported in the literature. These observations did not encourage us to pursue our investigations on ALK.

Moreover, several points led us to focus on AXL. Indeed, AXL expression is associated with the acquisition of a mesenchymal cell phenotype, invasive properties, and resistance to treatments and AXL is an attractive therapeutic target against which several inhibitors are in preclinical and clinical development (Shen Y et al. Life Sciences 2018). Moreover, AXL expression in tumors is attributed to post-transcriptional regulation, but the mechanisms are totally unknown. Understanding how its stabilization and signaling can be triggered by flotillin-mediated endocytic pathways is new and of high significance for the cancer field and the trafficking community.

3) The conclusions of the manuscript are contradicted by the reported clinical data. In Figure S4 the authors clearly observe co-expression of Flotillin 1 and AXL prevalently in luminal breast cancers, which is the subtype known to not be driven by EMT. This evidence already indicates that this (otherwise interesting) mechanism is not relevant to EMT in breast cancer. So, the conclusions are not supported by the data, and the experimental setup and model chosen are not appropriate to generalize the findings to cancer.

We acknowledge that flotillin 1/AXL co-expression is highest in the luminal subtype. If this co-expression was observed only in this particular subtype, we would have agreed that it excluded that flotillins and AXL co-overexpression may participate in EMT in tumor cells. However, our results show that flotillin 1 and AXL are co-expressed also in other subtypes that have undergone EMT. Considering this observation and the influence of flotillin upregulation on AXL overexpression we reported here, we believe that the point raised by the Reviewer is not sufficient to exclude that the co-upregulation of flotillins and AXL can participate in EMT induction in breast cancer cells.

**Minor (here the most important):**

4) The point of the Figure 2 is not clear. Why this part should have such a central role in the story? The entire data presented are not followed up in the rest of the paper. Moreover, in some cases upregulations also questionably significant (like RAS and STAT3 are not even 2 fold).

Moreover, the error bars are so small that it seems unrealistic that the plots indicate three independent experiments.

Because the activation of oncogenic signaling pathways is crucial to promote EMT, we think that analyzing these pathways in the context of flotillin upregulation is coherent with the message of the paper.

To our knowledge, the amplitude of up- or down-regulation has nothing to do with its significance. The amplitude also depends strongly on the context (stimulation with an agonist, overexpression of GEF, etc). For instance, increases lower than 2-fold are frequently reported (Bodin and Welch, Mol Biol Cell, 2005; Miura SI et al, Arteriosclerosis, Thromb and Vasc Biology, 2003; Matsunaga-Udagawa R et al, J Bio Chem 2010)** when assessing the activity of Ras or small GTPases, but they represent real upregulations. Furthermore, Ras activation is supported by the downstream 4-fold activation of ERK that we measured (Figure 2C).

In Figure 2, panels B, C, E, F and J, considering the amplitude of the mean increases shown, the error bars corresponding to SEM do not seem disproportionately small.

As the Reviewer seems to insinuate that we have not performed independent experiments, we are presenting in the table below the detailed results all obtained from independent experiments.

Panel

Parameter measured

Number of independent experiments

Fold of increase value in MCF10AF1F2 cells compared with MCF10AmCh cells in each experiment

Mean

SEM

p-value

B

Ras-GTP

5

1.95 ; 1.96 ; 1.18 ; 1.67 ; 1.86

1.72

0.14

0.001

C

Phospho- ERK

5

1.24 ; 5.43 ; 3.22 ; 6.11 ; 3.52

3.71

0.73

0.0042

E

Phospho-AKT

4

2.29 ; 6.54 ; 3.76 ; 2.6

3.8

0.97

0.0276

F

Phospho-STAT3

4

1.63 ; 1.63 ; 2.42 ; 1.60

1.82

0.20

0.0066

J

Phospho-SMAD3

8

4.1 ; 5.12 ; 6.29 ; 1.82 ; 2.58 ; 6.66 ; 2.82 ; 5.40

4.35

0.64

0.0001

In the legend to figure 2 panels C, E, F, J, “The histograms show […] with control MCF10AmCh **cells calculated from 4 independent experiments” was corrected by “The histograms show […] with control MCF10AmCh cells calculated from at least 4 independent experiments” as data shown in panel J were actually calculated from 8 independent experiments.

5) More robust statistical analysis should be provided in the Figure 1 to support that EMT is suppressed with F1F2 overexpression. For instance a more standard GSEA on hallmark signatures.

To avoid confusion, we understand that Reviewer #1 meant “… that EMT is induced with F1F2 overexpression” and not “… suppressed …”.

As recommended by Reviewer #1, we performed a GSEA on the hallmark signature and the results are already included in the current revised version of our manuscript (figure 1C).

6) In Figure 3 E-Cadherin is rescued with siAXL in the IF but not in the western blot.

Using siRNA transfection, we can have a mosaic effect due to the fact that not all the cells of the sample are transfected and thus efficiently knocked down. This mosaicism was clear when we analyzed E-cadherin by immunocytochemistry. Indeed, in some cells, probably the ones that have been more efficiently transfected with the AXL siRNA, E-cadherin expression is clearly seen. By western blotting, which provides a global analysis in which transfected and non-transfected cells are mixed, this was not significantly higher than in MCF10AF1F2 cells transfected with a control siRNA, although there was a trend towards increased E-cadherin expression in MCF10AF1F2 transfected with the AXL siRNA.

For the revised version of our manuscript we will try to improve the efficacy of the AXL siRNA and test whether we can fully rescue E-cadherin expression. The corresponding panel could be modified according to the data we will obtain.

7) Some sentences require clarifications. The authors should be more clear on why ZEB2 antibody was not available or what they mean with "Unfortunately the available tools..".

Page 7: we wrote «no anti-Zeb2 antibody is available». We should have said: «none of the anti-Zeb2 antibodies tested worked in MCF10A cells». We decided to remove “no anti-Zeb2 antibody is available” from the sentence to avoid confusion in the revised version of our manuscript.

Page 19: we wrote «unfortunately the available tools» to refer **the available tools against EphA4 and ALK that did not allow us to validate the data obtained using the phospho-RTK array showing that the Y-phosphorylation of these two RTK is increased in cells with upregulated flotillins. (see also our answer to major point 2).

8) Western blot from the CHX experiment should be shown, at least in the supplements. Again, the standard deviation in this experiment is minimal, was this really an average of three independent experiments (and not three western on the same lysates)?

As asked, a representative western blot is now shown in Figure 3C in the current revised version of the manuscript.

As indicated in the legend to the figure already in the initial version of our manuscript: “**The results are the mean ± SEM of 6 to 8 independent experiments depending on the time point, and are expressed as the percentage of AXL level at T0”. We wish to reassure Reviewer#1 that the results are really based on western blots performed on different lysates obtained in independent experiments. We can show the Reviewer these data obtained from independent experiments if necessary.

9) All conclusions are derived from one single cells MCF10a. NMuMG cells are shown at the beginning but not used for the rest of the paper. Anyway, if this wants to be a cancer research paper, then cancer cells needs to be used.

It is true that we did not use a cancer cell line at the beginning of the paper because, as expected, flotillin knock-down did not allow to revert the mesenchymal phenotype of MDA-MB-231 cells toward an epithelial one. If this had been obtained, we would have used these cells from the beginning of the paper. The lack of reversion of the mesenchymal phenotype after flotillin knock-down was expected. Indeed, the EMT process is multifactorial and the decrease of flotillins alone is obviously not sufficient to reverse it in a tumor cell line bearing multiple oncogenic mutations. Moreover, because we wanted to assess whether flotillin upregulation is sufficient in normal cells to acquire the properties of tumor cells and particularly to induce EMT, we used human MCF10A and murine NMuMG cells, two non-tumoral epithelial cell lines. Until now, the studies carried out on the effects of flotillin overexpression have used tumor cells that already harbor pro-oncogenic perturbations, preventing to show that flotillin overexpression alone activates oncogenic processes leading to EMT, and to identify the downstream mechanisms.

Nevertheless, we have used the MDA-MB-231 cell line in several experiments to analyze: i) AXL distribution and internalization following the knock-down of flotillins (Figures 4 and S5), ii) SphK2 and flotillin 2 co-localization and co-endocytosis (Figures 5A and D and S7A), iii) the impact of SphK2 inhibition on AXL expression level distribution and endocytosis (Figure 6), iv) SphK2 expression level upon flotillin knock-down (Figure S7E) and AXL expression level upon SphK1 inhibition (Figure S7F). With these experiments performed in MDA-MB-231 cells, we showed that AXL and SphK2 colocalize in flotillin-positive late endosomes and are co-endocytosed from the plasma membrane containing flotillin-rich domains to flotillin-positive vesicles. We also demonstrated that flotillins and SphK2 control the rate of AXL endocytosis and its stabilization.

We recently obtained additional data with HS578T cells, another triple negative breast cancer cell line, on the co-trafficking of AXL and flotillins as well as the co-trafficking of SphK2 and flotillins (Additional Figure 3, this data could be added in the fully revised version of our manuscript).

In addition, we observed that inhibiting SphK2 also decreased the level of AXL in HS578T cells. This data could be added in the revised version of the manuscript (see data in our answer to Point #1 from Reviewer #3).

• ADDITIONAL FIGURE 3 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST*

Additional figure 3: Co-trafficking of SphK2 and AXL with flotillin 1 in intracellular vesicles in HS578T cells. HS578T cells co-expressing Flot1-mCherry with SphK2-GFP (A) or AXL-GFP (B) were monitored by time lapse spinning disk confocal video-microscopy. On the right of each panel are shown still images at different time points (min) of the boxed area. The colored arrows allow following three distinct vesicles that are positive for Flot1-mCherry and Sphk2-GFP, or AXL-GFP.

10) The methods section contains inconsistent data about patients' samples (9 are indicated, but the Figure S4 features 37). Then, where those other 527 come from?

We corrected the manuscript and added all characteristics regarding the 37 patients in the “Supplementary information” section.

The 527 patients are from another cohort and were used for the analysis of the correlation between the mRNA levels of FLOT1 and p63 in breast cancer biopsies from 527 patients (Figure 2I). This cohort was described in our previous study (Planchon et al. J Cell Science 2018, https://doi.org/10.1242/jcs.218925). In the revised version of our manuscript, we now refer to this previous article in the “Result” section and in the legend to figure 2I to explain the origin and characteristics of this cohort.

11) Some figures do not match with the legends or with the description in the text. It has not been easy to review this paper.

We apologize as we indeed made one mistake in figure 2 that was inserted into the manuscript and that was actually figure S2 (that appeared twice). However, the correct figure 2 was uploaded on the website of Review Commons and BioRxiv. Regarding the comments made in point 4, it seems that Reviewer #1 examined the correct figure 2 that was uploaded and that matches the legend indicated in the manuscript.

Besides this mistake, we do not see any other mismatch between figures and legends.

Reviewer #1 (Significance (Required)):

I am a cancer biologist working on EMT.

**Referee Cross-commenting** I have nothing to comment on other's reviews.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): Genest and co-authors present in this paper new fascinating evidence on how intracellular trafficking can modulate oncogenic signalling.

First of all, they show how overexpression of Flotillin1 and 2 in non-cancerous breast lines can induce a strong reprogramming towards an EMT phenotype. They analyse mRNA and protein expression, intracellular distribution of activated proteins, cell phenotypes to demonstrate a strong activation of oncogenic signalling pathways. They then identify AXL as a key player in this process and show how this protein is stabilised upon Flotillin expression. The authors use an amazing variety of approaches to study the endocytosis and the trafficking of endogenous, GFP-tagged, Halo-tagged and Myc-tagged AXL in different cell lines and their data are strong and very convincing, the images are of very high quality and the analysis rigorous. Their data strongly support the hypothesis that high Flotillin levels triggers AXL endocytosis and accumulation in non-degradative late endosomes where signalling remains active. The authors then show how SphK2 has a key role in AXL stabilisation, it colocalises with Flotillin, AXL and CD63 and its activity (which they block by using inhibitors or siRNA) is necessary for flotillin-induced AXL stabilisation and EMT induction. The paper is extremely well written, the data flow logically and they are appropriately presented and analysed. I don't have any major comment and I believe the paper is suitable for publication.

