Reviewer #3:

This paper describes redox-active proteins in the ER of malaria parasites. The authors start out with PfJ2, a J- and Trx-domain containing protein. They find that it is an essential ER protein that interacts with other chaperone and Trx domain proteins. Using a crosslinker with specificity for redox-active cysteines they identify PfPDI8 and PfPDI11 as redox-partners that together may aid folding of other proteins in the secretory pathway. Finally the authors use inhibitors that act on human PDIs and show that they inhibit parasite growth, albeit at rather high concentrations. This may be fortunate as this suggests different specificities for host and parasite PDIs. However, it also means that from this work it is difficult to judge if the parasite PDIs can be specifically targeted.

This is an interesting paper and rightly emphasises that it addresses a much understudied process and organelle in the parasite. The DVSF-crosslinking and the knockdown cell lines are highlights (although the knockdown cell lines were not fully exploited). The paper covers a lot of ground. However, this comes at the cost of depth. The actual function of the studied proteins on folding of other proteins and on the state of the ER was not evaluated and it is also not clear if the human PDI inhibitors indeed target the parasite enzymes. The high concentrations of inhibitors needed to show an effect on DVSF-crosslinking might indicate a secondary effect due to loss of parasite viability. As a result it is not fully clear if the studied proteins are indeed critical for folding of relevant substrates and if this process is druggable. More work is needed to support the main conclusions of the paper.

Major points:

1) The authors describe conditional knockdown lines and find that PfJ2 and PfPDI8 are essential but these lines are not further exploited for functional studies. Did the knock downs have any effect on proteins they mention as potential substrates (Table 1)? Did it affect the state/morphology of the ER? Did knock down of PfPDI8 remove/shift one of the PfJ2 bands after DVSF-crosslinking, as would be expected? Is there an effect on BiP? A general folding problem in the ER with such a lethal phenotype might have profound effects on the morphology of the organelles receiving protein from the ER. What happens to other cellular markers after knock down of these proteins? Were the knock down cells analysed by EM? Was there an effect on protein export? As it stands the knock down data does not show a role of the complex in the folding of any type of substrate and the function in oxidative folding, as indicated in the title, remains tentative.

2) While I like the idea to use established commercial drugs as novel potential antimalarials, those used here are specific for non-infectious human diseases and target the host which is not a desirable property. Considering this, their rather low activity against the parasite can be taken as a positive result. However, the low activity is less convincing to establish the folding pathway in the parasite ER as a drug target. Beside the issue that it is unclear if indeed oxidative folding is the essential function of the PfJ2 complex (see previous point), the data in Fig. 7 does not clearly establish that this function is targeted by the inhibitors used. The effect is only seen at concentrations of 5xIC50. It is possible that this severely reduced viability which could be a non-specific reason for the lack of DVSF-crosslinked products. This needs to be examined in more depth. For instance, is the crosslink still seen after equivalent treatment of cultures with 5xIC50 of other unrelated drugs? Were other, unrelated processes unaffected? What was the effect of exposure to the drug on the ER and parasite morphology? Was the appropriate parasite stage affected? Can it be tested how fast exposure to 5xIC50 of the drug kills the parasites (at least morphologically, but preferably also by more specific means)?

3) While generally sound, a few experiments would have benefitted from more controls. A reducing sample from the same parasites for Fig. S7 (loaded a couple of lanes away to avoid interference of the reducing agent) would have been nice for comparison to show specificity of the higher molecular weight adducts. Detection of a control protein not expected to co-purify (for instance a cytosolic protein or a membrane-bound protein to control for residual parasite material) would have been appropriate for the co-immunoprecipitations (e.g. Fig. 6A,D, Fig. S9).

Reviewer #2:

The claim here is of having discovered a druggable cellular process in P. falciparum, one that opens the door to therapeutic intervention in the most deadly form of malaria.

The study commences with a focus on what appears to be the Pf homologue of a eukaryotic protein disulphide isomerase, known to many as ERdJ5 and referred to here as PfJ2. Its cellular contingents were identified by cross-linking and pull down, it’s (predicted) thiol reactivity explored with agents that react with reduced thiols and it’s functional importance to parasite fitness (in the lab) explored by gene knockout. These experiments provide evidence that PfJ2 and it’s associated Pf PDIs engage in thiol redox chemistry in the ER of the parasite and that integrity of this biochemical process is important to viability of the parasite.

Lacking all expertise in molecular parasitology, this reader is unable to judge the specific significance of these findings to the field nor indeed the extent to which these are hard-won discoveries. However, from the perspective of the fundamentals of ER redox chemistry the findings represent a modest advance, showing that what is true of yeast and mammals is also true of Apicomplexa. The important mystery related to the juxtaposition of a J-domain and thioredoxin domains in PfJ2, remains.

The most important claim however is the one with translational potential, namely that one might be able to discover (electrophilic) compounds that, despite the monotony of shared chemical features of thiol chemistry, will nonetheless possess sufficient specificity towards this or that malarial protein to be converted one day to a useful drug. However, in regards to this important point the authors offer very little in the way of evidence how and if this might be achieved.

Therefore, the main conclusions to draw from this paper are that ER-localised thiol chemistry is also important in malaria parasites and that, assuming one were able to explore localised context-specific features of thiol reactivity in malarial proteins, it may one day be possible to develop anti-malarial drugs that exploit this as a mechanism of action. The generic nature of these considerations limits the significance of the conclusions one might draw from this paper.

Reviewer #1:

In this manuscript, Cobb and colleagues report on the biochemical and functional characterization of redox active ER proteins in the malaria parasite Plasmodium falciparum. They studied a protein called PfJ2, which contains HSP40 J and Trx domains and is homologous to human ERdj5. Using the TetR-PfDOZI aptamer system to tag PfJ2 and conditionally regulate its expression, they show that PfJ2 is localized in the parasite ER and is essential for parasite growth during the asexual blood stages. Using co-immunoprecipitation combined with mass spectrometry, they identify partner proteins of PfJ2 including other ER proteins such as PDI and BIP. Using a chemical biology approach based on DVSF crosslinker, they document the redox activity of PfJ2 and identify redox substrates of PfJ2, which include PDI8 and PDI11 protein disulfide isomerases. They further functionally characterized PDI8 and PDI11 using the glmS ribozyme for conditional knockdown. These experiments confirm that PDI8 and PDI11 are partners of PfJ2 and show that knockdown of PDI8 impairs parasite blood stage growth. Finally, the authors show that inhibitors of human PDI inhibit parasite growth (at best in the micromolar range) and block the redox activity of PfJ2 and parasite PDI.

This is an interesting study combining genetic and chemical biology approaches to investigate an understudied compartment of the malaria parasite. The manuscript is clearly written and the work technically sound. In summary, this study illustrates that ER redox proteins in the malaria parasite perform similar functions as in other organisms. The main limitation of this study is that evidence showing that redox ER parasite proteins are druggable is rather weak. PfJ2 is very similar to human ERdj5 in terms of active redox site and function, and the authors used inhibitors that are active on human PDI. It thus remains uncertain whether an antimalarial strategy targeting such conserved pathways is achievable.

In addition, a number of specific points should be addressed to improve the quality of the manuscript:

Although PDI8 and PDI11 gene edition were performed in the PfJ2apt line, the authors did not attempt to knockdown both PfJ2 and PDI8/11 simultaneously (because PfJ2 is essential). Therefore, referring to "double conditional mutants" is misleading.

The authors should provide details on the parasite lysis conditions used for the co-IP experiments to identify interacting proteins (Table 1) and redox partners (figure 3). In their proteomic analysis, the authors considered proteins with a 5-fold increase in the specific versus control conditions. A more stringent analysis would retain only proteins identified exclusively in the modified J2apt line.

In figure 6, the authors should probe the blots for a control protein that is not co-immunoprecipitated with PfJ2 or PDI8.

In Supplementary fig 4, control untreated parasites should be analyzed in parallel to GlcN-treated parasites.

The partial reduction of protein levels (Fig S4) shows that the glmS system is not very efficient here, which might explain why there is no phenotype in the PDI11 mutant (Fig5B). This questions the conclusion that PDI11 is dispensable.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Reviewer #3:

In this manuscript, Bohr et al examine how the pluripotent stem cell system of planarians responds to organ-specific damage. If and how the differentiation of specific cell types is dynamically regulated is a conceptually fascinating problem in planarians and in general stem cell research. The authors address this problem by comparing the stem cell response between a single-organ amputation (the pharynx) versus broad tissue loss (decapitation). Their findings indicate that only the removal of the pharynx triggers the increased differentiation of pharyngeal cell types, while the loss of non-pharyngeal tissues upregulates the differentiation of progenitors of multiple organs, but not the pharynx. Further, the authors implicate temporally restricted ERK signaling as a regulatory component in the differentiation of pharyngeal cell types. These observations are also important because they contrast with the previously proposed "target blind" model (LoCascio et al., 2017) that posits the differentiation of different cell types at constant relative proportions, with the rate of stem cell divisions as global production rate regulator. In contrast, the observations by Bohr et al provide further evidence for more flexibility and specificity within the planarian stem cell system ("target consciousness") in the sense of lineage-specific adjustments in the production rates of specific cell types.

That said, the manuscript generally suffers from an overly narrow focus. Important questions remain regarding the specificity of the stem cell response to pharynx amputation and multiple experiments lack important controls (see below). Moreover, the authors have overlooked that a "target conscious" progenitor response has already been demonstrated by the selective proliferation of protonephridial markers expressing neoblasts in response to protonephridial damage by RNAi (Vu et al., 2015).

Major points:

1) Specificity of the stem cell response:

The central premise of the paper is the selective amplification of pharyngeal progenitors in response to pharynx amputation. The authors conclude this based on i) an increase in the absolute number of foxA+/piwi-1+ cells in a specific area, while ii) de-capitation has no effect on the absolute number of foxA+/piwi-1+ cells in the same area. This approach is an insufficient demonstration of specificity, as the known phenomenon of wound-induced stem cell activation might also change the absolute number of specific neoblast subclasses and might do so in an injury-dependent manner.

To account for this important caveat, the authors need to i) quantify RELATIVE proportions of foxA+/piwi-1+ cells out of total piwi cells (or of total H3P+ cells) and ii) they need to include other organ progenitors in the initial analysis. The latter is also critical because the pharynx is a complex organ comprising descendants of multiple lineages (e.g., muscle, neurons, epidermis) and it is not clear whether the foxA+/piwi-1+ cells indeed serve as a singular origin of all constituting lineages (as assumed by the authors), or if they only provide a subset of pharyngeal cells with a rate-limiting role in pharynx assembly (e.g., pharyngeal muscle). In the face of such uncertainty, iii) the quantification of new cell incorporation into the pharynx versus other tissues via BrdU labeling would be necessary to address this caveat and to provide a global perspective on the specificity of the response independent of incompletely characterized marker genes.

In addition, the following experimental design problems need to be addressed or better documented, including:

• The authors provide insufficient methodological detail on progenitor quantifications, even though the entire manuscript rests on this assay. What are their criteria for scoring a piwi-1+ cell as double-positive for the often weak and noisy lineage labels? If done "by eye", was double-blind scoring used? Were all cells in a given Z-stack counted or only specific planes? If the latter, by which criteria were image planes selected for quantification? How were the specific specimens out of an experimental cohort selected for imaging/quantification? Though not necessarily a unique shortcoming of this particular study, these points simply need to be adequately addressed in order to rigorously support quantitative differences between experimental conditions (e.g., specificity).