We thank the Reviewer for the positive appreciation on our manuscript.

I have only some minor comments/questions: 1) did the authors try to colocalise AXL with endogenous Flotillin in MDA-MB-231 cells? They could use the antibodies used in Fig S1B. Of note, the authors have shown it in luminal tumours in Fig S4C.

We performed co-immunofuorescence experiments to detect endogenous AXL with endogenous Flotillin in MDA-MB-231 cells. As shown below (Additional Figure 4), we could find AXL and Flotillin being present in the same intracellular endosomes. Images could be added in the revised version of the manuscript.

ADDITIONAL FIGURE 4 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST

Additional figure 4: Endogenous AXL and flotillin 1 are found in the same in intracellular vesicles in MDA-MB-231 cells. MDA-MB-231 cells were fixed and labelled with relevant antibodies directed against Flotillin1 and AXL. Scale bar in the main image : 10 µm. Scale bars in the magnified images from the boxed area : 1 µm. Arrows indicate flotillin and AXL positives vesicles

2) In Fig6G, it appears that AXL-Flotillin colocalization is lost upon SphK2 inhibition. Is this the case? It could be that the correct lipids are necessary for the formation of Flotillin-positive internalisation domains and this could be very interesting and reinforce the model proposed in the paper.

In figure 6G, cells were not permeabilized. Thus, only AXL at the cell surface was labelled using an antibody against the extracellular domain of AXL. Because flotillin 2 is tagged with mCherry, this allowed its visualization revealing its localization both at the cell surface and intracellularly in the inset of the lower pane l of figure 6G.

After 6 hours of treatment using the opaganib inhibitor, we did not notice any major change in AXL-flotillin colocalization at the cell surface. Somehow, this is expected because blocking the generation of S1P is more likely to inhibit the invagination of flotillin-rich membrane microdomains rather than their formation.

3) I would remove the sentence on line 995-997 "to our knowledge this is the first report to describe ligand-independent AXL stabilization..." as the cells are not serum starved in all experiments and animal serum can contain variable amounts of the ligand GAS6.

We understand and agree with Reviewer #2, this sentence has been modified by “**To our knowledge this is the first report to describe AXL stabilization following its endocytosis”

Please note that the authors don't have to necessarily address comments 1-2, their paper is already very rich in convincing data.

Reviewer #2 (Significance (Required)):

AXL is a major oncogene that promotes EMT in a variety of tumour types. Understanding how its signalling can be triggered by endocytic pathways even in cells that are non-cancerous is very important and of high significance for the cancer field and the trafficking community.

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

This is an interesting and well written paper describing that upregulated flotillin promotes an endocytic pathway called upregulated flotillins-induced trafficking (UFIT) that mediates AXL endocytosis and allows its stabilization. Consequently, stabilized AXL in these flotillin-positive late endosomes enhances activation of oncogenic signaling pathways that promotes EMT. The authors suggest that Flotillin upregulation-induced AXL stabilization requires the activity of SphK2. However, this latter point is not supported by the data and further studies are needed to support this important conclusion.

**Major concerns:**

1. Most of the conclusions are based on effects of high concentrations (50 uM) of an ill-defined SphK2 inhibitor. The experiment described in Figure 6C-H need to be confirmed by downregulation of SphK2.

We understand that Reviewer #3 is concerned that in our experimental conditions, the effects we observed could be really explained by a specific inhibition of SphK2.

From the literature, among all the inhibitors described for SphK2, opaganib (ABC294640) is the most specific inhibitor available. It was shown to have no inhibitory effect on SphK1 up to 100 µM (French et al, J Pharmacol Experimental Exp Ther 2010; Neubauer HA and Pitson SM, The FEBS Journal 2013). In agreement, we found that PF543, the most specific SphK1 inhibitor, had no effect on AXL level (Figure S7F), unlike incubation with opaganib (Figure 6A and C), and that was confirmed in MCF10AF1F2 cells by the knock down of SphK2 with a specific siRNA (Figure 6B).

In the literature, depending on the cell lines, opaganib is used in vitro in the 10 to 60 µM range. Opaganib IC50 on recombinant SphK2 was established at 60 µM (French et al, J Pharmacol Experimental Exp Ther 2010). In our experiments, opaganib was used at a concentration of 50 µM, below the IC50 value, as previously done by Nichols’ group (Riento and al, PloS ONE, 2018). In most of our experiments (Figure 6, A, D, E-I, Figure S7D), opaganib was added for a maximum of 10 hours, which is shorter compared to what done in other studies (24-48 hours). Furthermore, it was shown that an opaganib concentration of 50 µM does not have any inhibitory effect in vitro on 20 protein kinases tested, including PKA, PKB, PKC, CDK, MAP-K, PDK1 and Src (French et al, J Pharmacol Experimental Exp Ther 2010).

In addition to inhibit SphK2, acting in a sphingosine-competitive manner, opaganib also was shown to act as an antagonist of estrogen receptor (ER), and inhibits ER-positive breast cancer tumor formation in vivo (Antoon JW et al, Endocrinology 2010). If Reviewer #3 is concerned about the possibility that the opaganib downstream effects we observed in our study might be explained by ER inhibition, we remind that we used cellular models that do not express ER. Indeed, the MDA-MB-231 cell line is a triple negative breast cancer cell line. MCF10A cells also do not express ER (Lane MA et al, Oncolgy Report, 1999,)** and our transcriptomic analysis (Table S1) did not reveal any increase in the expression of ER genes in MCF10AF1F2 cells in which flotillins are upregulated, thus eliminating a possible non-specific effect of opaganib in these cells.

In conclusion, we hope that these arguments help to convince Reviewer #3 that our experiments were performed in conditions where we carefully limited the possibility of opaganib off-target effects, on the basis of the currently available opaganib-related data from the literature.

We totally agree with Reviewer #3 that complementary experiments by downregulating SphK2 must be used. In agreement, we already downregulated SphK2 by siRNA in MCF10AF1F2 cells. This led to a significant decrease in AXL and ZEB1 expression. In the current revised version of the manuscript we have added data obtained with similar siRNA experiments performed in MDA-MB-231 cells (now Figure 6C). In agreement, we observed AXL and ZEB1 downregulation.

As shown below (Additional Figure 5) we recently obtained similar data in HS578T cells, showing that inhibiting SphK2 also affects AXL protein level in this triple negative breast cancer cell line (these data could be added in the manuscript).

ADDITIONAL FIGURE 5 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST

Additional figure 5: SphK2 inhibition decreases AXL level in HS578T cells. HS578T cells were incubated with opaganib (50µM, 10 hours) (A) or with siRNA Ctrl or siRNA SphK2 for 72 hours (B). Cell lysates were blotted with relevant antibodies against AXL, SphK2 and actin. The histograms show AXL level (normalized to actin) expressed as fold-increase compared with the control condition, and data are the mean ± SEM of 3 (A) and 4 (B) independent experiments.

Reviewer #3 also asks to use the siRNA approach on experiments shown in previous panels D-H (now panels E-I) of figure 6.

In complement to Figure 6D (now Figure 6E), experiments using a siRNA against SphK2 to show that “**AXL decrease upon SphK2 inhibition is not due to protein synthesis inhibition” are on-going and the obtained data could be added in the full revised version of our manuscript.

However, we are unfavorable to use a siRNA against SphK2, in addition to opaganib, in the experiments done to measure the effect of SphK2 inhibition on the rate of AXL internalization (previously in Figure 6E and F, now Figure 6F and G) and the level of AXL at the cell surface (previously in Figure 6G and H, now Figure 6H and I). Indeed, we carefully chose a short (4 hours) incubation with opaganib at the end of which the total cellular level of AXL was not yet decreased, allowing to measure unambiguously a defect in AXL endocytosis or a change in the level of AXL at the cell surface. We believe that it would be very difficult to achieve similar experiments using a siRNA against SphK2. It would require to determine the exact time after siRNA transfection leading to a sufficient SphK2 level reduction but in conditions where AXL level is still maintained. We think that due to the mosaic transfection efficiency, being able to precisely synchronize the effect of a siRNA at its beginning is impossible.

1. Does overexpression of SphK2 reverse the effects of the SphK2 inhibitor? In a similar manner, does overexpression of SphK2 enhance stabilization of AXL?

To answer the first question, it is not clear for us how to test whether SphK2 overexpression can reverse the effects of the SphK2 inhibitor because the ectopically expressed SphK2 would also be sensitive to the inhibitor. This would require to overexpress a SphK2 mutant that is catalytically active but insensitive to the inhibitor, and to our knowledge, such a mutant does not exist.

Regarding the second question, we are currently generating a retroviral DNA construct allowing to overexpress SphK2 homogeneously in the cell population. Then we will test whether it further increases AXL level through its stabilization. This will be tested in cells upregulated for flotillin. As we showed in Figure 6 A and D (previously Figure 6 A and C) that AXL level depends on SphK2 activity only in cells that overexpress flotillins, we anticipate that there will be no impact in a cell line with a moderate level of flotillin. Results could be added in the fully revised manuscript.

1. Although the authors suggest recruitment of SphK2 and formation of S1P in UFIT, there are no measurements of S1P. Also, there is no indication that SphK2 is activated despite the fact that ERK and AKT are activated in UFIT and are known to phosphorylate and activate SphK2. Is SphK2 that is recruited to flotillin phosphorylated?

To answer the first point raised by Reviewer#3, we recently performed, in collaboration with a lipidomic platform, a comparative analysis by quantitative mass-spectrometry of S1P levels between MCF10AmCh and MCF10AF1F2 cells. As we anticipated, the results show a 3,5-fold increase in S1P in MCF10AF1F2 cells compared with MCF10AmCh (Additional Figure 6). This data agrees with the fact that we found that the SphK2 catalytic activity is required for the UFIT pathway mediated AXL stabilization. This result is also in agreement with the study from the Nichols’ group which detect a decrease in S1P in cells in which flotillins were knocked out (Riento et al, PloS ONE, 2018). The results regarding the analysis of S1P level along with the complete methodology used will be added in the fully revised version of our manuscript.

ADDITIONAL FIGURE 6 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST

Additional figure 6: Upregulation of flotillins in MCF10A cells promotes an increase in the level of Sphingosine-1-phosphate. The level of sphingosine-1-phosphate was compared by quantitative mass-spectrometry analysis from three independent samples of MCF10AmCh and MCF10AF1F2 cells. The results are expressed in pmol equiv / 1 . 106 cells. The graph shows the value for each sample and the bar horizontal bars indicate the mean value for each condition.

Regarding the second point, we would like to clarify that we do not think that SphK2 interacts directly or indirectly with flotillins because SphK2 did not co-immunoprecipitate with flotillins (not shown). Thus, investigating by western blotting SphK2 phosphorylation status in flotillin immunoprecipitates is pointless. In theory, we could investigate the activity-related phosphorylation status of SphK2 associated with flotillin rich-membranes and endosomes. But this seems difficult to achieve because unfortunately, the only two commercially available antibodies against phosphorylated SphK2 are not described to work for immunofluorescence staining. One is against the Thr578 residue (https://www.abcam.com/sphk2-phospho-t578-antibody-ab215750.html), identified as phosphorylated downstream of ERK by Sarah Spiegel’s group (Hait et al, J Biol Chem, 2007). The second is designed to recognize specifically the phospho-Thr614 residue (https://www.abcam.com/sphk2-phospho-t614-antibody-ab111948.html), but this site has not been rigorously demonstrated to be phosphorylated downstream of AKT or ERK or to stimulate SphK2 activity. Thus, considering the lack of appropriate tools and considering that we already showed, using opaganib, that the catalytic activity of SphK2 is required for the UFIT pathway, we believe that investigating the phosphorylation status of SphK2 reflecting its activity in flotillin-positive vesicles will be complicated to achieve in a reasonable amount of time and we think that it will not bring a higher value to our present study.

To answer more broadly to the question “Is SphK2 recruited to flotillin phosphorylated?”, we anticipate that it could be the case at least on the Ser419 and Ser420 residues because Nakamura’s group demonstrated that the phosphorylation of these sites favors the nuclear export of SphK2 (Ding G et al, J Biol Chem, 2007). This group developed an antibody against these phospho-sites, potentially working by immunofluorescence. However, as it is unknown whether phosphorylation of these residues influences SphK2 activation status, we do not plan to perform immunofluorescence experiments with this tool (not available commercially) because the results would not address the Reviewer’s question.

1. It should be determined whether the optogenetic system used to induce flotillin oligomerization also induces recruitment and activation of SphK2.

As we already have all the available tools, optogenetic experiments will be performed to answer this point and the results could be added to the fully revised version of our manuscript.

As suggested, we plan to perform experiments in which exogenous S1P will be added to cells with a moderate flotillin expression level to check whether it could recapitulate the effect of flotillin upregulation on AXL expression. Results could be added to the fully revised version of the manuscript.

However, our current results on the localization and the involvement of SphK2 suggest that the generation of S1P involved in the UFIT pathway occurs at the plasma membrane and in late endosomes. Because the exogenous S1P that will be added in the culture medium will not go through the plasma membrane, we anticipate that it could be insufficient to mimic all the mechanisms of the UFIT pathway. Its effect will be limited to the plasma membrane. In addition, these mechanisms are very likely based on a local concentration of S1P in some microdomains (at the plasma membrane and in intracellular membranes) scaffolded by flotillins. It will be very difficult to mimic such local concentration of S1P just by adding S1P to the cells.

We agree that identifying the S1P receptors involved would be of valuable interest for a better characterization of the UFIT pathway. However, we think that this is beyond the scope of our present study. Among the five known S1P receptors, we do not know if any could be involved in membrane remodeling at the plasma membrane to promote endocytosis. To our knowledge, involvement of S1P receptors in endocytosis has never been reported. However, based on the work by Nakamura’s group (Kajimoto et al, Nat Comm, 2013 and Kajimoto et al, J Biol Chem, 2018), the S1P1 and S1P3 receptors are involved in membrane remodeling and cargo sorting from the outer membrane of late endosomes (where flotillins accumulate in our cell models). We could hypothesize that these receptors are influenced by flotillins and are involved in the UFIT pathway. But we think that testing this hypothesis would be the subject of a distinct study.

At the plasma membrane, we totally agree that the effect of S1P could be mediated, as suggested by De Camilli’s group (Shen et al, Nat Cell Biol 2014), by the formation of tubular endocytic structure rich in sphingosine after acute cholesterol extraction. Reciprocally, in our cell models, upregulated flotillins, thanks to their ability to bind to sphingosine (demonstrated by Nichols’ group (Riento et al, PloS ONE, 2018)) and to oligomerize, could create sphingosine-rich membrane regions.

1. There is a commercial antibody for endogenous SphK2 that can be used to validate and substantiate the data with GFP-SphK2. (F1000Res . 2016 Dec 6;5:2825. doi: 10.12688/f1000research.10336.2. eCollection 2016. Validation of commercially available sphingosine kinase 2 antibodies for use in immunoblotting, immunoprecipitation and immunofluorescence)

We thank Reviewer #3 for this suggestion and advice. Being able to detect the localization of endogenous SphK2 in late endosome would be valuable for our study. We already tried with no success with antibodies from Sigma and Cell Signaling Technology (not described to work in immunofluorescence experiments).

We will follow the advice from Reviewer #3 and test the anti-SphK2 antibody from ECM-Biosciences mentioned in the article by Neubauer and Pitson F1000 research, 2016. If we obtain interesting results, they will be included in the revised version of our manuscript.

However, in experiments using SphK2-GFP, we noticed that in live cells, the signal in late endosomes was completely lost after fixation using paraformaldehyde. Similarly, we also observed in live cells that NBD-Sphingosine, added in the culture medium, quickly accumulated in flotillin-positive late endosomes (Additional Figure 7, this data could be added in the fully revised version of the manuscript), but this accumulation was no longer detectable after fixation. Based on these observations, we believe that SphK2 recruitment to flotillin-positive late endosomes is highly labile probably because it mainly involves its interaction with sphingosine molecules that are enriched in these intracellular compartments. This is supported by our observation that addition of opaganib, characterized as a sphingosine competitive inhibitor, displaces SphK2-GFP from flotillin-positive late endosomes in live cells (Figure S7D). In addition, we showed that SphK2-Halo is more recruited in CD63-positive late endosomes in cells overexpressing flotillins (Figure 5E). This could be due to a higher concentration of sphingosine promoted by flotillins (that bind to sphingosine) accumulating in these compartments.

Thus, we will try the immunofluorescence staining of endogenous SphK2 using the recommended antibody, but it might be difficult to detect its presence in flotillin-rich late endosomes in fixed cells. The data could be added in the fully revised version of the manuscript.

ADDITIONAL FIGURE 7 CAN NOT BE ADDED BUT IS AVAILABLE UPON REQUEST

Additional figure 7: Visualization of NBD-sphingosine in flotillin-positive late endosomes. Live HS578T, MDA-MB-231 and MCF10AF1F2 cells expressing Flot1-mCherry were monitored by time lapse spinning disk confocal video-microscopy, 5 min after addition of fluorescent NBD-Sphingosine in the culture medium. On the right are shown still images corresponding to the boxed areas to illustrate the accumulation of NBD-sphingosine in virtually all flotillin-positive endosomes.

Reviewer #3 (Significance (Required)): This is an interesting paper. If the authors confirm the involvement of Sphk2 and mechanism of action of S1P, this would be an important contribution to the field.

Modifications done in the initial revised-version of our manuscript (at the time of the initial response). A full revised version will be provided after all the additional experiments asked by all the Reviewers will be achieved.

Revisions are highlighted in grey in the initial revised-version of the manuscript

1) Figure 1 has been modified and now includes results from a GSEA analysis as recommended by Reviewer #1. The texts of the corresponding legend and of the “Results” and “Methods” sections have been modified accordingly.

1) The Figure 2 version that was inserted in the manuscript was wrong because it was a copy of Figure S2. However, the correct Figure 2 was uploaded to the Review Commons website and accessible for the Reviewers. The correct Figure 2 is now inserted in the manuscript.

2) In the legend to panels C, E, F, J of Figure 2, the sentence: “The histograms show […] with control MCF10AmCh cells calculated from 4 independent experiments” was corrected to “The histograms show […] with control MCF10AmCh cells calculated from at least 4 independent experiments” because data shown in panel J are actually calculated from 8 independent experiments.

3) Figure 6 has been modified with the addition of panel C showing the effect of SphK2 downregulation by siRNA on AXL and ZEB1 level in MDA-MB-231 cells. The text has been modified accordingly.

4) In Figure 3 C, representative western blots have been added as asked by Reviewer #1.

5) In the Supplementary information section, the full clinicopathological characteristics of only 9 patients were indicated, whereas Figure S4 mentioned 37 patients. We corrected this mistake and now provide the characteristics of all patients.

6) In the sentence “Conversely, it induced ZEB 1 and 2 mRNA expression (Figures 1H and S1K) and ZEB1 protein expression (Figures 1I and S1L) (no anti-ZEB2 antibody is available)”, we removed “no anti-ZEB2 antibody is available”.

7) The sentence previously on line 995-997 "to our knowledge this is the first report to describe ligand-independent AXL stabilization..." has been modified to “**To our knowledge this is the first report to describe AXL stabilization following its endocytosis”

8) We are now referring to reference 18 (Planchon et al. J Cell Science, 2018) for the description of the cohort of 527 patients with breast cancer because this was missing.

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Referee #3

Evidence, reproducibility and clarity

This is an interesting and well written paper describing that upregulated flotillin promotes an endocytic pathway called upregulated flotillins-induced trafficking (UFIT) that mediates AXL endocytosis and allows its stabilization. Consequently, stabilized AXL in these flotillin-positive late endosomes enhances activation of oncogenic signaling pathways that promotes EMT. The authors suggest that Flotillin upregulation-induced AXL stabilization requires the activity of SphK2. However, this latter point is not supported by the data and further studies are needed to support this important conclusion.

Major concerns:

1. Most of the conclusions are based on effects of high concentrations (50 uM) of an ill-defined SphK2 inhibitor. The experiment described in Figure 6C-H need to be confirmed by downregulation of SphK2.
2. Does overexpression of SphK2 reverse the effects of the SphK2 inhibitor? In a similar manner, does overexpression of SphK2 enhance stabilization of AXL?
3. Although the authors suggest recruitment of SphK2 and formation of S1P in UFIT, there are no measurements of S1P. Also, there is no indication that SphK2 is activated despite the fact that ERK and AKT are activated in UFIT and are known to phosphorylate and activate SphK2. Is SphK2 that is recruited to flotillin phosphorylated?
4. It should be determined whether the optogenetic system used to induce flotillin oligomerization also induces recruitment and activation of SphK2.
5. Most importantly, it has not been established that the effects are mediated by S1P. Does addition of S1P enhance stabilization of AXL? Are the effects of S1P mediated by a S1P receptor? If so, which S1P receptor? There are several specific agonists and antagonists of S1PRs that can be utilized to answer this question. It's also possible that the effects of S1P are mediated by intracellular actions as were suggested by the De Camilli group (Nat Cell Biol. 2014 Jul;16(7):652-62).
6. There is a commercial antibody for endogenous SphK2 that can be used to validate and substantiate the data with GFP-SphK2. (F1000Res . 2016 Dec 6;5:2825. doi: 10.12688/f1000research.10336.2. eCollection 2016. Validation of commercially available sphingosine kinase 2 antibodies for use in immunoblotting, immunoprecipitation and immunofluorescence)

Significance

This is an interesting paper. If the authors confirm the involvement of Sphk2 and mechanism of action of S1P, this would be an important contribution to the field.

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Referee #2

Evidence, reproducibility and clarity

Genest and co-authors present in this paper new fascinating evidence on how intracellular trafficking can modulate oncogenic sigalling.

First of all, they show how overexpression of Flotillin1 and 2 in non-cancerous breast lines can induce a strong reprogramming towards a EMT phenotype. They analyse mRNA and protein expression, intracellular distribution of activated proteins, cell phenotypes to demonstrate a strong activation of oncogenic signalling pathways. They then identify AXL as a key player in this process and show how this protein is stabilised upon Flotillin expression. The authors use an amazing variety of approaches to study the endocytosis and the trafficking of endogenous, GFP-tagged, Halo-tagged and Myc-tagged AXL in different cell lines and their data are strong and very convincing, the images are of very high quality and the analysis rigorous. Their data strongly support the hypothesis that high Flotillin levels triggers AXL endocytosis and accumulation in non-degradative late endosomes where signalling remains active. The authors then show how SphK2 has a key role in AXL stabilisation, it colocalises with Flotillin, AXL and CD63 and its activity (which they block by using inhibitors or siRNA) is necessary for flotillin-induced AXL stabilisation and EMT induction.

The paper is extremely well written, the data flow logically and they are appropriately presented and analysed.

I don't have any major comment and I believe the paper is suitable for publication.

I have only some minor comments/questions:

1) did the authors try to colocalise AXL with endogenous Flotillin in MDA-MB-231 cells? They could use the antibodies used in Fig S1B. Of note, the authors have shown it in luminal tumours in Fig S4C.

2) In Fig6G, it appears that AXL-Flotillin colocalization is lost upon SphK2 inhibition. Is this the case? It could be that the correct lipids are necessary for the formation of Flotillin-positive internalisation domains and this could be very interesting and reinforce the model proposed in the paper.