• The authors appear not to distinguish at all between technical replicates (e.g., multiple specimens within an experimental cohort) versus biological replicates (independent experimental cohorts). This is significant, because i), the use of the standard error of the mean (SEM) that the authors employ throughout is not really an appropriate measure for a single biological replicate with 3 animals - the standard deviation (SD) would seem a more appropriate measure in this context (SD). ii), the number of worms quantified for each experiment is generally low (n=3 animals in Fig. 1, 3, 5, 6; n=5 animals in the rest of the figures) given the observed variability in the data (e.g., ~25-30 foxA+/piwi-1+ cells 3d after pharynx amputation in Fig. 1E versus 50 cells in figure 1H). Similarly, for kinetic experiments as in Fig. 1H or 2C, it is simply crucial to ensure that the error bars include the variation in response dynamics between multiple replicates due to the drift in the baseline fraction of H3P+ cells or varying staining efficiencies (e.g., different batches of animals on different days), rather than the technical variation in a single experimental cohort only. Please address these concerns by adding more specimens and a thorough description of the experimental design.

2) Timeline of pharynx regeneration: The pharynx regeneration timeline and associated events that the authors present are insufficiently supported by experimental data. The conclusion in line 215 "that proliferation in a critical window of 1 to 2 days after pharynx amputation produces a population of progenitors that are likely essential for pharynx regeneration" rests i) on the diagnosis of a "proliferative peak of FoxA+ stem cells that occurs after pharynx amputation (Figure 2C)" (line 202). However, rather than a "proliferative peak", Fig. 2C shows a broad "proliferative plateau" of FoxA+ stem cells between 6h and 3 days after amputation. Similarly, the foxA+/H3P+ quantification after pharynx amputation in Fig. 4G also displays a lack of a peak of foxA+/H3P+ from 1d to 2d after amputation. ii), the associated nocodazole experiments suffer from the fact that the authors did not quantify the impact of the drug on the abundance of foxA+/piwi-1+ cells during treatment intervals from 0-1d and 2-3d after pharynx amputation. Therefore, the authors cannot rule out that nocodazole treatment might have similar effects on the abundance of foxA+/piwi-1+ cells throughout the 1-3 d post-amputation time interval, with the more severe organ-level phenotype of the 1-2d treatment window being caused by some other effect of the drug (e.g., on the differentiation of another rate-limiting cell type for pharynx regeneration or, conceivably, inhibition of priming neuronal activity ). Similar concerns apply regarding the statement in line 242, "... a window 1-2 days after amputation in which activation of ERK signaling is important for pharynx regeneration." Here, i) the quantification of the end-stage phenotype of drug treatment during the 1-2d time interval (regain of feeding ability) is missing. ii) Similarly, the examination of the consequences of PD treatment on foxA+ expression in piwi-1+ cells in panel 4D-H employs drug soaking for 3 days, yet the corresponding end-stage phenotype of 3-day drug treatment is not shown. iii) the implications of ERK in pharynx regeneration are tentative. Even though the PD compound is initially correctly introduced as "MEK inhibitor", the authors subsequently switch to the factually wrong "ERK inhibitor" designation (e.g., line 358). Further, additional experimental evidence for the assumed Erk inhibition as the cause of the observed phenotypes would be desirable to rigorously support the conclusion.

These caveats need to be addressed if a cell biological timeline is to remain part of this manuscript.

3) Integration with the existing literature:

The authors need to better integrate their findings with the literature. First, they need to cite the findings of Vu et al, which explicitly demonstrated a specific increase in the fractional abundance of piwi-1+/protonephridial marker+ cells in response to RNAi-mediated damage to protonephridia (Vu et al., 2015). As such, this study already demonstrates the main point of Bohr et al., namely that the planarian stem cell system is capable of "target conscious" progenitor provision. At the very least, the authors should credit these results as additional evidence for their model. A further finding that they should discuss is the demonstration by LoCascio et al (LoCascio et al., 2017) that flank region cut-outs cause a significant increase in pharynx cell incorporation over baseline, despite the absence of injury to the pharynx. How do the authors reconcile the discrepancy between these data and their own? In general, the discussion would benefit greatly from a more explicit comparison between the "target blind" model versus their data, as well as a broader perspective on the regulation of stem cell homeostasis.

Reviewer #2:

Bohr, Shiroor, and Adler investigate how stem cells respond to the loss of specific tissues in planarians. The planarian stem cell population (neoblasts) are distributed throughout the planarian body and include pluripotent stem cells and a wide range of lineage-committed progenitor cells. How this heterogenous pool of cells behave post-injury or amputation is incompletely understood. The discovery of markers to label stem cell progeny have opened the door to investigate how stem cells respond to tissue loss. However, the anatomy of planarians makes it difficult to surgically remove or damage specific organs. The PI of this study developed an assay to remove the pharynx by "chemical amputation" to study the mechanisms underlying regeneration of this organ without drastically perturbing or injuring other tissues. Using this approach, this paper investigates how a well-defined population of FoxA+ progenitors respond to pharynx removal at early time-points during the regeneration. Their data suggest that stem cells are able to detect loss of the pharynx and respond by generating significantly more cells fated to become pharynx, whereas amputation of non-pharyngeal tissues does not have an obvious effect on pharynx progenitor specification dynamics. In addition, using pharmacological treatments, the authors show that cell proliferation and ERK signaling are required for the expansion of pharynx progenitors and cell differentiation. In contrast, other cell types in the planarian eye do not appear to require proliferation or ERK signaling, suggesting that stem cell responses "target blind" as suggested in a previous study, but are rather tuned to specific missing tissues.

This work has the potential to make a significant contribution to the field by advancing our understanding of how the planarian heterogenous stem cell population responds to the loss of a specific organ. However, the report is preliminary as presented. It appears that the authors performed many experiments a single time. In addition, description of the methods is insufficient. The authors need to chiefly demonstrate the reproducibility of the data and robustness of the observations.

Concerns:

1) The authors need to replicate experiments to increase the sample size for most experiments.

2) Details for imaging and quantification should be explicitly stated in the methods, and the reported cell count numbers should be normalized as appropriate for each set of experiments.

3) Although the authors mention "lineage-tracing" experiments (see minor comments), they do not perform DNA analog pulse-chase experiments to analyze a temporal progression and spatial localization of stem cells to FoxA+ progenitors after pharynx removal. The authors rely on PH3-staining in conjunction with FoxA, and supplementary experiments using the pluripotent stem cell marker tgs-1 (which was only examined at 1 dpa). Could the authors clarify what they think FoxA+ stem cells represent? Are these self-renewing pluripotent stem cells or lineage-committed progenitors? Can the authors get some insight by scanning their images of PH3+ cells expressing FoxA visibly undergoing metaphase? Are daughter cells uniformly FoxA+ as reflected in the model? At least in one of the cells shown in the nocodazole treated controls it appears that both daughter cells express FoxA (Figure 3). I suggest showing some higher magnification images to support the interpretations/conclusions. Others have posited (e.g., Rink, Chapter 2 of Planarian Regeneration: Methods and Protocols), that not every dividing cell may be a long-term self-renewing stem cell and whether transient amplifying cells exist or contribute to regeneration in planarians is unknown. Adler and Sánchez Alvarado (2015) discuss the role of transient states and how the transcriptional profiles change in response to regeneration. It wasn't clear to me how the authors think about these cells based on the limited number of experiments and analysis, and there are a few places where the terminology is inconsistent, especially in reference to proliferating ovo+ progenitors (P. 14). The authors need to be clear, and it might be helpful to illustrate their model in one of the early figures or to include it in the final model, which omits tgs-1 due to the limited number of experiments performed with this marker gene (Figure 7).

4) The pharynx is complex and there is no data to assess what the contribution of other progenitor populations might be. I don't think or think it is unlikely that FoxA+ progenitors are solely responsible for reconstructing the pharynx. The authors should examine how other progenitor populations behave during the process of pharynx regeneration by extending the timeline of progenitor cell analysis. This would reveal if there is fluctuation in progenitor dynamics as animals regenerate the pharynx or re-scale proportions after pharynx regeneration. For example, can the authors test if they are able to detect a contribution of neural progenitors to regeneration of the pharyngeal nervous system? And if so, when during the regeneration process does it take place in the context of their study?

Reviewer #1:

This manuscript explores how planarian stem cells respond to the loss of a specific organ: the pharynx. The previously proposed "target-blind" model of planarian regeneration (LoCascio et al. 2017) posited that stem cells do not respond directly to missing tissues, but rather replace missing cell types based on their normal rates of homeostatic turnover. In contrast, the authors of this manuscript suggest that planarian stem cells can sense and respond to the loss of specific missing tissues, using the pharynx as a case study. The authors conclude that planarians may use more than one mode of regeneration, depending upon the target being regenerated (eye vs. pharynx).

The question explored in this paper is of fundamental importance, and providing an alternative model by which planarian stem cells regenerate missing tissues should be of interest to a broad readership. Unfortunately, in its current form, the manuscript presents enticing preliminary findings, rather than robust experimental observations. Because the authors are attempting to refute a previously published model, it is critical that the data are clear and convincing. If not, these findings could be summarily dismissed without appropriate debate. If the authors can demonstrate that their results are robust across larger samples sizes and experimental replication, and address the major issues listed below, this manuscript would represent a significant contribution to our understanding of planarian regeneration.

Major Issues:

1) Throughout the manuscript, experiments were either not repeated, or the number of biological replicates was not reported. In most cases, it appears that experiments were done only once (with the exception of the drug treatments). Numbers of biological replicates and sample sizes should be explicitly stated and the data from different replicates reported for Figs. 1D-G, 2B-D, 3C, 3E-F, 4B, 4D-H, 5C-D, and 6A-E.

2) The authors do not sufficiently describe their methods for imaging and quantifying cells (Figs. 1E, 1G, 2C-D, 3F, 4E-H, 5D, 6B). The size of the area covered to collect these data is unclear. High-magnification images are shown: are these the areas that were imaged? If so, their results could be biased by choosing small regions of interest. Ideally, the authors should quantify more than one region per animal. Also, they do not describe the depth of the z-stacks collected or how these stacks were normalized/standardized across conditions. All their conclusions hinge on the quantification of progenitor populations in response to different amputation paradigms or chemical treatments, so the standards for imaging and quantification must be clearly reported.

3) Inappropriate statistical tests were used throughout. The use of multiple t-tests amplifies the chance of a Type I error and is especially problematic when up to 7 comparisons were made! The authors should use one-way ANOVA with multiple comparison corrections for all experiments with more than two groups.

4) Figs. 1D-E show that upon pharynx amputation but not head amputation, FoxA+ piwi+ pharynx progenitors increase. These data suffer from the quantification issues highlighted above: how the data were quantified is not sufficiently described, only 3 data points were taken (one per animal), the experiment appears to have been performed only one time, and the wrong statistical test was used. Rather than reporting the number of FoxA+ piwi-1+ cells counted, the authors should quantify the total number of doubly positive cells as a percentage of piwi-1+ cells, as was previously published (Adler et al. 2014). The authors also fail to specify whether the change observed between "3 dpa phx" and "3 dpa head" is significant, which is a material point.

5) Fig. 2D also suffers from the inadequate quantification practices described above. Ideally, FoxA+ cells should be quantified as a percentage of the H3P+ cells observed.

6) The authors use "stem cell", "progenitor", "stem cell progenitor", and "progenitor stem cells" in a mixed and confusing way throughout the paper. For example, in lines 174-175 the authors state that "proliferation of FoxA+ stem cells precedes the increase in pharynx progenitors." This refers to FoxA+ H3P+ cells vs. FoxA+ piwi-1+ cells, but the only difference is that the former are stem cells in the act of mitosis. Is a distinction being made? Elsewhere in the paper, FoxA+ piwi+ cells are referred to as stem cells. The terminology used needs more clarity and consistency.

Along these lines, what is a FoxA+ PSC (Line 168)? Are the authors suggesting that FoxA is a pluripotency marker? Or are the authors saying that tgs-1 has a more expansive expression pattern and is co-expressed with progenitor markers? If double FISH was performed with the progenitor markers reported (ovo, myoD, gata-4/5/6, six-1/2, and pax6), would they all overlap with tgs-1? These experiments need to be performed to make any claims about FoxA expression in the context of pluripotency.

7) In Fig. 3C, how does pharynx regeneration occur over such a long period of time after nocodazole treatment in the 1-2 day window? Does target-blind regeneration occur once this window is missed? The authors should repeat analysis of FoxA+ progenitors at later time points in this condition, and/or show rates of BrdU incorporation into the pharynx with and without nocodazole treatment in this window.

8) The use of the inhibitor PD in Fig. 4 is problematic. No data are shown to verify that phosphorylation of ERK was inhibited in these experiments. A citation of previous use is not sufficient. The effect of PD on WT uncut animals with regards to FoxA+ cells is not shown and is a necessary control. To address questions of drug specificity, the authors should corroborate their findings with a second inhibitor of ERK signaling like U0126, which has already been shown to work in planarians (Owlarn et al. 2017).

9) The conclusion that ERK signaling functions in regulating differentiation but not proliferation is premature (line 249-264). Figs. 4E-H should be quantified as percentages of piwi-1+ and H3P+ cells, especially since there is decreased proliferation overall with PD treatment.

10) The use of head fragments to compare eye regeneration vs. pharynx regeneration is inappropriate. Previous studies have already shown that the absence of eyes is not required to induce ovo+ progenitor amplification (LoCascio et al. 2017). Thus, this is not a surprising result (line 343-345) and the authors are mis-citing previous observations (in the earlier work, head fragments were never described). The region where ovo+ cells was quantified in Fig. 6A is not justified or explained. The yellow box is placed in a medial region where ovo+ cells do not normally reside. The authors should image within the laterally positioned ovo+ streams that have been previously described (Lapan & Reddien 2012; LoCascio et al. 2017).

11) Rather than using head fragments, the authors should repeat the flank resection experiments shown previously (LoCascio et al. 2017). This previous study showed that increased BrdU incorporation into the pharynx occurred following flank resection even though the pharynx was present. That result may have been 1) an artifact of increased BrdU staining due to stimulation of proliferation upon injury, 2) caused by unintentional damage to cells associated with the pharynx, or 3) a response to the loss of FoxA+ progenitor populations that surround the pharynx rather than the loss of the differentiated organ. The authors have the opportunity to revisit this published observation by quantifying the FoxA+ progenitor response during flank resection +/- pharynx. Without these data, this story is incomplete and therefore the conclusion of a targeted regeneration response is not yet convincing.

12) The negative results that proliferation and ERK signaling are dispensable for eye regeneration in Fig. 6 are weak and unconvincing. The regenerated eyes appear smaller; this should be quantified (number of PRNs per eye). If the small pharynges that form in Figs. 3D and 4C are considered a deleterious phenotype, why is the same standard not applied to the eye? Also, existing eye progenitors could have been sufficient for eye regeneration in these drug treatments. Furthermore, eyes did not regenerate after nocodazole treatment 50% of the time. Is it not more likely that the observations reported are dosage and timing artifacts? How has proliferation been affected? These observations do not live up to the claims made.

13) The authors claim that ovo+ cells are not proliferative (H3P+) even in cases where there is eye progenitor amplification (head amputation), but the data are not shown (line 321). They should be. Indeed, previous publications have never shown that ovo+ cells proliferate. This might mean that there are proliferating eye progenitors that precede expression of ovo. The authors should discuss this alternative.

14) The authors claim that eye regeneration does not require proliferation or ERK signaling but pharynx regeneration does. This conclusion hinges on the gross observation that eyes can regenerate in the presence of nocodazole and PD (see point 12 above). These data are coarse and the interpretations are unconvincing. Instead, their model can be directly tested using BrdU pulse-chase experiments. According to the authors' model, one would predict that following pharynx amputation, the rate of incorporation of BrdU+ cells into the regenerating pharynx should be higher than in uninjured controls. Conversely, the rate of BrdU incorporation into the regenerating eye should remain unchanged between injured (i.e. eye-resected) and control animals (LoCascio et al. 2017). Once the authors have established the prediction above, they have the opportunity to show the effects of nocodazole, PD, and U0126 on BrdU incorporation in the regenerating eye vs pharynx following eye resection and pharynx amputation in the same animal. This way, the authors can directly test the requirement for proliferation and/or ERK signaling in both tissues.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary

All three reviewers recognized the potential significance of this work, but shared concerns about sample sizes, lack of biological replicates, and insufficient details about cell quantification.

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

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Reply to the reviewers

Note from the authors (AU): This manuscript has been reviewed by subject experts for Review Commons. The authors would like to thank the reviewers for their comments to the manuscript, and the editor for patience with our response. Our reponse was delayed due to the COVID-19 lock-down situation in our institution. Now we are pleased to provide the following point-by-point response, as detailed below.

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

The manuscript by Suomalainen et al. describes a fluorescence-based approach combined with high-resolution confocal microscopy to study the heterogeneity of adenovirus infection in a population of human cells. The main focus of the authors is the detection of viral transcripts in infected cells, how this correlates with viral genomes, the cell state, and how it varies between different cells in a single population. The paper is generally well written and easy to read, with a few typos, although I found parts of it to be somewhat length and repetitive. Particularly the results section could be pruned somewhat for readability and clarity. The major limitation of the study as it stands is it's overall impact and novelty, which limits journal selection somewhat. A very similar study was recently published, which the authors cite (Krzywkowski et al, 2017). Nevertheless, I think the study design is rigorous and well executed, but I do have some specific comments which may enhance it's overall impact and novelty.

**Major:**

Results "Visualization of AdV-C5..." section:

Why not also look at normal cells that can be synchronized? Cancer cells, such as A549 will by definition be highly heterogenous and at all phases of the cell cycle. Primary non-transformed cells can easily be synchronized by contact inhibition and are much more physiologically relevant.

AU: In the current manuscript, we concentrated on the early phases of the AdV-C5 infection, on the question how virus gene expression is initiated and whether the cell cycle phase of the host cell impacts the initiation of virus gene expression. Answering these questions requires use of cells that express good amount of virus receptors so that viruses efficiently bind to the cells and infections can be synchronized so that extended time does not elapse between virus addition and accumulation of E1A transcripts; extended time between these two steps would make interpretation of the results more complex since cells could have progressed from one cell cycle stage to another during the experiment. Furthermore, having cells at all phases of the cell cycle is actually a benefit since then the experiment can be carried out under an “unperturbed” condition; all cell cycle synchronization methods have pleiotropic effects on the cells.

It is true that primary non-transformed cells are physiologically more relevant than cancer cells, but primary cells have issues with donor-to-donor variability and many primary cells express rather low amounts of AdV-C5 receptors, so synchronized infections in these cells are not possible. Furthermore, the extended cell morphology of many normal fibroblast cell lines and the tendency of cell extensions from neighboring cells to overlap makes fluorescent images of these cells incompatible for automated cell segmentation.

Here, we provide data also from HDF-TERT cells (nontransformed human diploid fibroblasts immortalized by human telomerase expression) to show that two of our key findings from A549 cells are not artefacts of cancer cells. This is, that akin to A549 cells, the infected HDF-TERT cells accumulate high number of E1A transcripts (Fig.1C), and also in these cells nuclear vDNA numbers do not predict the cytoplasmic E1A transcript counts during early phases of infection (S2C Fig). However, since HDF-TERT cells are rather inefficiently infected by AdV-C5, correlation of early E1A transcript accumulation to the cell cycle phase of the host cell could not been done in these cells. We have been unable to identify primary or normal immortalized cells that would be easily available and efficiently infected by AdV-C5 (synchronized infection with short time elapsed between virus addition and accumulation of E1A transcripts).

"The virus particles bound..." - Can the spatial resolution of a confocal microscope truly differentiate individual particles that are sub-wavelength in size? What about the sensitivity for single particles? Some sort of experiment to show that single particles can be detected should be performed and shown to assure the readers that this is in fact possible. Furthermore, even when based on the particle to pfu ratio, the MOI would still be nearly 2000pfu/cell, so the actual number of observed particles is an order of magnitude lower than what was applied to the cells.

AU: The fluorescence signal from individual fluorophore-tagged AdV or anti-hexon antibody-decorated particle is bright enough to be picked up by PMT or HyD detectors of the current confocal laser scanning microscopes. In fact, tracking fluorophore-tagged particles of the size of AdV has been a standard microscopy procedure since late 1990’s.

Because the Reviewers were questioning the apparently high multiplicity of infection used in the experiments, we clarify the difference between “standard” MOI estimations and our infection set-up. First of all, as described in Material and Methods, we estimated the number of physical virus particles in our virus preparations using A260 measurements (J.A. Sweeney et al., Virol. 2002, doi: 10.1006/viro.2002.1406). This method, like all other methods used to estimate virus particle numbers, is likely not 100% reliable.

Second, we incubated the virus inoculum with cells only for 60 min, after which the unbound viruses were washed away. During this short incubation time only a small fraction of input virus particles bind to cells, and indeed as shown in Fig.1A, a theoretical MOI of 54400 physical virus particles/cell or 13600 physical virus particles/cell yielded Median of 75 and 26 bound virus particles per cell, respectively. Interpretation of the results from the cell cycle assays required that there was a relatively short time between infection and analysis so that cells in a large scale did not change their cell cycle status during the experiment. This required use of a rather high MOI. Furthermore, for collection of a large data set, it is convenient that every cell is infected.

Third, what exactly does one pfu mean in terms of physical adenovirus particles? There is no clear answer to this, since several parameters affect the pfu. In which cells was the titration carried out? How long was the input virus inoculum incubated with the cells? How many of the virus particles entering the cell actually established an infection? And, as described in A. Yakimovich et al. (J. Virol. 2012, DOI: 10.1128/JVI.01102-12), only a fraction of infected cells produce a plaque. The majority of papers stating that x pfu/cell was used for infection, usually incubate the cells with the virus inoculum for several hours at 37°C, and never make any attempts to estimate exactly how many virus particles entered into the cells.

Fig. 4 - I am not certain that the observed difference is significant, at least looking at it, beyond the width difference of the peaks, highest expression for both is largely in G1. It would be nice to see this using a western blot of cell cycle sorted cells, which can easily be accomplished using FACS.

AU: In the highest GFP expression bin, CMV-eGFP expressing cells have 43% cells in G1 and 50% in S/G2/M. In comparison, E1A-GFP expressing cells have 58% cells in G1 and 35% in S/G2/M. The difference in G1 cells in the highest eGFP bin is statistically significant (p Page 15, 2nd paragraph. It would be valuable and informative to determine whether there is heterogeneity in histone association with these different vDNAs and whether these histones exhibit divergent modifications (enabling or restricting transcription). Same as above. I am rather surprised that the DBP signal did not correlate well with vDNA signal, particularly for the larger replication centers. How can this be reconciled? Was there an increase in overall vDNA signal later in infection? It is important to know this as it determines whether the observed vDNA signal is real or could be caused by viral RNA or other background causes (non-infected controls notwithstanding). Can the signal be detected with inactivated viruses (via UV for example?)