3) I would remove the sentence on line 995-997 "to our knowledge this is the first report to describe ligand-independent AXL stabilization..." as the cells are not serum starved in all experiments and animal serum can contain variable amounts of the ligand GAS6.

Please note that the authors don't have to necessarily address comments 1-2, their paper is already very rich in convincing data.

Significance

AXL is a major oncogene that promotes EMT in a variety of tumour types. Understanding how its signalling can be triggered by endocytic pathways even in cells that are non-cancerous is very important and of high significance for the cancer field and the trafficking community.

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Referee #1

Evidence, reproducibility and clarity

The paper by Genest et al. describes the effect of flotillins and sphingosine kinase 2 to stabilize AXL as a mechanism to promote epithelial-mesenchymal transition in breast (cancer) cells. The potential role of vesicles trafficking EMT-promoting proteins is of high interest in the field, also for exploring new opportunities of pharmacological targeting. However, the paper fails to convincingly demonstrate that the proposed mechanism is of real importance to support or promote EMT for the following main reasons:

1) The role of flotillins is studied only by overexpression and in the context of non-cancerous MCF10A cells, while breast cancer cells of epithelial-like origin are not analyzed. This is contrast with the purpose of the paper (see abstract, introduction, patients' data) which is to study tumors and EMT. Effect of shRNAs is also not reported, making it difficult to estimate the importance on the EMT phenotype. Then, alteration of EMT should be concluded also from other non-genetic functional parameters, not just by markers. For instance: was morphology of the cells changed? Was cell migration affected with F1F2?

2) AXL up-regulation is not very strong (2-fold). What is unclear is if the minimal AXL increase due to F1F2 really really provides a significant contribution to the EMT phenotype (as the authors conclude). The siRNA experiment knocks down all AXL, not just the F1F2-induced levels, making it difficult to estimate the real effect of the mechanism proposed. Why didn't the author focus on EphA4 (or to a lesser extent ALK), which showed better regulation?

3) The conclusions of the manuscript are contradicted by the reported clinical data. In Figure S4 the authors clearly observe co-expression of Flotillin 1 and AXL prevalently in luminal breast cancers, which is the subtype known to not be driven by EMT. This evidence already indicates that this (otherwise interesting) mechanism is not relevant to EMT in breast cancer. So, the conclusions are not supported by the data, and the experimental setup and model chosen are not appropriate to generalize the findings to cancer.

Minor (here the most important):

4) The point of the Figure 2 is not clear. Why this part should have such a central role in the story? The entire data presented are not followed up in the rest of the paper. Moreover, in some cases upregulations also questionably significant (like RAS and STAT3 are not even 2 fold). Moreover, the error bars are so small that it seems unrealistic that the plots indicate three independent experiments.

5) More robust statistical analysis should be provided in the Figure 1 to support that EMT is suppressed with F1F2 overexpression. For instance a more standard GSEA on hallmark signatures.

6) In Figure 3 E-Cadherin is rescued with siAXL in the IF but not in the western blot.

7) Some sentences require clarifications. The authors should be more clear on why ZEB2 antibody was not available or what they mean with "Unfortunately the available tools..".

8) Western blot from the CHX experiment should be shown, at least in the supplements. Again, the standard deviation in this experiment is minimal, was this really an average of three independent experiments (and not three western on the same lysates)?

9) All conclusions are derived from one single cells MCF10a. NMuMG cells are shown at the beginning but not used for the rest of the paper. Anyway, if this wants to be a cancer research paper, then cancer cells needs to be used.

10) The methods section contains inconsistent data about patients' samples (9 are indicated, but the Figure S4 features 37). Then, where those other 527 come from?

11) Some figures do not match with the legends or with the description in the text. It has not been easy to review this paper.

Significance

I am a cancer biologist working on EMT.

Referee Cross-commenting

I have nothing to comment on other's reviews.

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Referee #3

Evidence, reproducibility and clarity

Recommendation: Publish after revisions

Duart and colleagues have put forth a manuscript detailing the under-appreciated effect of intrahelical salt bridge formation to the insertion transmembrane helices. Utilizing an in vitro and in vivo applicable construct of vehicle protein leader peptidase (Lep) from Escherichia coli, the authors were able to use glycosylation patterns as a way to quantify the apparent free energy of membrane insertion for multiple transmembrane helices. These results have demonstrated the importance of taking salt bridge formation into account when developing membrane protein prediction tools; however, prior to publication, further analyses would be beneficial for supporting their quantitative conclusions.

Major Comments:

• It would be helpful if the authors detailed their process in deciding which of the 136 potential salt bridge-containing helices were chosen for further investigations.
• Considering the data presented in Fig. 3c, it may be useful to also include charged pair mutations in the i, i+3 positions in the analyses of helix G and helix A, as these positions are the most likely to form salt bridges. This would act as a useful positive control, to see if the mutations would improve the insertion of the sequence.
• Page 14, Line 255: Authors state "The salt bridge contributes approximately ~0.5 kcal/mol to the apparent experimental free energy of membrane insertion." Can this change in apparent free energy be attributed completely to the mutation? Are there any potential interactions between the inserted helix and the natural H2 transmembrane sequence of Lep that could be changing with the various mutations?
• It is promising to see these results in the context of the Lep protein, but the authors should consider the effect these salt bridges may have in the context of the full protein. Creating mutants of Halorhodopsin or calcium ATPase would determine the impact of potential salt bridge disruption on protein folding, which would provide some context on the functional consequences of these mutations.
• Authors have presented a strong argument for the inclusion of potential salt bridge formation in the prediction of transmembrane helices; however, they have not detailed the necessary steps for developing a new system. It would be encouraging to see recommendations on the next steps towards better prediction software.

Minor comments:

• Page 8, Line 118: Authors state "Our results showed a tendency to better insertion when charge pairs were placed in positions (i, i+1; i, i+3; i, i+4) that are permissive with salt bridge formation (Fig. 1c), actually an effect not observed in the predictions (Fig. 1b)." It is important to clarify that this "better" insertion in Fig. 1c is compared to each respective predicted value in Fig. 1b. Currently, it reads as if the authors are suggesting the introduction of the charged pair residues is helping the insertion of the unaltered L4/A15 sequence.
• Figure 1a: Add cytoplasmic and lumen identifiers for clarity.
• Figure 3b: Slashes for "Opp charge" and "Same charge" in the legend appear to be reversed according to the values presented in Table 2.

Significance

This paper increases our understanding of salt bridges in membrane protein structure and function, as performed systematically by a lab with major expertise in this research area.

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Referee #2

Evidence, reproducibility and clarity

As the title states, Duart et al. have examined the energetic cost of the translocon-assisted insertion of TM helices containing salt bridges into membranes. The paper has three parts: (1) model studies using the methods of Hessa et al. (12,13), (2) statistical analysis of salt bridges in membrane proteins of known 3D structure, and (3) Hessa et al. measurements of selected i,i+4 salt-bridge containing TM helices from halorhodopsin (PDB ID = 3QBG) and calcium ATPase (1SU4). The major overall conclusion is that for i,i+4 salt bridges yield a more favorable insertion free energy of about 0.5 to 0.7 kcal/mol.

The subject of the paper is broadly interesting, but it suffers from several problems that must be addressed before it can be considered seriously for publication. The comments below are described in terms of the three parts.

(1) Figure 1b reports tabular values of predicted Hessa et al. DG values for sequences that contain K, D, or K & D substitutions in a parent L4A15 parent sequence, which has a favorable DG of about -0.5 kcal/mol. For all of the other sequences, DG is predicted to be unfavorable 1.4 kcal/mol to 3.5 kcal/mol. Figure 1c presents triplicate experimental measurements of DG for the sequences in Figure 1b shown as bar graphs. All of the sequences yield unfavorable DG values of about +0.2 kcal/mol except for the parent sequence that has a favorable value close to the predicted value.

There are several problems with these data and their presentation. Fig. 1b should also include the measured DGs with standard deviations in addition to the predicted values. In Fig. 1c, the positive values are plotted on different scale than the sole negative value. This causes the authors to insert a break in the bar representing the sole negative value. The bars are color coded in a mysterious way that is not clearly described in the figure legend. In any case, the measured DG values are all about the same.

A fundamental problem with the measurements is that the method of Hessa et al (12) should have been adhered to rigidly. As those authors noted "The quantification [of DG values]is maximally sensitive for H-segments with DGapp values close to zero (p < 0.5 in Fig. 1d); therefore, for each kind of residue we balanced the contribution from the central residue by varying the number of Leu residues until an H-segment with DG in the range -1.2 to 1.2 kcal/mol was found." The measurements reported Fig. 1b and 1c are far outside the maximum sensitivity range. The Western blots upon which the numbers are based should have been included (perhaps as an appendix).

(2) The statical analysis seems fine and is useful.

(3) Fig.4, halorhodopsin helix G measurements. The table of Fig. 4a should be expanded to include both in vitro (panel e) and in vivo data (panel f). It is not entirely clear where the values given in the table are from, but presumably from the in vitro data (panel e). Fig. 5, calcium ATPase helix A. Comments similar to those regarding Fig. 4 apply. The division of the long helix into a short greasy one and longer one carrying more charges is interesting, but it seems to add little to the main intent of the paper to assess the thermodynamic properties of helices containing salt-bridges.

Overall, the paper would be stronger if it focused mostly on the part (1) experiments to arrive at definitive answer to the energetics of salt-bridge insertion. As it stands, it is a smash up of ideas and experiments.

Significance

Surprisingly,there have been no reported measurements that I am aware that examine the energetic cost of inserting TM helices containing salt bridge into membranes. This paper is a start in that direction.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In the manuscript „Intra-helical salt bridge contribution to membrane protein insertion" the authors investigate the effect of salt bridge formation between positively and negatively charged amino acids on the insertion behavior of α-helical protein segments into the membrane. Generally it is believed that polar or even charged residues prevent stable membrane insertion of α-helical protein segments, but some of these authors had already shown in a previous paper that such residues are more frequent than expected in transmembrane helices. In the current study, the authors investigate in detail the role of intra-helical salt bridge formation on stable membrane insertion. Using an in vitro membrane insertion assay based on the E. coli leader peptidase (Lep) protein, they found better membrane insertion for helical segments with opposite charge pairs placed at positions compatible with intra-helical salt bridge formation (positions i→i+1; i→i+3 and i→i+4). Furthermore, the authors performed a database screen which revealed that oppositely charged residues are overrepresented at these positions. Finally they picked two candidate membrane proteins from the database (Halorhodopsin and calcium ATPase 1) and proved the presence of an intra-helical salt bridge and determined the contribution of the salt bridge to the apparent free energy of membrane insertion (ΔGapp), which was in the range of 0,5-0,7 kcal/mol.