AU: Whether histone modifications impact the transcriptional output of adenovirus genomes early in infection is indeed an intriguing question, but unfortunately this is very challenging, if not impossible, to study at single-cell / single vDNA level with the existing technology. Techniques for single-cell measurements of chromatin states are still in infancy, although some notable advancements in this field were reported in 2019 (e.g. K. Grosselin et al. Nature Genetics, DOI: https://doi.org/10.1038/s41588-019-0424-9 and S. Ai et al. Nature Cell Biology, DOI: https://doi.org/10.1038/s41556-019-0383-5).

Furthermore, current literature offers a confused picture as to when exactly protein VII on incoming virus genomes is replaced by histones (reviewed in the reference 39, Giberson et al.). Of note, the vast majority of incoming nuclear vDNA molecules scored protein VII-positive with anti-VII staining under the experimental conditions used for the Fig. 2C data. However, we did not include these results into the manuscript because VII-positive signal on vDNAs does not exclude these vDNAs having histones on certain parts of the genome.

The Reviewer wonders why the DBP signal in Fig.6C does not correlate with vDNA signal. There is no discrepancy here because DBP signal in the figure is a proxy for replicating vDNA whereas the click vDNA signal reports incoming vDNA. The one DBP spot without an associated click vDNA signal could be due to a replication center originated from a replicated viral genome, not from incoming viral genome. The figure shows that incoming vDNAs within the same nucleus initiate replication asynchronously.

Page 18, 1st paragraph. It would be interesting to determine whether there was association between pol II and those genomes that showed no E1A, similarly to the histone suggestion. What about things like viral chromatin organization? Soriano et al. 2019 showed how E1A and E4orf3 work in tandem to alter viral chromatin organization by varying histone loading on the viral genome.

AU: This again would be technically very challenging to show. We actually tried to visualize active transcription using an antibody against RNA polymerase II CTD repeat YSPTSPS (phosphor S5), azide-alexa fluor488 and anti-alexa fluor488 antibody to mark EdC-labeled incoming vDNAs and proximity ligation assay for signal amplification. However, this method was not sensitive enough to detect RNA polymerase II association with individual viral genomes. We only detected the proximity ligation signal in replication centers when replicated viral genomes were tagged with EdC.

Fig. 2. Can you really say that a single dot correlates with a single transcript? Has that been validated in any way?

AU: Signal amplification with branched DNA technology leads to binding of a large number of fluorescent probes to a mRNA and thus enables detection of single nucleic acid molecules. This has been validated e.g. in A.N. Player et al. 2001. J. Histochem. Cytochem (https://doi.org/10.1177/002215540104900507) and N. Battich et al. 2013. Nature Methods (https://doi.org/10.1038/nmeth.2657).

**Minor:**

Page 5, last paragraph. "Transcirpts from the viral late transcription unit,..." This is not correct as recently shown by Crisostomo et al, 2019.

AU: The data in Crisostomo et al. paper suggest that some late gene expression can occur before vDNA replication, but an abundant accumulation of late transcripts coincides with onset of vDNA replication. However, the Crisostomo et al. study did not test what the levels of late gene transcripts are if the vDNA replication was inhibited. But to acknowledge the possibility that there might be some level of late gene transcription prior to replication of the viral genomes, the sentence is modified as follows: “Transcripts from the viral late transcription unit, amongst them mRNAs for the viral structural proteins, vastly increase in abundance concomitant with the onset of vDNA replication”. Furthermore, we have added the Crisostomo et al. reference here as well.

Page 10, "... because AdvV-infected cells are less well adherent..." This is not strictly true as loss of attachment only occurs later on in infection. It would be helpful to have statistical significance indicated directly in the figures.

AU: Although clearly visible cell rounding indeed occurs only late in infection, also during early stages of infection the HAdV-C5-infected cells are less adherent than non-infected cells. In many assays this is not obvious, but the RNA FISH staining procedure includes several incubation and washing steps in rather harsh buffers, and we observed random, sometimes considerable, cell loss with infected cultures but not with non-infected cultures.

In the revised manuscript we have included the statistical significance P values both into the main text and the figure legends, but not to the figures directly, because the P values were generated with different statistical tests and P values should not be shown/mentioned without stating which statistical test was used. However, we noticed that we had in some cases omitted to mention what was the number of pairs analyzed in some of the Spearman’s correlation tests. This has now been corrected in the revised manuscript.

The very high MOIs used are concerning, could these have negative effects on the cell viability or overall state?

AU: We refer to our explanation above about the theoretical MOI and the actual MOI. Furthermore, in the experiment described in Fig.2C (correlation of E1A transcripts per cell vs. viral genomes per cell), 42% of analyzed cells had ≤ 5 viral genomes/cell and 27.5% of analyzed cells had between 6-10 viral genomes per cell; these are not high numbers. We also provide controls that the EdC-labeled genomes are detected with good efficiency. Hence the EdC-labeled genomes per cell are a good estimate of the numbers of virus particles that indeed entered into the cells.

There are a few typos and such that should be corrected. AU: We have tried to find and correct the typos.

Reviewer #1 (Significance (Required)):

As I stated above, the work is interesting and significant, to a degree. The major limitation is that the novelty is low as a paper published in 2017 (cited by the authors) used a very similar approach to investigate a similar problem. In addition, there are multiple other recent papers looking at cell populations in the context of adenovirus infection, and whether a single cell or population based approach is better is unclear. This is something the authors might want to strengthen prior to submission.

AU: In the current study, we focused on the early phase of HAdV-C5 infection, on how viral gene expression is initiated and how individual nuclear viral genomes proceed to a replicative phase. The Krzywkowski et al. 2017 J. Virol. Paper that the reviewer refers to used padlock probe-based rolling circle amplification technique to simultaneously detect HAdV-C5 genomes and viral mRNAs in individual infected cells.

The shortcoming of this method is inferior sensitivity compared to the branched DNA technology-based method used by us in the current study. Krzywkowski et al. were able to pick up signals from virus mRNAs and virus genome only relatively late in the infection, i.e. at the time when incoming genomes were expected to have multiplied by replication. Thus the study by Krzywkowski et al. was unable to provide information for the questions addressed in our study, i.e. do the levels of E1A transcripts early in infection correlate with viral vDNA counts in the nucleus and is there variability in the transcription output from individual vDNAs within the same nucleus, or variability in how individual vDNAs within the same nucleus proceed into the replication phase. We hence do provide novel information, and do not consider this as a limitation of our paper.

We emphasize that population assays are done to attempt to understand molecular basis of a phenomenon by correlations. Instead, deep molecular insights require to-the-point-assays, in the case of transcription, single-molecule live cell assays at the level of single genes. Technically, we (and also the field) are not quite there yet.

Regardless, our study is a first step towards understanding transcription output of nuclear HAdV-genome at single-cell, single-genome levels. It has revealed insight that was not apparent from population assays. It is clear that the next step will be time-resolved live cell assays with simultaneous detection of transcription output, genome detection and transcription factor clustering on the genomic loci. With current technology the simultaneous detection of all these events is challenging, and requires the development of further technology.

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

The authors show heterogeneity of AdV-C5 mRNA transcript quantity and dynamics in different cell types, which is regulated by the cell cycle phase and does not correlate to incoming viral DNA, using single molecule RNA FISH technologies and detection of incoming viral DNA by EdC labeling.

**Major Comments:**

The authors change the MOI used in their experiments (7 different MOIs are used throughout the paper) in a manner that appears randomly and without explanation. (54400 for Figure 1A, 1B, 3B, S3B; 37500 for Figure 1C; 23440 for Figure 2A, 2C, S5A; 13600 for Figure 1A, 1D; 36250 for Figure 3C, S3D; 11200 for Figure 4B; 23400 for Figure 6B). The authors should provide explanation, why these changes in MOIs are necessary.

AU: The MOIs given are theoretical MOIs, and essentially all figures indicate what was the actual MOI, that is, the real number of virus particles entering into the cells. This is beyond what is commonly provided in virology. It is essential, however, since MOI differs between different cell types. Therefore, we prefer to use the actual MOI as shown in Fig.1A, or we indicate the number of vDNAs that were delivered to the cells of interest.

Variable MOIs had to be used to ensure that different cell lines received comparable numbers of virions, in particular virus particle binding to and entering into the cells. Infection kinetics are different in different types of cells, but can be tuned by MOIs used. Furthermore, different virus preparations were used in the experiments and we performed analyses at different stages of the infection cycle. Due to all these different facettes provided by our experiments, it was impossible to choose one standard (theoretical) MOI for all the experiments.

The authors use mean fluorescence intensity of E1A probes per cell as estimate for viral transcript abundance for some of their experiments (Figure 1D, E, 3B), and count E1A punctae as measure for E1A transcripts in other experiments (Figure 2C, 3C, 5), without showing data, that these measures correlate. Problematic is hereby, that not all E1A punctae have the same signal intensity, as can be seen in Figure S1, which makes the estimation of the correlation of E1A punctae (= number of transcripts) and fluorescence intensity difficult. The authors should provide both (E1A punctae counts and estimation via fluorescence intensity) for at least one experiment, to prove, that the estimation of E1A transcript levels via fluorescence intensity is feasible.

AU: The quantification method had to be adjusted to the number of virus transcripts in the cell at the time of analysis. The best quantification method is segmentation and counting the individual fluorescent puncta per cell, but, as stated in the manuscript, this method does not accurately quantify the mRNA puncta from maximum projections of confocal or widefield image stacks when the number of puncta per cell exceeds ~ 200.

On the other hand, as shown in the quantification below, mean fluorescence intensity measurements per cell do not of course distinguish between cells having one vs. two mRNA puncta. Yet, as shown in the figure below, a relatively good correlation between puncta counting and fluorescence intensity measurements is achieved when cells have ≥ 10 transcripts per cell. Subsets of randomly picked images of the Fig.2C/Fig.5 dataset were included into the analysis (rs is Spearman’s correlation rank coefficient, approximate P p.15: "The nuclear E1A signals in AraC-treated cells were resistant to RNase A, but they were dampened by treatment with S1 nuclease (S6B Fig)." The authors make this statement based on (i) two completely different timepoints (12 h.p.i. for RNaseA treatment, 24.5 h.p.i. for S1 nuclease treatment) and (ii) in different clones of the A549 cells as stated in the methods section on p.21 (Two different clones of human lung epithelial carcinoma A549 cells were used in the study: our laboratory's old A549 clone (experiments shown in Fig. 1, Fig. 3B and S1 Fig., S3B and S3C Fig., S6A and S6B Fig., RNase A treatment) and A549 from American Type Culture Collection (ATCC, experiments shown in Fig. 2 and Fig. 5, Fig. 6, S2B Fig., S4 Fig., S5 Fig., and S6B Fig. S1 nuclease-treatment)). This makes it difficult to interpret, if the data is due to differences in the timepoints or cell types, or if it is due to binding of the E1A probe to single stranded vDNA.

AU: This is a fair criticism, thank you. We have replaced the RNase A figure S6B in the revised manuscript. A new RNase A experiment was repeated in ATCC A549 cells using the same infections conditions as with the S1 nuclease-treated cells.

**Minor Comments:**

p.4: "AdV are non-enveloped, double-stranded DNA viruses that cause mild respiratory infections in immuno-competent hosts, and establish persistent infections, which can develop into life-threatening infections if the host becomes immuno-compromised [reviewed in 6]." Not all AdV cause respiratory diseases, the disease outcome of human AdV depends on the site of primary infection, which differs between the different AdV types.

AU: We have modified the text as follows: AdV are non-enveloped, double-stranded DNA viruses that cause mild respiratory, gastrointestinal or ocular infections…

p.7: The authors state, that "At the 17 h time point, about half of the cells had high numbers of protein VI transcripts, and most of them very high numbers of E1A transcripts.", however, the picture shown in Figure 1F shows a different phenotype, with low transcript levels of VI in E1A high cells and high transcript levels of VI in E1A low cells.

AU: This was perhaps a bit difficult to see in the overlay images since one has to distinguish between green and yellowish green. We have provided the individual channels along the overlay picture in Fig. S1D, and now it is clear that at 17h pi cells with high numbers of VI transcripts have also high numbers of E1A transcripts.

p.8: "This nuclear E1A signal is due to binding of the E1A probe to single-stranded vDNA in the replication centers (see below)." The authors should state here, that due to the binding of the probes to the single stranded vDNA in the replication centers, the nucleus was excluded from the analysis for Figure 1F in late timepoints.

AU: We have modified the text according to the Reviewer’s suggestion. The text is now as follows: ‘Due to further studies (see below), we assume that this nuclear E1A signal represents binding of the E1A probe to single-stranded vDNA in the replication centers. Accordingly, the nuclear area was excluded when quantifying the viral transcripts per cell in late timepoints (Fig. 1F).’

Due to this time point the author cannot state that the E1A staining seen (Fig. 1F; indicated with white arrows) are replication centers; this is just an assumption, since there is no evidence in Fig 1 the author cannot be sure; the author should change the text: "taking the following experiments into account...", "due to further studies (see below)..... we assume that..."

AU: We have modified the text according to the Reviewer’s suggestion; see also the previous comment above.

p.8: The authors should mention the figure they refer to, since there is no E1B-55K staining in Fig. 1F

AU: The text has been modified as follows: Whereas other time points showed relatively few E1A, E1B-55K or VI puncta over the nuclear area (Fig. 1B, 1F, S1A Fig.), clustered nuclear E1A signals were apparent at 23 h.

p.9: Which test was used to calculate the additional p-values?

AU: As stated in the Material and Methods section or the figure legends, the p-values were calculated either by a permutation test using custom-programmed R-script (the code has been deposited on Mendeley Data along with other data associated with this manuscript), or by Kolmogorov-Smirnov test using GraphPad Prism. GraphPad Prism was also used to calculate Spearman’s correlation coefficients and the associated approximate p values. In the revised manuscript, we have added the following sentense into the Material and Methods section / Statistical analyses: Spearman’s correlation tests were done using GraphPad Prism.

p.10: For the experiment for the correlation of viral genomes per cell and E1A transcripts in HDF-TERT cells (Figure S2C), the MOI is missing in the description of the results, as well as in the corresponding figure legends.

AU: We have indicated the theoretical MOI (~ 4800 virus particles per cell) in the figure legend and in the Material and Methods section. The actual MOI, i.e. the actual number of virus particles entering into the cells, could not be determined due to the long (15 h) incubation time of virus inoculum with the cells, which in turn was required because these cells bind AdV-C5 rather inefficiently. However, between 1 and 32 EdC-labeled virus genomes were detected per cell nucleus at 22 h pi.

11: calculation of correlation? rs? Why does the author combine S and G2/M phase? Fig. S3A show different values for the phases

AU: rs is the abbreviation for Spearman’s correlation coefficient, and, as indicated in the Material and Methods, we used GraphPad Prism to calculate the Spearman’s correlation coefficients.

Different methods to estimate cell cycle stages. DNA content method cannot separate S and G2/M with great confidence, whereas Kusabira Orange-hCdt1 and Azami-Green-hGeminin expressions in HeLa-Fucci cells allow more fine-tuned assessment of the cell cycle phases.

p.11: "Thus, the total intensity of nuclear DAPI signal can be used to accurately assign G1 vs S/G2/M stage to cells." The authors should also here refer to other papers, which showed that this correlation is feasible, as they did in the methods section (67. Roukos V, Pegoraro G, Voss TC, Misteli T. Cell cycle staging of individual cells by fluorescence microscopy. Nature protocols. 2015;10(2):334-48. Epub 2015/01/31. doi: 10.1038/nprot.2015.016. PubMed PMID: 25633629; PubMed Central PMCID:PMCPMC6318798.), and maybe also refer to a newer paper which deals with this technique: Ferro, A., Mestre, T., Carneiro, P. et al. Blue intensity matters for cell cycle profiling in fluorescence DAPI-stained images. Lab Invest 97, 615-625 (2017). https://doi.org/10.1038/labinvest.2017.13

AU: The integrated nuclear DAPI signal intensity is indeed a widely used method to assign cell-cycle stage to individual cells. We have added the second reference suggested by the Reviewer to the reference list for this method.

p.11: "Furthermore, when focusing on the highest E1A expressing cells, i.e. the cells with mean cytoplasmic E1A intensities larger than 1.5 × interquartile range from the 75th percentile, 71.9% of these cells were found to be in the G1 phase of cell cycle, whereas only 55.8% of cells in the total sampled cell population were G1 cells." The authors do not provide any reference to a figure within the manuscript or the supplements, which contains these data. Are these data not shown in the manuscript?

AU: These values are calculated from the data shown in Fig.3B. The source data supporting findings of this study (maximum projection images, excel files of the CellProfiler and Knime workflows) have now been deposited to Mendeley Data as stated in the Material and Methods / Data availability section of the revised manuscript and listed in Supplementary tables.

p.12: punctuation mistake; . instead of , To enrich G1 cells. AdV-C-5 (moi ~ 36250) was added. Why does the author switch between signal intensities and counting E1A puncta per cell (limited to 200) in the different experiments to illustrate accumulation of E1A transcripts?

AU: The same answer as above: the quantification method had to be adjusted to the number of virus transcripts in the cell at the time of analysis. The best quantification method is segmentation and counting the individual fluorescent puncta per cell, but, as stated in the manuscript, this method does not accurately quantify the mRNA puncta from maximum projections of confocal or widefield image stacks when the number of puncta per cell exceeds ~ 200. On the other hand, as shown in the quantification in the new S1C Fig., mean fluorescence intensity measurements per cell do not of course distinquish between cells having one vs. two mRNA puncta, but a relatively good correlation between puncta counting and fluorescence intensity measurements is achieved when cells have ≥ 10 transcripts per cell.

p.14: "For E1A (or E1B-55K), we did not detect transcriptional bursts with bDNA-FISH probes on nuclear vDNAs, either prior to or after accumulation of viral transcripts in the cell cytoplasm." The authors do not provide any reference to a figure within the manuscript or the supplements, which contains these data. Are these data not shown in the manuscript?

AU: This statement is based on hundreds of images we have analyzed during the course of the study. It is impossible to show all of these images, so in principle, this is “data not shown”. We have modified the text as follows: With hundreds of images analyzed, we never unambiguously detected transcriptional bursts with E1A (or E1B-55K) bDNA-FISH probes on nuclear vDNAs, either prior to or after accumulation of viral transcripts in the cell cytoplasm.

p.14: space between number and %

AU: Thank you for pointing this out. It has been corrected.

p.15: "This is was also seen in AdV-C5-EdC-infected cells" should be changed to "This was also seen in AdV-C5-EdC-infected cells"

AU: Thank you for pointing this out. It has been corrected.

Fig. 1B:

−figure legend does not indicate how cells were staine −also no description in the continuous text −which E1A transcripts are stained? all? 12S? 13S?

AU: The first sentence in Results section states that “We used fluorescent in situ hybridization (FISH) with probes targeting E1A, E1B-55K and protein VI transcripts followed by branched DNA (bDNA) signal amplification to visualize the appearance and abundance of viral transcripts in AdV-C5-infected A549 lung carcinoma cells.” Furthermore, the legend to Figure 1 starts with the title “Visualization of AdV-C5 E1A, E1B-55K and protein VI transcripts in infected cells by bDNA-FISH technique”, and the legend to Fig.1B mentions that “cells were stained with probes against E1A and E1B-55K mRNAs or E1A and protein VI mRNAs”. We are of the opinion that this is enough information to understand the figures.

The main text to Fig.1 also states that “The E1A probes covered the entire E1A primary transcript region and thus all E1A splice variants. The temporal control of E1A primary transcript splicing and E1A mRNA stability give rise predominantly to 13S and 12S E1A mRNAs at 5 h pi (references)”.

Fig. 1D: −difference in accumulation of viral transcripts is not that visible as in IF staining (Fig. 1B; Fig. 1S);

Fig. 1 or S1 Fig. do not show IF staining but signals from FISH.

−graph does not show any difference between E1A and E1B-55K

AU: The y-axes values in Fig.1D graph are arbitrary units and thus E1A and E1B-55K graphs are not directly comparable to each other. We have included into the revised manuscript S1B Fig., which shows quantification of E1A and E1B-55K fluorescent puncta per cell at the 5 h pi; the difference between E1A and E1B-55K was statistically significant.

Fig. 1F: −figure legend does not fit with labelling of IF images and continuous text −description says 22 h, while IF labeling and text (p. 7, last lane) mentions 23 h pi

AU: The figure annotations state the time of analyses as total time after virus addition to cells, whereas text stated the time of analyses as x h post virus removal since we wanted to stress that the input virus was incubated only for 1 h with the cells. However, Reviewers found this confusing, so we have changed the text in the revised manuscript so that time of analysis is stated as total time after virus addition to cells (as in the figure annotations). Only in the Material and Methods section we maintain the original 1 h + x h statement for the time of analysis.

Fig. 2A: −figure legend: lane 5 Punctuation wrong: azide-Alexa Fluor488. Alexa Fluor647

AU: Thank you for pointing this out. It has been corrected.

Fig. 4A: −difficulties to understand −author stated that promoter-driven EGFP expression is clearly dominated by G1 cells for E1A and by S/G2/M cells for CMV, however this is not clearly visible in the graph −no severe differences visible between CMV-eGFP and E1A-eGFP −author should include numbers for quantification and statistical calculations to illustrate the differences

AU: In the highest GFP expression bin, CMV-eGFP expressing cells have 43% cells in G1 and 50% in S/G2/M (n=2149). In comparison, E1A-GFP expressing cells have 58% cells in G1 and 35% in S/G2/M (n=2258). The difference in G1 cells in the highest eGFP bin is statistically significant (p

Fig. 4B: −amount of E1A protein levels calculated via IF (signal intensities) −immunofluorescence is not a suitable tool for protein quantification

AU: It is true that not all antibodies are suitable for IF (or for Western blot), and we cannot be certain that the monoclonal anti-E1A antibody used by us detects all E1A forms with different post-translational modifications with equal efficiency. However, IF is a widely accepted method to estimate protein levels in the cell, especially if the proteins like E1A accumulate in the nucleus (makes segmentation of the signal easy) and give a rather uniform nuclear staining pattern.

Fig. 5: −in A. it is stated, that E1A bDNA -FISH is not suitable, since it is too short to be detectable. However, in B E1A bDNA-FISH is used. is there a difference? −according to the method part just one E1A mRNA was used for the assays, why is it then not possible to use that one in Fig. 5A? −explanation of the procedure and the experiment is very confusing

AU: The Reviewer probably refers to Fig.6 here, not to Fig.5. The E1A introns are short (about 100 bases) and cannot be picked up with bDNA FISH probes. In Fig. 6B we were using the E1A bDNA-FISH probes, which were made against the AdV-C5 genome map positions 551-1630 to detect vDNA single strands of the E1A region and these single strands were long enough to be picked out by our E1A probes.