Major comments

1. It seems that the data in Fig. 3b has been mixed up, making it difficult to judge the conclusions. The bars with forward slash seem to represent the "same charge" data and the bars with backward slash seem to represent the "opposite charge" data (exactly contrary to the figure legend). In general the forward and backward slash representation is not easily distinguishable, and for the position i+4 both bars contain a forward slash (making it impossible to discriminate same and opposite charge). Please use filled and unfilled bars instead. Furthermore the bar diagram in Fig. 3a is stacked for opposite and same charge, whereas in Fig. 3b the respective bars are placed next to each other. Additionally the label of the y-axis in Fig. 3c is misleading, as it is not the "Frac. of opp. charged pairs" but the fraction of oppositely charged pairs that form salt bridges.
2. The authors don´t give details no how the log odds ratios and the respective p-values have been determined. Please include this in the Materials and Methods section. What does a p-value of 0.00e+00 mean (see Table 2, Spacing: +3, "All Log odds")?
3. What is the proof that for the isolated helix A from the calcium ATPase 1 the membrane embedded part is identical to the full-length protein? The authors investigated two different helix A peptides, the full-length helix ranging from L49-F78, and one short fragment ranging from L49-A69 containing the more hydrophilic N-terminal region, which is the membrane-embedded region in the full-length protein. The authors state: "In contrast, when only the membrane-embedded sequence was included, the Lep chimera was mainly doubly-glycosylated (Fig. 5c, lane 3), suggesting that helix A is properly inserted when the full helical sequence is present." In my opinion this conclusion cannot be drawn from the data presented. The authors used an isolated helical segment, so in my opinion it is much more likely that the isolated full-length helix inserted via its hydrophobic C-terminal part (L60-F78) into the membrane. The authors themselves state in their manuscript: "It has been previously shown that the position in the membrane of TM helices in protein folded structures does not always correspond to the thermodynamically favored positions in the membrane of the isolated helices." Also the i→i+5 mutant points into that direction, because the effect of disturbing the intra-helical salt bridge for the helix A is much less pronounced compared to the similar data in Fig. 4f for the Halorhodopsin protein. In my opinion this shows that most probably only one charged residue (R63) is embedded inside the membrane (with a membrane embedded part of L60-F78).

Minor comments:

1. line 151: ",see Figure 2)" Typo: Bracket missing.
2. line 172: "Other known structural features can also be hinted at, including aromatic ring stacking by His-Trp pair [20] at i→i+6." Please give some more examples of important structural features of membrane proteins, which can be seen in your analysis (e.g. I think that also the glycine zipper can be seen in the i→i+4 data set).
3. line 255: "The salt bridge contributes approximately ~0,5 kcal/mol to the apparent experimental free energy of membrane insertion." Please explain that this value was derived from the comparison of the ΔGexp between the wt and the i→i+5 mutant. Please comment also on the large difference between the predicted (ΔGpred) and the experimental values (ΔGexp), even if no salt-bridge is involved (e.g. for the DD mutant).
4. line 348: "Asp-Lys pairs at position i, i+4 and Glu-Lys pairs at position i→ i+3 are the most prevalent as seen previously in Figure 2. They are both among the most prevalent oppositely charged pairs and the charged pairs that form the highest number of salt bridges in membrane protein structures. This is in stark contrast to Glu-Arg pair at position i→ i+1 that although as frequent in pairs as Asp-Lys and Glu-Lys at positions i→i+4 and i→i+3 respectively, only form salt bridges in one-fourth of the cases." Fig. 2 shows that each charge pair has a different prevalence depending on the order (e.g. Asp-Lys and Lys-Asp pairs). I think for this statement the sum of both prevalences should be taken into account, and as the sum is not easy discernible from Fig. 2, it would help to include a table containing the sums. Furthermore, it would be good to refer also to Fig. 3, which also contains a part of the discussed data.
5. line 402: "c-myc tag (Glu-Gln-Lys-Leu-Ile-Ser-Glu-Glu-Asp-Leu, EQKLISEEDL) was added in Ct in hanging with de PCR primer before cloning." Please revise the sentence and I think the one letter code for the c-myc tag is sufficient (please correct this also in line 428).
6. line 420: "A region's total ΔG is the sum of these individual scores weighted on where in the region the residue, a residue in the middle of the helix has a higher weight than residues at the ends." Please revise the sentence, the meaning is unclear.
7. line 436: "Total protein was quantified and equal amounts of protein submitted to Endo H treatment or mock-treated, followed by SDS-PAGE analysis and transferred into a PVDF transfer membrane (ThermoFisher Scientific)." Please revise the sentence.
8. line 498: "Topological files with sequence and membrane topology are created with the help of the RCSB secondary structure file and only membranes annotated as pure α-helices were retained." I assume that the description contains a typo (membranes annotated as pure α-helices?)
9. line 507: typo "..., but we did not clustered the proteins" 14: line 560: "The individual value of each experiment in represented by a solid dot being represented as a green square the experimental ΔG value for the L4/A15 sequence from [2]." Please revise the sentence. 15: line 562: "The wt and simple mutants are shown in white bars." Typo: single mutants 16: line 563: "Charges at compatible distances with salt bridge formation (i→i+1; i→i+3; and i→i+4) are shown in yellow. Not compatible distances with salt bridge formation (i→i+2; and i→i+5) are shown in dark gray. Compatible distances but not compatible amino acid pair (i, i+4 DD pair) is shown in clear gray." The given colors don´t match with the figure (i→i+1 = brown; i→i+3 = orange; i→i+4 = yellow and i→i+4 DD pair = white) 17: line 597: "The different monomers are shown in transparent blue, purple and indigo." The different colors are hardly distinguishable in the figure. 18: Figure 4a: The table could be simplified. I think the column "charges" can be removed, as it contains not really charges and the names of the peptides already contain the same information. The column "Å" contains only a value for the wt (and not for the DK i,i+5 mutant) and as the distance for the wt is also given in Fig. 4g, this column can be also removed.
10. Fig. 4f: The marker lane is hardly visible (completely dark lane)
11. Fig. 5b: The column "Å" contains only values for the wt sequences (long and short). See also comment 18.
12. Fig 5d: Why is in the SDS gel a mass shift between the wt and the i→i+5 mutant visible, even though the peptide mass is equal.
13. There are several changes of font type or format changes (e.g. line 210-214). Please correct this.

Significance

As a structural biologist with a focus on membrane-proteins, I understand that the study is concerned on intra-helical salt bridges, but the implications of inter-helical salt bridges should also be discussed, at least in the introduction or outlook. The authors propose that their results are important for the improvement of membrane protein topology prediction methods, so for this aim it is also necessary to take any potential inter-helical salt bridges into account. In this context, it would be relevant to point point out that there even exist extended rows of salt bridges between transmembrane segments (charge-zippers), which serve an important structural element in several membrane proteins.

The article is well written and most of the conclusions drawn from the experimental results are convincing. I agree with the authors that their results are relevant for future improvement of membrane protein topology prediction software, which so far does not take the possibility of salt bridge formation into account. Therefore, I recommend publication after clarification/revision of the abovementioned points.

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Reply to the reviewers

We thank the three reviewers for their helpful and valuable comments. We plan to address their criticisms in a revised manuscript and hope that our manuscript will then be significantly improved.

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

The authors have presented a very interesting and compelling set of data regarding the impact of conditional deletion of the only known pathway allowing the uptake of pyruvate into mitochondria. The paper comprises two interwoven stories that are both important. The first is the remarkable finding that the majority of excitatory neurons in the cortex (i.e. those under the influence of the CaMKII promoter) show remarkable metabolic flexibility as they tolerate elimination of pyruvate oxidation, considered the major supplier of ATP in neurons. The data on this seem clear although the authors did not delve into the potential mechanisms of metabolic compensation that likely occurs. Instead they examined whether there was some mal-adaptive compensation and they found clear evidence of this: in the absence of MPC activity the mice are much more prone to epileptic seizures, unveiled experimentally by relatively standard protocols (kindling). The authors present largely very convincing evidence that this mal-adaptive compensation in turn ends up decreasing the activity of KV7.2/7.3 channels whose job is normally to limit runaway repetitive firing by mediating an hyperpolarizing K+ efflux following an action potential. This channel, put on the map as it was one of the downstream targets modulated by cholinergic metabotropic activation, is also know known to be controlled by Calmodulin and therefore cytosolic Ca levels. Overall, I think at its core this manuscript is interesting and important. There however several weaknesses, I fear, will diminish the impact on the eventual readership. If these points can be addressed, it will strengthen the longevity of these findings:

1) It is puzzling why the authors resorted to using shRNA-mediated KD of MPC1 for some of the in vitro studies when they have gone to the trouble of making a floxed CRE-dependent mouse. Primary cells (e.g. Fig 1) or organotypic cultures (Fig. 6) from these mice would have made a more consistent set of starting conditions to compare data across the manuscript. As there viruses expressing the CRE recombinase are widely available this could have been used on mice simply harboring the floxed gene it they are worried about waiting for the expression of the CaMKII promoter for in-vitro conditions.

This is indeed a good point. Indeed initially, when we started these experiments, we tried to use viruses expressing the CRE recombinase in cultured neurons from mice harboring the floxed gene as proposed by the reviewer. However, for reasons that we do not fully understand, the use of AAVs or lentiviruses expressing the CRE was found to be deleterious for the cultured neurons. In view of this toxicity we tried using TAT-CRE recombinase, a recombinant cell-permeant fusion recombinase, which we added directly to the medium. However, this strategy proved to be poorly efficient. We finally used cultures of Cre-floxed neurons in which we tried to knockout MPC1 gene using 4-hydroxytamoxifen in the culture medium. However, we did not obtain satisfying results because, as previously reported, cortical neurons grow poorly in the presence of 4-hydroxytamoxifen (Nichols et al., Cell Death and Disease, 2018. https://doi.org/10.1038/s41419-018-0607-9). For these reasons we turned to the shRNA strategy and to the use of 3 small molecule inhibitors of the MPC each with different chemical structures. Both the RNA interference and the pharmacological approaches gave similar results, reinforcing our confidence in the specificity of the results, and the unlikelihood of off-target effects.

2) The data in Figure 5 gets a little less convincing as using extracellular glutamate to drive Ca elevations is so non-physiological that the results might really be distorted by the participation of something irrelevant to the story, even though it supports the overall interpretation for a role of Ca/CaM in the control of the channel. Similarly, the use of RU360 should be done with caution. The drug, although a useful antagonist of MCU in purified mitochondria, is famously finicky with respect to its ability to cross membranes and could well have off target impact. A much cleaner experiment would be to suppress the expression of MCU via KD. Presumably in the MPC-deficient neurons, this would have minimal impact on Ca signals. Given the frequent ambiguity associated with interpreting pharmacological results, coupled to the central importance of this finding in interpreting the entire paper, I think carrying out experiments with molecular genetic manipulation of MCU is warranted.

The main point of this figure is to study the capacity of MPC1 KO neurons to handle intracellular calcium increase and to regulate calcium homeostasis. To this end, we used strategies described to acutely increase cytosolic calcium, either through membrane depolarization with KCl (Rienecker et al., ASN Neuro. 2020. https://doi.org/10.1177/1759091420974807) or through activation of glutamate receptors using glutamate (For example see Wong, Vis Neurosci, 1995 : DOI: 10.1017/s0952523800009469). It is important to mention that the concentration of glutamate used in our experiments (10 microM for 2 min) is well below the concentration normally used to induce excitotoxicity (100-500 microM for 30min). The fact that both stimulations provided similar results and clearly indicated a defect in the clearance of cytosolic calcium in MPC-deficent neurons.

Regarding the concern with RU360, we are aware of the problems with plasma membrane permeability associated with this compound, and for this reason we included a membrane permeabilizer (0.02% pluronic acid) to facilitate its entry into the cell. This was indicated in the Material and Methods section (line 585) as well as in the figure legend (line 948). In order to clarify this methodology, we will add this information in the main text. It should be noted that this concern would not apply to the electrophysiogical experiments, since in this case the compound was injected directly into the cell. We would like to add that we chose to inhibit the MCU using a chemical inhibitor rather than a shRNA because of the well known difficulty in obtaining a complete loss of function of the MCU using RNA interference (Nichols et al., Cell Death and Disease, 2018. https://doi.org/10.1038/s41419-018-0607-9). Nevertheless, as recommended by the reviewer, we will attempt to downregulate the expression of MCU using shRNA.

3) The authors have not really made clear in this paper whether the ability to suppress the phenotype of the MPC deficiency with ketones is really related to a providing TCA cycle support or instead a pharmacological impact on non-TCA related targets (such as the Kv7.2/7.3 channels). Presumably the use of other ketones might circumvent this. The action of ketone bodies has been a topic of considerable interest in neuroscience, given the clinical relevance for childhood epilepsies. Previous studies for example have argued for direct inhibition of the vesicular glutamate transporter (Juge et al. Neuron 2010). The use of other ketones (acetoacetate) would narrow down the interpretations of the data.