Fig. S6B: −authors want to show that it is RNase-insensitive, but S1 nuclease-sensitive

−two different A549 cell clones and two different time points are used for the treatments → not compareable to each other

AU: This is a fair criticism. We have replaced the RNase A figure in S6B Fig. in the revised manuscript. The new RNase A experiment was carried out in ATCC A549 cells using the same infections conditions as with the S1 nuclease-treated cells.

Material and Methods: −headings do not indicate which methods are explained −no clear structure AU: We have made minor changes to the headings of Material and Methods section. We have first explained in detail the bDNA-FISH method, but otherwise the order is according to the order of the figures.

Reviewer #2 (Significance (Required)):

highly significant manuscript very important for the virology field

my research topics are human adenoviruses and their replication cycle

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

**Summary:** Soumalainen et al have studied adenovirus viral gene expression and replication at a single-cell level. They explore the extent of correlation between incoming genome copy number and early gene expression and progression into the late phase, revealing substantial variation between cells in the numbers of E1A transcripts (the first gene expressed upon infection) that is not explained by differences in the numbers of viral genome templates in the cells. They also explore the relevance of cell cycle stage to this variability and show a positive correlation between G1 cell cycle stage and higher levels of gene activity, which explains at least part of the variation. To form these conclusions they have applied new methods to visualise and quantify single molecules of nucleic acid in single cells. The experiments are all carefully and fully described with full detail of materials. Overall the manuscript is well written and easy to follow.

**Major comments:**

All of the experiments appear to be done with rigour and their results reported with due regard to statistical significance etc. My major concern though is that they have been done, perhaps out of necessity to get detectable signals, at very high multiplicities of infection. A well-accepted standard to achieve infection of all cells in a culture is an MOI of 10 infectious units per cell. Even this is acknowledged not to represent the biology of natural infection and it is striking that, where technically feasible, lower MOI studies are more revealing of how a virus actually works. Here, the authors have used counts of particles rather than infectious units to determine MOI and for Ad5, the particle/pfu ratio is typically 20-100. Their MOIs though are 13,000 - 50,000 per cell, implying an infectious MOI of at least 130 for their A549 experiments, which are known to be readily infected by Ad5 from other work.

AU: Unlike common experiments done by others, we used a synchronized infection and removed the input virus after 1h incubation at 37°C. This type of infection initiation requires high input virus amounts, as opposed to studies in which the virus inoculum is incubated with cells for several hours/days, as is typically done in studies determining the infectious or plaque forming units in virus inoculum. Hence, the MOI used by others involved incubation of inoculum with cells over extended periods of time, and they cannot be compared to our pulsed infection conditions.

Although the calculated theoretical MOIs (physical particles/cell) were high in our experiments, only 0.1% – 0.2% of input virus particles bound to cells during the 1h incubation period (Fig. 1 A; this estimation is based on the ratios between Median values for the number of cell-associated viruses vs input virus numbers).

Furthermore, in the experiment described in Fig.2C (correlation of E1A transcripts per cell vs. viral genomes per cell), 42% of analyzed cells had ≤ 5 viral genomes/cell and 27.5% of analyzed cells had between 6-10 viral genomes per cell. Please note, that these are not high numbers.

The input virus amounts used were selected this way, because we aimed at getting a broader view of how virus transcription at early phases of infection responds to a varying number of virus genomes delivered to the nucleus. Therefore, we did not limit the analyses to a situation with 1 or less than 1 virus particles/genomes per cell.

In addition, the analyses of how cell cycle phase impacts the initiation of virus gene expression requires a relatively short time between virus inoculation and time point of analysis (i.e. a rather high MOI). Otherwise, as also pointed out by the Reviewer, the cells could have experienced more than one cell cycle phase during the duration of the experiment. Furthermore, although the initial natural infection probably starts with a very low MOI, the second round of infection is a high MOI infection due to a large number of progeny virus particles released from an infected cell.

Surprisingly, the authors do not see intracellular vDNA copy numbers that are fully reflective of this high MOI, with median intracellular vDNA of 75 /cell at the highest MOI. The authors should consider how the population distribution of vDNA /cell does or does not fit the predicted Poisson distribution. Nonetheless, at these high copy numbers / cell, there must surely be a risk that the variation in gene expression activity arises stochastically, out of competition between genomes for essential transcription factors. Given that multiple cellular factors are each required for E1A transcription, high genome copy numbers could actually inhibit E1A expression relative to cells with more modest copy numbers because limited supplies of individual factors are recruited to different viral genome copies.

AU: The “discrepancy” between theoretical MOI and the actual observed number of cell-associated virus particles or cell-associated virus genomes is explained above. Furthermore, we would like to point out that we have directly estimated the number of virus particles bound to cells with the input virus amounts used, something that is usually not done in other studies.

It is indeed theoretically possible that high nuclear genome numbers could lead to inhibition of transcription due to competition for limiting essential host factors. However, if we included only cells with ≤4 vDNA molecules per nucleus into the analysis (total number of cells analyzed was 258), then Spearman’s correlation coefficient for vDNA per nucleus vs E1A mRNAs per cell was 0.186 (p=0.0027). Thus, this would not support the notion that cells with moderate nuclear vDNA copy numbers would have a better correlation between the nuclear vDNA copies vs E1A mRNA counts per cell.

The vDNA/cell in Fig.2C does not fit predicted Poisson distribution, var/mean=9.129.

It is important for the analysis of correlation of gene expression with cell cycle that the virus has not, at the time point analysed, already perturbed the cell cycle (a well-known effect of infection) which the authors document in Suppl Fig3B. To my eye, the G1 peak in infected cells is somewhat narrower than in the control while the S/G2 bump is a little greater. The % of cells in each of the two gates needs to be shown to support the conclusion.

AU: In non-infected sample G1= 54.63% and S/G2/M = 45.37%, in infected cells G1= 51.4% and S/G2/M= 48.6%. We have added this information into the S3B Fig.

Turning to the experiments documenting a correlation between E1A expression and cell cycle stage, the authors interpret their findings in terms of the stage the cells are at when the analysis was done (G1 stage cells have more E1A transcripts). The key experiment (Fig 3B) is analysed at only 4 h pi, so substantial progression from G2/M back to G1 after virus addition can probably be discounted, but the point should be discussed. The authors also use release from G1 in another cell line to support their argument that G1 supports higher levels of E1A expression (Fig 3C). Here, they elect to exclude all cells with fewer than 50 E1A transcripts from their analysis. The reason for this is completely obscure and isn't obviously justified; conceivably it could bias the outcome of the experiment. At minimum, this decision needs to be carefully explained; ideally, the full data set should be used.

AU: Fig.3B: As suggested by the Reviewer, we have added to the main text the following explanation: “We used a high MOI infection (median 75 cell-associated virus particles, Fig. 1A) in order to achieve a rapid onset of E1A expression so that the time between virus addition and analysis was short. Thus, it is not expected that a substantial number of cells would have changed their cell cycle status during the experiment.”

Fig.3C: We show the results also from the full data set of infected cells, i.e., cells with ≥ 1 E1A puncta in S3D Fig. We excluded the cells without zero E1A puncta because with these cells it is impossible to know whether they received no virus or whether E1A transcription had not yet started. Permutation test indicated that the difference between the starved+starved and starved+FCS is statistically significant even in this case. Because both samples are dominated by cells with low E1A counts, we log-transformed the E1A values for the box plot figure.

The authors note the highest level of E1A activity (as opposed to RNA) was in G1/S cells and suggest that high E1A cells advance preferentially into S. Whilst in line with the literature that E1A promotes progression into S, an alternative explanation is simply that there is a time lag between RNA accumulation and protein accumulation, during which progression through the cycle would be expected.

AU: This is a valid point, and we have modified the text as follows: “… which could reflect the advancement of high E1A expressing cells into S-phase. However, considering the time between virus addition and analysis (10.5 h), we cannot exclude the possibility that the observed G1/S preference is at least partly due to time-dependent progression of G1 cells to G1/S.”

**Minor comments:** Fig 1 and elsewhere. Given that the 1 h incubations with virus were done at 37 C, the convention would be to include this period in the time post-infection at which harvest / fix time points are quoted. There is inconsistency between text and legend with 12 h pi being sometimes represented as 11 h after virus removal; this is an unnecessary confusion.

AU: We have modified the text so that hours pi always include the 1h incubation with the input virus. Only in the Material and Methods section we kept the original 1h virus binding – fixing at xh post virus removal.

Results description prior to the ref to Fig 1B: unclear what this is supposed to mean.

AU: We have now slightly modified the first paragraph of the Results section. We mention the benefits of the bDNA signal amplification method and explain the experimental set up, i.e. that the input virus was incubated with the cells only for 1h. We also justify why we used a short incubation for the virus inoculum.

Fig 4A: provide % of cells in each gate in each histogram.

AU: In the highest GFP expression bin, CMV-eGFP expressing cells have 43% of cells in G1 and 50% in S/G2/M. In comparison, E1A-GFP expressing cells have 58% of cells in G1 and 35% in S/G2/M. This has been added to the figure, and it is also mentioned in the main text. Furthermore, we added to the text the results from Two Proportion Z-test to show that the proportion difference of G1 cells in the highest bin was statistically significant (p

Fig 5: bottom right panel x axis label is wrong

AU: Thank you for pointing out this. This has been corrected.

In the presentation of Fig 6, it would be much clearer for the reader if the detected replication foci (ss DNA detected as E1A puncta) were referred to as something other than E1A puncta. There is too much scope for confusion with the earlier experiments in which E1A RNA was detected.

AU: We agree. In the revised manuscript, we refer to these puncta in the text as E1A ssDNA-foci.

Reviewer #3 (Significance (Required)):

The study represents the application of state of the art single-molecule visualization techniques to an as yet not understood aspect of virus infection. That said, there is prior experimentation in this area, which the authors fully acknowledge and build upon. The new work is largely descriptive, in that it reveals very clearly the discrepancy between genome copy number and amounts of mRNA without seeking to explain these, beyond the cell cycle analysis. Whilst there is a better correlation between vDNA number and transcript once the data are stratified by cell cycle stage, it is still not strong (Fig 5), indicating that other substantial contributing factors remain to be described.

The work will be of interest certainly to adenovirologists, but also to others who study virus infections - particularly nuclear-replicating DNA viruses such as herpesviruses - where similar considerations are likely to apply.

Expertise: adenovirus; gene expression; virus-host interactions; molecular biology

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Referee #3

Evidence, reproducibility and clarity

Summary: Soumalainen et al have studied adenovirus viral gene expression and replication at a single-cell level. They explore the extent of correlation between incoming genome copy number and early gene expression and progression into the late phase, revealing substantial variation between cells in the numbers of E1A transcripts (the first gene expressed upon infection) that is not explained by differences in the numbers of viral genome templates in the cells. They also explore the relevance of cell cycle stage to this variability and show a positive correlation between G1 cell cycle stage and higher levels of gene activity, which explains at least part of the variation. To form these conclusions they have applied new methods to visualise and quantify single molecules of nucleic acid in single cells. The experiments are all carefully and fully described with full detail of materials. Overall the manuscript is well written and easy to follow.