Our results point to 2 two possible mechanisms of ketone bodies: i) providing acetyl-CoA to the Krebs cycle, thereby stimulating OXPHOS and ii) direct action of 3-beta hydroxybutyrate on the activity of Kv7/7.3 channels. The reviewer is asking whether, in addition to 3-beta hydroxybutyrate, other ketone bodies, acetone or acetoacetate, may display antiepileptic activity, which would probably indicate that providing substrates to the TCA cycle is sufficient to prevent neuron-intrinsic hyperactivity and seizures. We agree that this in an interesting question and we will now test the effect of acetoacetate on PTZ-induced seizures in MPC KO mice.

**other**

1) In vitro - scramble controls only serve to demonstrate there is no general effect of treating cells with shRNAs, but do not address if there is an off-target effect. The most convincing thing here would be to have an shRNA-insensitive variant that rescues.

We have used 2 different shRNAs and 3 chemically unrelated inhibitors of the MPC and in all cases we obtained similar results. Therefore, we think that it is unlikely that the effects we observe are due to an off-target activity. The experiment proposed by the reviewer is interesting but extremely difficult. The idea would be to reintroduce a shRNA-insensitive MPC1 into MPC1-deficient neurons treated with shRNA. This is difficult as it is known that the expression level of MPC1 needs to be matched to that of MPC2, otherwise it leads to depolarization of the mitochondria. Obtaining the right level of MPC1 would be extremely difficult to achieve in practice.

2) Does rescuing CaMK binding to KCNQ channels rescue the phenotypes?

The question raised by the Reviewer implies that CaM is not constitutively bound to KCNQ channels, which is a matter of debate. As we pointed out in the discussion, ‘Intracellular calcium decreases CaM-mediated KCNQ channel activity (32, 36) by detaching CaM from the channel or by inducing changes in configuration of the calmodulin-KCNQ channel complex (36).’ The CaM-KCNQ tethering is also described in a review by Alaimo and Villaroel, 2018 (doi:10.3390/biom80300579): ‘[…] CaM was first defined as an integral subunit constitutively tethered to the C-terminal region of Kv7.2/3 channels since Kv7.2 mutants that were deficient in CaM binding were unable to generate measurable currents [5,21]. However, this model has been questioned since Kv7.2 channels, carrying a hB mutation [40] or Kv7.4 hA mutated channels [41] that do not bind CaM, can still reach the plasma membrane and are functional.’

When considering to manipulate CaM binding to KCNQ, it should also be considered that previous studies on this matter have mainly worked with heterologous systems and through genetic manipulations of CaM (by expression of a dominant negative or by overexpression of CaM) or of the KCNQ binding motif.

Based on both theoretical and practical issues, we, thus, believe that it is not feasible to implement a straightforward approach that would be compatible with our mouse model.

An alternative, indirect approach, as indicated by Reviewer #3, would be to test the effect of Ca2+ chelators. Although this is likely to introduce confounding effects through the inhibition of other Ca2+-dependent channels, we propose to focus on trying this option and assess whether a XE991-sensitive component will be unmasked in MPC1 deficient cells.

3) As the authors imply that BHB activates KCNQ channels, showing this directly in their prep would provide some convincing data. If this is true, why doesn't BHB increase firing rate of WT neurons?

Activation of KCNQ channels is expected to reduce (not increase) neuronal firing. When exposed to BHB, we indeed found that WT cells also show a trend towards decreased excitability (p=0.08). We will report this trend in the revised figure 5F. Given that KCNQ channels are already available to be recruited upon repetitive firing in WT cells (to a larger extent as compared to KO, as indicated by our data with XE991) it is conceivable that a further potentiating effect of BHB at the concentration used for ex vivo recordings (2 mM) will be limited.

4) How does the anti-epileptic effects of ketones in this study relate to previous reports of regulation of KATP channels? One of main concerns is that ketones might have a parallel anti-epileptic effect in the MPC1 KO mice that is unrelated to the mechanism proposed here.

The ketogenic diet is likely to exert several effects including disruption of glutamatergic synaptic transmission, inhibition of glycolysis, and activation of ATP-sensitive potassium channels as pointed out by the reviewer. We do not exclude that inhibition of the MPC could also have an impact on the KATP channels and we are currently exploring this possibility. However, such work to dissect the potential implication of the KATP channels would go well beyond the scope of the present paper. Nevertheless, we will plan to certainly raise this important possibility in the discussion.

**Minor comments:**

1- What is the MPC1 KO efficiency in CaMK neurons? The western blot in 2c is from the whole cortex and therefore does not show that.

This is indeed a good comment, however, please note that the estimation of MPC1 KO efficiency has also been evaluated in synaptosomes isolated from MPC1 KO cortices. These structures are mainly isolated from neurons (Carlin et al., JCB, 1980. 10.1083/jcb.86.3.831). As shown in figure 2C, these synaptosomes are massively enriched for CamKII and contain less astrocytic marker GFAP in comparison to the whole cortex. The amount of MPC1 in the synaptosomes prepared from the KO animals is strongly decreased. Nevertheless, as recommended by the reviewer, we plan to quantify the efficiency of the KO by performing a double immunostaining for MPC1 and a specific marker for neurons.

2- Mitochondrial Ca2+ levels are not measured directly, for which there are many tools. This is needed to demonstrate definitively that there is a defect in Ca2+ handling."

The reviewer raised an important point and we plan to monitor the levels of mitochondrial calcium in MPC-deficient neurons using the mito-Aequorin, a luminescent quantitative probe targeted to mitochondria (Granatiero et al., Cold Spring Harb. Protoc. 2014. 10.1101/pdb.top066118)

Reviewer #1 (Significance (Required)):

see above.

**Referee Cross-commenting**

It seems we are in reasonable agreement about the pros & cons of the manuscript. I agree that alternative approaches to RU360 are warranted.

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

De la Rossa and colleagues examined the consequences of conditionally knocking out MPC1,a subunit of the mitochondrial pyruvate carrier. They found that despite decreased levels of oxidative phosphorylation in excitatory neurons, phenotypically these conditional knockout mice were normal at rest. However, when challenged by inhibition of GABA neurotransmission, these animals developed severe seizure activity and expired. These authors then showed that neurons with an absence of MPC1 were hyperexcitable in part through abnormal calcium homeostasis, which was associated with a reduction in M-type inhibitory potassium channel activity. Intriguingly, the ketogenic diet and the major ketone body beta-hydroxybutyrate were able to reverse these changes.

This is a carefully conducted research study that reveals cell type-specific alterations of MPC1 deletion and functional consequences. The study design was logical and involved an exhaustive array of methodologies. The manuscript was generally well written and organized, and there are no major concerns. This study shows a direct causal relationship between impaired bioenergetics at the level of mitochondrial, and subsequent behavioral seizures, and is perhaps the most direct demonstration to date that an intrinsic disturbance of metabolic function can result in seizure activity (through changes in calcium regulation and impairment of ion channel activity). This will be an important contribution to the scientific literature.

**MINOR:**

1. Page 4, line 86: Would recommend changing "paroxystic" to "paroxysmal" (the latter which is a more recognized term). We will make the change.

Page 5, line 124: recommend including the concentration of beta-hydroxybutyrate used when first mentioned. In general, concentration and dose information were difficult to find, as well as route of administration (for kainate, page 7, line 175). This type of information was not conveniently presented.

We will follow the reviewer’s recommendation.

Page 5, line 128: "both overcomed" is awkward. Would recommend using "both reversed".

We fully agree and will make the change in the revised manuscript.

Page 8, line 193: the authors probably meant "astro-MPC1-WT mice", not "neuro-MPC1-WT mice".

Thank you for the acurate look. This will be changed.

Page 12, lines 280-282: the authors might want to mention that chronic exposure of BHB might reduce the hyperexcitability of neuro-MPC1-KO mice.

This point could indeed be discussed.

Please review entire manuscript and use consistent tense. For example, on page 13, line 309, to maintain the past tense, it should read "We first assessed whether..."

Thanks for the recommendation.

Page 13, line 318: the authors used 10 mM BHB when examining calcium levels, but they earlier used 2 mM. They need to explain why they used a different concentration; and 2 vs 10 mM are quite different.

The reviewer makes a valid point. When we performed the in vitro experiments, we used 10 mM BHB, which is slightly higher than the amount of ketone bodies measured in the blood of mice fed on a ketogenic diet for 2 days (Supplementary figure 4). This concentration of BHB has also been used by others (see for example: Izumi et al., JCI 1998, 101:1121-1132). Later on, when electrophysiology experiments were performed, the person in charge of these experiments followed a previously published protocol by Yellen and colleagues, in which the authors had used 2 mM BHB (Ma et al., J. Neurosci 2007,27: 3618-3625). This explains the differences between the concentrations used in vitro and in vivo.

Page 13, line 323: it is not necessary to say "...interesting study published during the preparation of this manuscript." This phrase should be deleted, and the relevant reference simply cited.

We will follow the reviewer’s recommendation.

The authors need to explain more clearly in the beginning what exactly is meant by "paradoxical" hyperactivity. They provide greater meaning later in the manuscript, but this should be clarified at the outset.

We will explain why we used this adjective in the beginning as recommended by the reviewer.

Reviewer #2 (Significance (Required)):

This is a very important study to show how primary defects in metabolism (i.e., disruption of the mitochondrial pyruvate carrier) can lead to epilepsy. Moreover, it details a primary mechanism that connects cellular bioenergetics to membrane excitability (through changes in calcium homeostasis and M-current function).

This is a well-conducted study that utilizes a multiplicity of experimental tools to link biochemistry with seizure activity. This type of study is not so readily done, and strengthens the notion that primary defects in metabolism can result in epileptic seizures.

This study is unique and attempts successfully to be more than just correlational. Hence it is a valuable contribution to the field.

The audience will likely consist of metabolic geneticists, neurologists/epileptologists, and neuroscientists. This is a beautiful study that runs the translational spectrum from biochemistry to behavior.

My expertise is in the field of translational epilepsy research, with a focus on mitochondria, metabolism, the ketogenic diet and ketone bodies. Thus, I am qualified to critically evaluate the entire manuscript.

**Referee Cross-commenting**

After reading comments and reviewing the manuscript again, would agree with Reviewer #1, and would change recommendation to MAJOR REVISION.

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

This manuscript tests the genetic requirement of the mitochondrial pyruvate carrier (MPC) in regulation of neuronal excitability. The authors find that MPC deficiency in glutamatergic neurons is associated with aerobic glycolysis, inhibition of the M-type K channels, and neuronal hyperexcitability that manifests in increased sensitivity to chemical pro-convulsants without changes in resting conditions. Alterations in Ca homeostasis in MPC-deficient neurons is consistent with reduced mitochondrial membrane potential and attendant diminution of mitochondrial calcium buffering capacity. The authors further show that the effect of MPC deficiency can be phenocopied by treatment of wild type neurons with a chemical inhibitor of the mitochondrial Ca uniporter (MCU). Based on these data, it is proposed that reduced mitochondrial Ca uptake causes neuronal hyperexcitability in the absence of MPC. Overall, the manuscript presents detailed electrophysiology and in vivo seizure studies. However, there is significant disconnect between the actual data in Fig. 6 and the authors' conclusions/proposed mechanism. In particular, the evidence for the role of Ca in the hyperexcitability due to MPC deficiency is the weak link in the authors' argument.

1. The studies linking reduced mitochondrial Ca uptake to hyperexcitability in MPC-deficient neurons (Fig. 6) have several limitations that significantly weaken the paper: 1a. The Ca measurements in cortical neurons (Fig. 6A-F) are performed under conditions (glutamate/KCl) that are fundamentally different from those used in electrophysiology of CA1 pyramidal neurons (Fig. 6G-N). The electrophysiological excitation is much briefer and less extreme than the chemical stimulation, and it is not clear that the Ca dysregulation occurs at the earliest times (see Fig. 6A).

This point was also raised by reviewer 1. Please see our response to point 2.

1b. The conclusion that MCU is functionally responsible for MPC's effect on neuronal excitability is singularly based on the use of RU360 as a chemical inhibitor of MCU but the specificity of this reagent is questionable. Evidence for a cause and effect relationship that directly implicates altered MCU/mitochondrial Ca buffering has not been provided.

This accurate point was also raised by the reviewer 1. Please see our response to point 2 for a complete response. We will downregulate expression of MCU using shRNAs. We will also measure the mitochondrial calcium level in the hope of better understanding whether the phenotype of the MPC-deficient mice is due to impaired mitochondrial calcium uptake.

1c. There is a large variation in the effect of 10 uM RU360 on firing frequency, comparing Fig. 6H and N (blue traces), including the shape of the traces and values at ramp number 6. This calls into question the reliability of the comparisons in each separate figure.

Data presented in each single graph in the main Figures were obtained from groups of littermates through recordings conducted in consecutive days. Some caution is warranted when comparing data between different figures (i.e. between different experimental series), as several factors may contribute to inter-experiment variability, including variability between different batches of animals. However, the difference pointed out by the reviewer regarding the values of cell firing reported in Fig. 6H and N is only apparent. When applying depolarizations with ramps of 5s, a fair amount of WT cells infused with RU-360 show high instantaneous firing frequency, especially for the last ramps that steeply reach high current levels. This leads to accommodation/inactivation of the action potential towards the end of the ramps, as shown in the example trace in Fig 6G. As a result, the current-frequency plot deviates from linearity, as it is the case in Fig 6H (blue trace) and, even more evidently, in Fig 6N. We have now reanalyzed the same recordings from WT cells infused with 10 µM RU-360 and measured the firing frequency in response to a square depolarizing step (250 pA) of 0.5 or 1 second. No difference was found between the firing frequencies of the cells from Fig 6H and Fig. 6N (group 1 and group 2, respectively, in the figure below). Although the ramps may lead to some distortion for higher stimulation levels, we have decided to show results from ramps consistently throughout the main figures because this protocol with continuously increasing currents allows us to measure more precisely the rheobase and the firing threshold (as opposed to the stepwise increments of a square stimulation).

1d. The calcium > PIP2 > M-type K+ channel axis is well established but has not been fully explored in the context of MPC deficiency. The use of a calcium chelator will likely be informative in this context, and would be better evidence for a role of Ca in the MPC effects.

Although the use of a Ca2+ chelator such as BAPTA is likely to introduce confounding effects through the inhibition of other Ca2+-dependent channels, we will try this option and assess whether a XE991-sensitive component will be unmasked in MPC deficient cells.

1e. The ability of BHB to rescue various parameters in this and other figures in the paper is interesting but does not directly speak to the specific mechanism as to how MPC deficiency affects neuronal excitability. BHB's effect is consistent with the metabolic flexibility of neurons when the TCA cycle cannot be fueled by glucose/pyruvate (as in GLUT1 or MPC deficiency).

The mechanism we propose to explain the hyperexcitability of MPC-deficient neurons relies on the low mitochondrial membrane potential and their decreased capacity to buffer calcium. Based on our data, we propose that calcium accumulation in the cytosol disrupts the CaM-KCNQ interaction leading to hyperexcitability. Indeed, BHB could act in two possible (and parallel) ways. 1: directly on the M-type channels, 2. on mitochondria by providing acetylCoA to the TCA cycle. The use of an alternative ketone body will be informative in disentangling these two possibilities.

The manuscript (and the field) will benefit from a more scholarly discussion and integration of published literature:

2a. The published studies on the outcome of pharmacologic MPC inhibition in neurons (Ref 18, Divakaruni et al.) are not only consistent with the bioenergetic effect in Fig. 1, but more importantly, show that interference with MPC does not lead to broad deficiencies in energy metabolism but rather remodel fuel utilization patterns to alternative substrates that feed the TCA cycle (BHB, leucine, etc). For this reason, terms such as "mitochondrial dysfunction" and "OXPHOS deficiency" used throughout the manuscript to describe MPC deficiency are vague and imprecise. In addition, this metabolic flexibility may explain lack of defects under resting conditions. In light of these considerations, the argument as to whether aerobic glycolysis in MPC-deficient neurons explains the lack of phenotype in resting conditions (p 17) seems one-sided. Overall, the studies in ref 18 are relevant to the current manuscript and should be better integrated in the discussion.

We fully agree with the possibility that the rewiring of cell metabolism in MPC-deficient neurons in the presence of leucine, BHB and other metabolites could explain the lack of phenotype in resting conditions. We thank the reviewer for this highly relevant comment which we will include in the revised discussion.

2b. Several references are cited to describe the role of OXPHOS vis-à-vis aerobic glycolysis in neuronal function. At times, however, the authors' statements are not consistent with what these papers actually show (or do not show). For example, see the use of refs 6 and 44 on p17 of the discussion, where the authors state that aerobic glycolysis uncoupled from OXPHOS is sufficient to provide ATP for normal neurotransmission, but this does not mean OXPHOS is not needed.

We agree that these references are not appropriate here and they will be removed.

2c. Although the XE991 experiments support an important role for the M-type channels in the altered excitability with deficiency, it is not clear that the proposed mechanism can explain all of the electrophysiological differences, particularly those resting properties that are measured without a Ca challenge to the neurons. It would be good to discuss other possible mechanisms that could affect neuronal excitability.

Our results point to M-type channels as important players in the phenotype of the MPC-deficient mice. Previous reports indicate that inhibition of this channel by XE991 can modulate input resistance, membrane potential and firing threshold of pyramidal cells (e.g. Shah et al, 2018, doi/10.1073/pnas.0802805105; Hu et al. 2007, DOI:10.1523/JNEUROSCI.4463-06.2007; Petrovic et al., 2012, doi:10.1371/journal.pone.0030402). We also found that XE991 induced a shift towards more negative potentials in the firing threshold of WT cells, but not in MPC1 deficient cells (-3.3±0.6 vs. -0.4±1.0, n=9, 8, p=0.027). However, we agree with the reviewer that the phenotype is probably highly complex and that additional mechanisms may contribute to modulate the intrinsic excitability of MPC-deficient neurons. One such mechanism could be closure of KATP channels, which we are currently investigating. This will be discussed.

Reviewer #3 (Significance (Required)):

The significance of the advance: The studies provide genetic evidence for the role of MPC in neuronal excitability.

The work in the context of existing literature: Please see specific comments above under point 2 regarding the need for a scholarly discussion and integration of existing literature.

Audience that might be interested: mitochondrial bioenergetics and metabolism and metabolic control of neuronal excitation.

Keywords describing expertise: metabolism, mitochondria and electrophysiology.

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Referee #3

Evidence, reproducibility and clarity

This manuscript tests the genetic requirement of the mitochondrial pyruvate carrier (MPC) in regulation of neuronal excitability. The authors find that MPC deficiency in glutamatergic neurons is associated with aerobic glycolysis, inhibition of the M-type K channels, and neuronal hyperexcitability that manifests in increased sensitivity to chemical pro-convulsants without changes in resting conditions. Alterations in Ca homeostasis in MPC-deficient neurons is consistent with reduced mitochondrial membrane potential and attendant diminution of mitochondrial calcium buffering capacity. The authors further show that the effect of MPC deficiency can be phenocopied by treatment of wild type neurons with a chemical inhibitor of the mitochondrial Ca uniporter (MCU). Based on these data, it is proposed that reduced mitochondrial Ca uptake causes neuronal hyperexcitability in the absence of MPC. Overall, the manuscript presents detailed electrophysiology and in vivo seizure studies. However, there is significant disconnect between the actual data in Fig. 6 and the authors' conclusions/proposed mechanism. In particular, the evidence for the role of Ca in the hyperexcitability due to MPC deficiency is the weak link in the authors' argument.

1. The studies linking reduced mitochondrial Ca uptake to hyperexcitability in MPC-deficient neurons (Fig. 6) have several limitations that significantly weaken the paper:

1a. The Ca measurements in cortical neurons (Fig. 6A-F) are performed under conditions (glutamate/KCl) that are fundamentally different from those used in electrophysiology of CA1 pyramidal neurons (Fig. 6G-N). The electrophysiological excitation is much briefer and less extreme than the chemical stimulation, and it is not clear that the Ca dysregulation occurs at the earliest times (see Fig. 6A).

1b. The conclusion that MCU is functionally responsible for MPC's effect on neuronal excitability is singularly based on the use of RU360 as a chemical inhibitor of MCU but the specificity of this reagent is questionable. Evidence for a cause and effect relationship that directly implicates altered MCU/mitochondrial Ca buffering has not been provided.

1c. There is a large variation in the effect of 10 uM RU360 on firing frequency, comparing Fig. 6H and N (blue traces), including the shape of the traces and values at ramp number 6. This calls into question the reliability of the comparisons in each separate figure.

1d. The calcium > PIP2 > M-type K+ channel axis is well established but has not been fully explored in the context of MPC deficiency. The use of a calcium chelator will likely be informative in this context, and would be better evidence for a role of Ca in the MPC effects.

1e. The ability of BHB to rescue various parameters in this and other figures in the paper is interesting but does not directly speak to the specific mechanism as to how MPC deficiency affects neuronal excitability. BHB's effect is consistent with the metabolic flexibility of neurons when the TCA cycle cannot be fueled by glucose/pyruvate (as in GLUT1 or MPC deficiency).

1. The manuscript (and the field) will benefit from a more scholarly discussion and integration of published literature:

2a. The published studies on the outcome of pharmacologic MPC inhibition in neurons (Ref 18, Divakaruni et al.) are not only consistent with the bioenergetic effect in Fig. 1, but more importantly, show that interference with MPC does not lead to broad deficiencies in energy metabolism but rather remodel fuel utilization patterns to alternative substrates that feed the TCA cycle (BHB, leucine, etc). For this reason, terms such as "mitochondrial dysfunction" and "OXPHOS deficiency" used throughout the manuscript to describe MPC deficiency are vague and imprecise. In addition, this metabolic flexibility may explain lack of defects under resting conditions. In light of these considerations, the argument as to whether aerobic glycolysis in MPC-deficient neurons explains the lack of phenotype in resting conditions (p 17) seems one-sided. Overall, the studies in ref 18 are relevant to the current manuscript and should be better integrated in the discussion.

2b. Several references are cited to describe the role of OXPHOS vis-à-vis aerobic glycolysis in neuronal function. At times, however, the authors' statements are not consistent with what these papers actually show (or do not show). For example, see the use of refs 6 and 44 on p17 of the discussion, where the authors state that aerobic glycolysis uncoupled from OXPHOS is sufficient to provide ATP for normal neurotransmission, but this does not mean OXPHOS is not needed.

2c. Although the XE991 experiments support an important role for the M-type channels in the altered excitability with deficiency, it is not clear that the proposed mechanism can explain all of the electrophysiological differences, particularly those resting properties that are measured without a Ca challenge to the neurons. It would be good to discuss other possible mechanisms that could affect neuronal excitability.

Significance

The significance of the advance: The studies provide genetic evidence for the role of MPC in neuronal excitability.

The work in the context of existing literature: Please see specific comments above under point 2 regarding the need for a scholarly discussion and integration of existing literature. Audience that might be interested: mitochondrial bioenergetics and metabolism and metabolic control of neuronal excitation.

Keywords describing expertise: metabolism, mitochondria and electrophysiology.