Major comments:

All of the experiments appear to be done with rigour and their results reported with due regard to statistical significance etc. My major concern though is that they have been done, perhaps out of necessity to get detectable signals, at very high multiplicities of infection. A well-accepted standard to achieve infection of all cells in a culture is an MOI of 10 infectious units per cell. Even this is acknowledged not to represent the biology of natural infection and it is striking that, where technically feasible, lower MOI studies are more revealing of how a virus actually works. Here, the authors have used counts of particles rather than infectious units to determine MOI and for Ad5, the particle/pfu ratio is typically 20-100. Their MOIs though are 13,000 - 50,000 per cell, implying an infectious MOI of at least 130 for their A549 experiments, which are known to be readily infected by Ad5 from other work.

Surprisingly, the authors do not see intracellular vDNA copy numbers that are fully reflective of this high MOI, with median intracellular vDNA of 75 /cell at the highest MOI. The authors should consider how the population distribution of vDNA /cell does or does not fit the predicted Poisson distribution. Nonetheless, at these high copy numbers / cell, there must surely be a risk that the variation in gene expression activity arises stochastically, out of competition between genomes for essential transcription factors. Given that multiple cellular factors are each required for E1A transcription, high genome copy numbers could actually inhibit E1A expression relative to cells with more modest copy numbers because limited supplies of individual factors are recruited to different viral genome copies. It is important for the analysis of correlation of gene expression with cell cycle that the virus has not, at the time point analysed, already perturbed the cell cycle (a well-known effect of infection) which the authors document in Suppl Fig3B. To my eye, the G1 peak in infected cells is somewhat narrower than in the control while the S/G2 bump is a little greater. The % of cells in each of the two gates needs to be shown to support the conclusion.

Turning to the experiments documenting a correlation between E1A expression and cell cycle stage, the authors interpret their findings in terms of the stage the cells are at when the analysis was done (G1 stage cells have more E1A transcripts). The key experiment (Fig 3B) is analysed at only 4 h pi, so substantial progression from G2/M back to G1 after virus addition can probably be discounted, but the point should be discussed. The authors also use release from G1 in another cell line to support their argument that G1 supports higher levels of E1A expression (Fig 3C). Here, they elect to exclude all cells with fewer than 50 E1A transcripts from their analysis. The reason for this is completely obscure and isn't obviously justified; conceivably it could bias the outcome of the experiment. At minimum, this decision needs to be carefully explained; ideally, the full data set should be used.

The authors note the highest level of E1A activity (as opposed to RNA) was in G1/S cells and suggest that high E1A cells advance preferentially into S. Whilst in line with the literature that E1A promotes progression into S, an alternative explanation is simply that there is a time lag between RNA accumulation and protein accumulation, during which progression through the cycle would be expected.

Minor comments:

Fig 1 and elsewhere. Given that the 1 h incubations with virus were done at 37 C, the convention would be to include this period in the time post-infection at which harvest / fix time points are quoted. There is inconsistency between text and legend with 12 h pi being sometimes represented as 11 h after virus removal; this is an unnecessary confusion.

Results description prior to the ref to Fig 1B: unclear what this is supposed to mean.

Fig 4A: provide % of cells in each gate in each histogram.

Fig 5: bottom right panel x axis label is wrong

In the presentation of Fig 6, it would be much clearer for the reader if the detected replication foci (ss DNA detected as E1A puncta) were referred to as something other than E1A puncta. There is too much scope for confusion with the earlier experiments in which E1A RNA was detected.

Significance

The study represents the application of state of the art single-molecule visualization techniques to an as yet not understood aspect of virus infection. That said, there is prior experimentation in this area, which the authors fully acknowledge and build upon. The new work is largely descriptive, in that it reveals very clearly the discrepancy between genome copy number and amounts of mRNA without seeking to explain these, beyond the cell cycle analysis. Whilst there is a better correlation between vDNA number and transcript once the data are stratified by cell cycle stage, it is still not strong (Fig 5), indicating that other substantial contributing factors remain to be described.

The work will be of interest certainly to adenovirologists, but also to others who study virus infections - particularly nuclear-replicating DNA viruses such as herpesviruses - where similar considerations are likely to apply.

Expertise: adenovirus; gene expression; virus-host interactions; molecular biology

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Referee #2

Evidence, reproducibility and clarity

The authors show heterogeneity of AdV-C5 mRNA transcript quantity and dynamics in different cell types, which is regulated by the cell cycle phase and does not correlate to incoming viral DNA, using single molecule RNA FISH technologies and detection of incoming viral DNA by EdC labeling.

Major Comments:

The authors change the MOI used in their experiments (7 different MOIs are used throughout the paper) in a manner that appears randomly and without explanation. (54400 for Figure 1A, 1B, 3B, S3B; 37500 for Figure 1C; 23440 for Figure 2A, 2C, S5A; 13600 for Figure 1A, 1D; 36250 for Figure 3C, S3D; 11200 for Figure 4B; 23400 for Figure 6B). The authors should provide explanation, why these changes in MOIs are necessary. The authors use mean fluorescence intensity of E1A probes per cell as estimate for viral transcript abundance for some of their experiments (Figure 1D, E, 3B), and count E1A punctae as measure for E1A transcripts in other experiments (Figure 2C, 3C, 5), without showing data, that these measures correlate. Problematic is hereby, that not all E1A punctae have the same signal intensity, as can be seen in Figure S1, which makes the estimation of the correlation of E1A punctae (= number of transcripts) and fluorescence intensity difficult. The authors should provide both (E1A punctae counts and estimation via fluorescence intensity) for at least one experiment, to prove, that the estimation of E1A transcript levels via fluorescence intensity is feasible. p.15: "The nuclear E1A signals in AraC-treated cells were resistant to RNase A, but they were dampened by treatment with S1 nuclease (S6B Fig)." The authors make this statement based on (i) two completely different timepoints (12 h.p.i. for RNaseA treatment, 24.5 h.p.i. for S1 nuclease treatment) and (ii) in different clones of the A549 cells as stated in the methods section on p.21 (Two different clones of human lung epithelial carcinoma A549 cells were used in the study: our laboratory's old A549 clone (experiments shown in Fig. 1, Fig. 3B and S1 Fig., S3B and S3C Fig., S6A and S6B Fig., RNase A treatment) and A549 from American Type Culture Collection (ATCC, experiments shown in Fig. 2 and Fig. 5, Fig. 6, S2B Fig., S4 Fig., S5 Fig., and S6B Fig. S1 nuclease-treatment)). This makes it difficult to interpret, if the data is due to differences in the timepoints or cell types, or if it is due to binding of the E1A probe to single stranded vDNA.

Minor Comments:

p.4: "AdV are non-enveloped, double-stranded DNA viruses that cause mild respiratory infections in immuno-competent hosts, and establish persistent infections, which can develop into life-threatening infections if the host becomes immuno-compromised [reviewed in 6]." Not all AdV cause respiratory diseases, the disease outcome of human AdV depends on the site of primary infection, which differs between the different AdV types.

p.7: The authors state, that "At the 17 h time point, about half of the cells had high numbers of protein VI transcripts, and most of them very high numbers of E1A transcripts.", however, the picture shown in Figure 1F shows a different phenotype, with low transcript levels of VI in E1A high cells and high transcript levels of VI in E1A low cells.

p.8: "This nuclear E1A signal is due to binding of the E1A probe to single-stranded vDNA in the replication centers (see below)." The authors should state here, that due to the binding of the probes to the single stranded vDNA in the replication centers, the nucleus was excluded from the analysis for Figure 1F in late timepoints. Due to this time point the author cannot state that the E1A staining seen (Fig. 1F; indicated with white arrows) are replication centers; this is just an assumption, since there is no evidence in Fig 1 the author cannot be sure; the author should change the text: "taking the following experiments into account...", "due to further studies (see below)..... we assume that..." p.8: The authors should mention the figure they refer to, since there is no E1B-55K staining in Fig. 1F

p.9: Which test was used to calculate the additional p-values?

p.10: For the experiment for the correlation of viral genomes per cell and E1A transcripts in HDF-TERT cells (Figure S2C), the MOI is missing in the description of the results, as well as in the corresponding figure legends.

p. 11: calculation of correlation? rs? Why does the author combine S and G2/M phase? Fig. S3A show different values for the phases

p.11: "Thus, the total intensity of nuclear DAPI signal can be used to accurately assign G1 vs S/G2/M stage to cells." The authors should also here refer to other papers, which showed that this correlation is feasible, as they did in the methods section (67. Roukos V, Pegoraro G, Voss TC, Misteli T. Cell cycle staging of individual cells by fluorescence microscopy. Nature protocols. 2015;10(2):334-48. Epub 2015/01/31. doi: 10.1038/nprot.2015.016. PubMed PMID: 25633629; PubMed Central PMCID:PMCPMC6318798.), and maybe also refer to a newer paper which deals with this technique: Ferro, A., Mestre, T., Carneiro, P. et al. Blue intensity matters for cell cycle profiling in fluorescence DAPI-stained images. Lab Invest 97, 615-625 (2017). https://doi.org/10.1038/labinvest.2017.13

p.11: "Furthermore, when focusing on the highest E1A expressing cells, i.e. the cells with mean cytoplasmic E1A intensities larger than 1.5 × interquartile range from the 75th percentile, 71.9% of these cells were found to be in the G1 phase of cell cycle, whereas only 55.8% of cells in the total sampled cell population were G1 cells." The authors do not provide any reference to a figure within the manuscript or the supplements, which contains these data. Are these data not shown in the manuscript?

p.12: punctuation mistake; . instead of , To enrich G1 cells. AdV-C-5 (moi ~ 36250) was added. Why does the author switch between signal intensities and counting E1A puncta per cell (limited to 200) in the different experiments to illustrate accumulation of E1A transcripts?

p.14: "For E1A (or E1B-55K), we did not detect transcriptional bursts with bDNA-FISH probes on nuclear vDNAs, either prior to or after accumulation of viral transcripts in the cell cytoplasm." The authors do not provide any reference to a figure within the manuscript or the supplements, which contains these data. Are these data not shown in the manuscript?

p.14: space between number and %

p.15: "This is was also seen in AdV-C5-EdC-infected cells" should be changed to "This was also seen in AdV-C5-EdC-infected cells"

Fig. 1B:

−figure legend does not indicate how cells were staine

−also no description in the continuous text

−which E1A transcripts are stained? all? 12S? 13S?

Fig. 1D:

−difference in accumulation of viral transcripts is not that visible as in IF staining (Fig. 1B; Fig. 1S);

−graph does not show any difference between E1A and E1B-55K

Fig. 1F:

−figure legend does not fit with labelling of IF images and continuous text

−description says 22 h, while IF labeling and text (p. 7, last lane) mentions 23 h pi

Fig. 2A:

−figure legend: lane 5 Punctuation wrong: azide-Alexa Fluor488. Alexa Fluor647

Fig. 4A:

−difficulties to understand

−author stated that promoter-driven EGFP expression is clearly dominated by G1 cells for E1A and by S/G2/M cells for CMV, however this is not clearly visible in the graph

−no severe differences visible between CMV-eGFP and E1A-eGFP

−author should include numbers for quantification and statistical calculations to illustrate the differences

Fig. 4B:

−amount of E1A protein levels calculated via IF (signal intensities)

−immunofluorescence is not a suitable tool for protein quantification

Fig. 5:

−in A. it is stated, that E1A bDNA -FISH is not suitable, since it is too short to be detectable. However, in B E1A bDNA-FISH is used. is there a difference?