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Referee #2

Evidence, reproducibility and clarity

De la Rossa and colleagues examined the consequences of conditionally knocking out MPC1,a subunit of the mitochondrial pyruvate carrier. They found that despite decreased levels of oxidative phosphorylation in excitatory neurons, phenotypically these conditional knockout mice were normal at rest. However, when challenged by inhibition of GABA neurotransmission, these animals developed severe seizure activity and expired. These authors then showed that neurons with an absence of MPC1 were hyperexcitable in part through abnormal calcium homeostasis, which was associated with a reduction in M-type inhibitory potassium channel activity. Intriguingly, the ketogenic diet and the major ketone body beta-hydroxybutyrate were able to reverse these changes.

This is a carefully conducted research study that reveals cell type-specific alterations of MPC1 deletion and functional consequences. The study design was logical and involved an exhaustive array of methodologies. The manuscript was generally well written and organized, and there are no major concerns. This study shows a direct causal relationship between impaired bioenergetics at the level of mitochondrial, and subsequent behavioral seizures, and is perhaps the most direct demonstration to date that an intrinsic disturbance of metabolic function can result in seizure activity (through changes in calcium regulation and impairment of ion channel activity). This will be an important contribution to the scientific literature.

MINOR:

1. Page 4, line 86: Would recommend changing "paroxystic" to "paroxysmal" (the latter which is a more recognized term).
2. Page 5, line 124: recommend including the concentration of beta-hydroxybutyrate used when first mentioned. In general, concentration and dose information were difficult to find, as well as route of administration (for kainate, page 7, line 175). This type of information was not conveniently presented.
3. Page 5, line 128: "both overcomed" is awkward. Would recommend using "both reversed".
4. Page 8, line 193: the authors probably meant "astro-MPC1-WT mice", not "neuro-MPC1-WT mice".
5. Page 12, lines 280-282: the authors might want to mention that chronic exposure of BHB might reduce the hyperexcitability of neuro-MPC1-KO mice.
6. Please review entire manuscript and use consistent tense. For example, on page 13, line 309, to maintain the past tense, it should read "We first assessed whether..."
7. Page 13, line 318: the authors used 10 mM BHB when examining calcium levels, but they earlier used 2 mM. They need to explain why they used a different concentration; and 2 vs 10 mM are quite different.
8. Page 13, line 323: it is not necessary to say "...interesting study published during the preparation of this manuscript." This phrase should be deleted, and the relevant reference simply cited.
9. The authors need to explain more clearly in the beginning what exactly is meant by "paradoxical" hyperactivity. They provide greater meaning later in the manuscript, but this should be clarified at the outset.

Significance

This is a very important study to show how primary defects in metabolism (i.e., disruption of the mitochondrial pyruvate carrier) can lead to epilepsy. Moreover, it details a primary mechanism that connects cellular bioenergetics to membrane excitability (through changes in calcium homeostasis and M-current function).

This is a well-conducted study that utilizes a multiplicity of experimental tools to link biochemistry with seizure activity. This type of study is not so readily done, and strengthens the notion that primary defects in metabolism can result in epileptic seizures.

This study is unique and attempts successfully to be more than just correlational. Hence it is a valuable contribution to the field.

The audience will likely consist of metabolic geneticists, neurologists/epileptologists, and neuroscientists. This is a beautiful study that runs the translational spectrum from biochemistry to behavior.

My expertise is in the field of translational epilepsy research, with a focus on mitochondria, metabolism, the ketogenic diet and ketone bodies. Thus, I am qualified to critically evaluate the entire manuscript.

Referee Cross-commenting

After reading comments and reviewing the manuscript again, would agree with Reviewer #1, and would change recommendation to MAJOR REVISION.

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Referee #1

Evidence, reproducibility and clarity

The authors have presented a very interesting and compelling set of data regarding the impact of conditional deletion of the only known pathway allowing the uptake of pyruvate into mitochondria. The paper comprises two interwoven stories that are both important. The first is the remarkable finding that the majority of excitatory neurons in the cortex (i.e. those under the influence of the CaMKII promoter)show remarkable metabolic flexibility as they tolerate elimination of pyruvate oxidation, considered the major supplier of ATP in neurons. The data on this seem clear although the authors did not delve into the potential mechanisms of metabolic compensation that likely occurs. Instead they examined whether there was some mal-adaptive compensation and they found clear evidence of this: in the absence of MPC activity the mice are much more prone to epileptic seizures, unveiled experimentally by relatively standard protocols (kindling). The authors present largely very convincing evidence that this mal-adaptive compensation in turn ends up decreasing the activity of KV7.2/7.3 channels whose job is normally to limit runaway repetitive firing by mediating an hyperpolarizing K+ efflux following an action potential. This channel, put on the map as it was one of the downstream targets modulated by cholinergic metabotropic activation, is also know known to be controlled by Calmodulin and therefore cytosolic Ca levels. Overall, I think at its core this manuscript is interesting and important. There however several weaknesses, I fear, will diminish the impact on the eventual readership. If these points can be addressed, it will strengthen the longevity of these findings:

1) It is puzzling why the authors resorted to using shRNA-mediated KD of MPC1 for some of the in vitro studies when they have gone to the trouble of making a floxed CRE-dependent mouse. Primary cells (e.g. Fig 1) or organotypic cultures (Fig. 6) from these mice would have made a more consistent set of starting conditions to compare data across the manuscript. As there viruses expressing the CRE recombinase are widely available this could have been used on mice simply harboring the floxed gene it they are worried about waiting for the expression of the CaMKII promoter for in-vitro conditions.

2) The data in Figure 5 gets a little less convincing as using extracellular glutamate to drive Ca elevations is so non-physiological that the results might really be distorted by the participation of something irrelevant to the story, even though it supports the overall interpretation for a role of Ca/CaM in the control of the channel. Similarly, the use of RU360 should be done with caution. The drug, although a useful antagonist of MCU in purified mitochondria, is famously finicky with respect to its ability to cross membranes and could well have off target impact. A much cleaner experiment would be to suppress the expression of MCU via KD. Presumably in the MPC-deficient neurons, this would have minimal impact on Ca signals. Given the frequent ambiguity associated with interpreting pharmacological results, coupled to the central importance of this finding in interpreting the entire paper, I think carrying out experiments with molecular genetic manipulation of MCU is warranted.

3) The authors have not really made clear in this paper whether the ability to suppress the phenotype of the MPC deficiency with ketones is really related to a providing TCA cycle support or instead a pharmacological impact on non-TCA related targets (such as the Kv7.2/7.3 channels). Presumably the use of other ketones might circumvent this. The action of ketone bodies has been a topic of considerable interest in neuroscience, given the clinical relevance for childhood epilepsies. Previous studies for example have argued for direct inhibition of the vesicular glutamate transporter (Juge et al. Neuron 2010). The use of other ketones (acetoacetate) would narrow down the interpretations of the data.

other

1) In vitro - scramble controls only serve to demonstrate there is no general effect of treating cells with shRNAs, but do not address if there is an off-target effect. The most convincing thing here would be to have an shRNA-insensitive variant that rescues.

2) Does rescuing CaMK binding to KCNQ channels rescue the phenotypes?

3) As the authors imply that BHB activates KCNQ channels, showing this directly in their prep would provide some convincing data. If this is true, why doesn't BHB increase firing rate of WT neurons?

4) How does the anti-epileptic effects of ketones in this study relate to previous reports of regulation of KATP channels? One of main concerns is that ketones might have a parallel anti-epileptic effect in the MPC1 KO mice that is unrelated to the mechanism proposed here.

Minor comments:

1- What is the MPC1 KO efficiency in CaMK neurons? The western blot in 2c is from the whole cortex and therefore does not show that. 2- Mitochondrial Ca2+ levels are not measured directly, for which there are many tools. This is needed to demonstrate definitively that there is a defect in Ca2+ handling."

Significance

see above.

Referee Cross-commenting

It seems we are in reasonable agreement about the pros & cons of the manuscript. I agree that alternative approaches to RU360 are warranted.

Transparent Peer Review

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Referee #1

Evidence, reproducibility and clarity

This study seeks to define how human lysosomes selectively downregulate membrane proteins and identify the machinery involved in this process. To this end, the authors screened a set of 30 lysosome membrane proteins (LMPs) in a cycloheximide chase assay in a human cell line which led to the identification of RNF152 (an E3 ligase) as a particularly short lived LMP. Further experiments demonstrate that RNF152 degradation is ubiquitin, ESCRT and lysosome dependent. They also show that the E3 ubiquitin ligase activity of RNF152 is critical for its turnover. The overall technical quality of the experiments is high and conclusions about the degradation of RNF152 are mostly reasonable. My most significant concern is that while compelling data is provided for RNF152 turnover, the authors over-reach in their efforts to generalize their findings to other LMPs. Given that the E3 ligase activity of RNF152 is so important for its turnover, RNF152 might be a special case. Consistent with this, the authors did not characterize other LMPs with similarly high rates of turnover. Although it would be interesting if RNF152 regulates the stability of other LMPs, until such proteins are identified, the authors should be more cautious in their interpretation. Speculation on this matter is reasonable so long as it is labeled as such. Even with respect to RNF152 turnover mechanisms, the overall conclusions would be significantly strengthened by a demonstration that the endogenously expressed, untagged protein behaves in a similar manner to what was described for the GFP-tagged transgene. With respect to the question about how long it would take for the authors to address these concerns, I cannot give a precise answer as it would depend on whether they decide to much more narrowly interpret their findings and temper their major claims (less than a month) or to expand efforts to generalize results (time frame unknown and perhaps not feasible).

1. As a specific (but not the only) example of over-reaching in generalizing the findings, the abstract ends with the following statement: "Thus, our study uncovered a conserved mechanism to down-regulate lysosome membrane proteins." My concern is that although this mechanism might be generalizable, the authors have only presented data for RNF152.
2. There is a complete reliance on over-expressed, GFP-tagged RNF152. There is no demonstration that the endogenously expressed protein undergoes such high rates of turnover. It is thus possible that the data does not reflect the normal turnover pathway for this protein.
3. In Figure 2B, why is the loss of full length RNF152-GFP not accompanied by an increase in the signal for free GFP during these pulse-chase experiments?
4. Figure 2E: Were all of the pairs of Input and IP immunoblots subject to the same exposure and image adjustments?
5. Figure 3C-E: The RNF152 mutants have slowed but not eliminated degradation. Is this dependent on their association with or ubiquitination by the endogenouslyh expressed RNF152?
6. Methods section indicates that t-tests were performed for all statistics. However, many experiments contain multiple comparisons and are thus ideally suited to t-tests. The authors should either justify the use of t-tests or provide a more suitable statistical analysis.
7. Although the model in Figure 7 shows the E3 (RNF152) ubiquitinating other proteins and promoting their ESCRT-dependent sorting into ILVs, this study did not identifying any such clients of RNF152.

Minor

Page 3: "Without treatment, almost all types of LSD patients will develop severe neurodegeneration in the central nervous system." This statement is misleading as there are multiple forms of LSDs that do not result in neurodegeneration and it is only these LSDs which can be successfully treated via enzyme replacement therapies. Unfortunately, the neuropathic LSDs remain largely untreatable due largely to issues of blood brain barrier permeability.

Page 3: "As we age, the lysosome membrane gradually accumulates damaged proteins and loses its activity, which dampens the cell's ability to remove pathogenic protein aggregates and damaged organelles, eventually leading to cell death and inflammation (Carmona-Gutierrez et al., 2016; Cheon et al., 2019; Yambire et al., 2019)." The references provided do not provide sufficient direct support for this broad statement.

Page 10: STED imaging results (currently "data not shown") should be supported by showing the relevant data.

Camera and objective information should be provided for microscopy studies.

Significance

The identification of a generalizable mechanism for the turnover of mammalian LMPs would represent a significant advance and would raise many interesting questions about mechanisms, regulations and physiological impact. While this studies contributes some interesting new clues to this topic, it falls short of unambiguously establishing how most LMPs are turned over in human cells. The data with respect to RNF152 is intriguing as it supports the idea that a novel form of ESCRT-dependent protein clearance occurs at the limiting membrane of lysosomes. However, it remains very much unclear to what extent this can be generalized to other proteins.