−according to the method part just one E1A mRNA was used for the assays, why is it then not possible to use that one in Fig. 5A?

−explanation of the procedure and the experiment is very confusing

Fig. S6B:

−authors want to show that it is RNase-insensitive, but S1 nuclease-sensitive

−two different A549 cell clones and two different time points are used for the treatments → not compareable to each other

Material and Methods:

−headings do not indicate which methods are explained

−no clear structure

Significance

highly significant manuscript very important for the virology field

my research topics are human adenoviruses and their replication cycle

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Suomalainen et al. describes a fluorescence-based approach combined with high-resolution confocal microscopy to study the heterogeneity of adenovirus infection in a population of human cells. The main focus of the authors is the detection of viral transcripts in infected cells, how this correlates with viral genomes, the cell state, and how it varies between different cells in a single population. The paper is generally well written and easy to read, with a few typos, although I found parts of it to be somewhat length and repetitive. Particularly the results section could be pruned somewhat for readability and clarity. The major limitation of the study as it stands is it's overall impact and novelty, which limits journal selection somewhat. A very similar study was recently published, which the authors cite (Krzywkowski et al, 2017). Nevertheless, I think the study design is rigorous and well executed, but I do have some specific comments which may enhance it's overall impact and novelty.

Major: Results "Visualization of AdV-C5..." section:

Why not also look at normal cells that can be synchronized? Cancer cells, such as A549 will by definition be highly heterogenous and at all phases of the cell cycle. Primary non-transformed cells can easily be synchronized by contact inhibition and are much more physiologically relevant. "The virus particles bound..." - Can the spatial resolution of a confocal microscope truly differentiate individual particles that are sub-wavelength in size? What about the sensitivity for single particles? Some sort of experiment to show that single particles can be detected should be performed and shown to assure the readers that this is in fact possible. Furthermore, even when based on the particle to pfu ratio, the MOI would still be nearly 2000pfu/cell, so the actual number of observed particles is an order of magnitude lower than what was applied to the cells.

Fig. 4 - I am not certain that the observed difference is significant, at least looking at it, beyond the width difference of the peaks, highest expression for both is largely in G1. It would be nice to see this using a western blot of cell cycle sorted cells, which can easily be accomplished using FACS. Page 15, 2nd paragraph. It would be valuable and informative to determine whether there is heterogeneity in histone association with these different vDNAs and whether these histones exhibit divergent modifications (enabling or restricting transcription). Same as above. I am rather surprised that the DBP signal did not correlate well with vDNA signal, particularly for the larger replication centers. How can this be reconciled? Was there an increase in overall vDNA signal later in infection? It is important to know this as it determines whether the observed vDNA signal is real or could be caused by viral RNA or other background causes (non-infected controls notwithstanding). Can the signal be detected with inactivated viruses (via UV for example?)

Page 18, 1st paragraph. It would be interesting to determine whether there was association between pol II and those genomes that showed no E1A, similarly to the histone suggestion. What about things like viral chromatin organization? Soriano et al. 2019 showed how E1A and E4orf3 work in tandem to alter viral chromatin organization by varying histone loading on the viral genome. Fig. 2. Can you really say that a single dot correlates with a single transcript? Has that been validated in any way?

Minor:

Page 5, last paragraph. "Transcirpts from the viral late transcription unit,..." This is not correct as recently shown by Crisostomo et al, 2019.

Page 10, "... because AdvV-infected cells are less well adherent..." This is not strictly true as loss of attachment only occurs later on in infection. It would be helpful to have statistical significance indicated directly in the figures.

The very high MOIs used are concerning, could these have negative effects on the cell viability or overall state?

There are a few typos and such that should be corrected.

Significance

As I stated above, the work is interesting and significant, to a degree. The major limitation is that the novelty is low as a paper published in 2017 (cited by the authors) used a very similar approach to investigate a similar problem. In addition, there are multiple other recent papers looking at cell populations in the context of adenovirus infection, and whether a single cell or population based approach is better is unclear. This is something the authors might want to strengthen prior to submission.

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Reply to the reviewers

First of all, we thank all reviewers for their constructive suggestions and comments.

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

This group has been at the forefront recently of using imaging technologies to understand how chromosome segregation is coordinated in mammalian oocytes, and why errors occur. In the current paper they examine the dynamics of microtubule organising centres (which effectively replace centrioles/centrosomes in oocytes) in MI. The imaging of oocytes in this paper is beautiful. The major findings are (1) that MTOCs that are supposed to be at the spindle pole sometimes end up at the spindle equator, and this is documented very beautifully and (2) the correct positioning of MTOCs at the spindle pole appears to require kinetochore microtubules, as indicated by experiments manipulating the kinetochore component NDC80.

We appreciate the reviewer’s comment and clear description of our study.

**Major Comments**

As such the major claims of the paper are basically well supported. However, the analyses are is almost entirely restricted to prometaphase/metaphase, and the conclusions are relatively limited. The salient omission is any analysis of MTOC/chromosome relationship during anaphase. Were the paper to be extended to determine whether the lingering of MTOCs at the spindle equator is related to chromosome segregation error, that would increase the reach and importance of the work substantially. Specifically:

Can tracking experiments be performed to determine whether the chromosome that shows movement similarities to the errant MTOC is more/less likely to missegregate? Complete tracking as these authors are expert at should achieve this, or photo-labelling the desired chromosome.

Thank you for your comment. In our experimental system, oocytes rarely exhibit chromosome segregation errors (

Can the position of MTOCs (proportion that linger at the equator) be manipulated in the absence of other defects to determine whether this increases errors (lagging at anaphase, metaphase-II chromosome counting spreads)?

We agree with the reviewer that a specific manipulation of MTOC positions is exactly what we would need to investigate the significance of central MTOCs. Unfortunately, there are currently no tools available to specifically manipulate MTOC positions without other defects. Therefore, the significance of central MTOCs is currently unclear. In the revised manuscript, we will state these points in Discussion.

The above analysis would have to be well supported by controls showing that these constructs are having no impact on normal anaphase (proportion of oocytes completing meiosis-I, likelihood of lagging chromosomes etc).

Thank you for the comment. As we answered above, control oocytes rarely exhibit chromosome segregation errors or lagging chromosomes (

Related to the above, though I appreciate a fixed metaphase image of MTOC immunofluorescence is presented, the paper is about the dynamics of MTOCs and thus nonetheless relies heavily on the live imaging of cep192. The core results should be confirmed using another (substantially different) MTOC probe. *This final comment applies to the current metaphase data, regardless of whether the study is ultimately extended*

Thank you for the suggestion. We will confirm the dynamics of MTOCs at metaphase with mEGFP-Cdk5Rap2, another established marker of MTOCs.

Reviewer #1 (Significance (Required)):

As explained above, as presented this paper is largely scientifically sound, but far more limited in scope than this groups other recent papers. As explained above, the paper would be made more impactful and the readership broadened if a relationship between MTOC position/movement and segregation problems were established. Or on the other hand if it were established why some MTOCs sometimes linger at the spindle equator. Whilst to my knowledge this is the first time that equator MTOCs have been documented so carefully, oocyte cell biologists may not find the core observation that MTOCs are occasionally at the spindle equator extremely surprising.

Thank you for your helpful suggestions. Due to lack of tools to specifically manipulate MTOC positions, we are unfortunately not able to directly address whether MTOC position/movement contributes to chromosome segregation problems. On the other hand, we are currently investigating to answer your important question ‘why some MTOCs sometimes linger at the spindle equator’. We speculate that MTOCs become central due to unstable kinetochore-microtubule attachments, which are predominantly observed at early metaphase in normal oocytes. To test this idea, we are currently investigating whether the appearance of central MTOCs are prevented by forced stabilization of kinetochore-microtubule attachments with Ndc80-9A. Our pilot analysis thus far supports this idea. In light of your suggestions, we will incorporate the results into the revised manuscript.

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

I am commenting on the work of Courtois et al. as an expert in the biochemistry of spindle formation with a focus on acentriolar assembly.

First and foremost, this a technically excellent study with a number of very interesting and well-documented observations, which are highly relevant for our understanding of the mechanisms of acentriolar spindle formation in the mouse oocyte model. In principle, the manuscript is in a very mature state. However, my major concern at this point would be that there is a break in the story. It starts describing the (very interesting) observation of "central MTOCs". After thoroughly investigating how these behave, the authors stop and look at overall MTOCs distribution after loss of stable MT-kinetochore interactions based on oocytes expressing the Ndc80_9D mutant instead of wt Ndc80. The two parts are experimentally and conceptually not well connected.

We appreciate your comments on our techniques and novel observations in this study, and thank you for your helpful suggestions.

Answering the following questions may help to further develop the paper:

If I understand the arguments correctly, central MTOCs are an "accident" on the way to complete meiosis I spindle formation, which will eventually be corrected and all MTOCs clustered at the poles. Thus, they may serve as an assay for spindle assembly fidelity and kinetics (?). At this point, the reader is left with the observation without efforts to explain the meaning of this observation, ideally experimentally, or at least in a valid discussion.

Thank you for your thoughtful comment. We agree that we should clearly explain our view on central MTOCs. We indeed speculate that central MTOCs are an “accident” due to unstable kinetochore-microtubule attachments, which are normally pronounced at early metaphase.

We will revise the manuscript as follows: (1) Following the section for the observation of central MTOCs, we will state our hypothesis that central MTOCs may appear due to unstable kinetochore–microtubule attachments. (2) We will introduce our experiment of the manipulation of kinetochore–microtubule attachment stability as a test for our hypothesis. (3) We will present new results of our analysis for the effects of kinetochore–microtubule attachment stability on the appearance of central MTOCs (please see below).

Enthusiasm for the technically excellent experiments using the Ndc80 variants are somewhat reduced as conclusions from these experiments are published in the parallel paper of the same laboratory (Yoshida et al.). Due to my opinion, it may thus be even more important to connect these observations with the first part described central MTOCs and to clarify their significance.

Thank you for the important suggestion.

First, we agree that we should connect our observations of central MTOCs to the phenotypes of Ndc80 manipulations. To do this, we will reanalyze our dataset to quantify the effects of Ndc80 manipulations on central MTOCs. Our pilot analysis thus far suggests that the forced stabilization of kinetochore–microtubule attachments by Ndc80-9A reduces the appearance of central MTOCs. This would support our idea that central MTOCs appear due to unstable kinetochore–microtubule attachments.

Second, we agree with the reviewer that experimental clarification of the significance of central MTOCs would be nice. However, as outlined above, we unfortunately have no tool to directly address the significance of MTOC positioning in the fidelity of spindle assembly and chromosome segregation. Although we assume that MTOC positioning is critical for spindle assembly fidelity, as generally thought based on previous studies (Breuer et al., 2010; Clift and Schuh, 2015; Schuh and Ellenberg, 2007), the significance of MTOC positioning in spindle assembly remains uncertain, as you (and also the reviewer 1) point out. We will discuss these points in the revised manuscript.

Shown if in Fig. 3B but not fully explained: How does the distribution of what is defined as central MTOCs behave in Ndc80_wt and Ndc80_9A mutant oocytes? Do the variants differ, i.e. are there fewer, or less persistent central MTOCs in the 9A mutant? Would they differ in kinetics of appearance and "rescue" to the poles?

Thank you for the question. As outlined above, we will reanalyze our dataset to quantify the effects of Ndc80-9A on the behavior of central MTOCs. Our pilot analysis suggests that the forced stabilization of kinetochore–microtubule attachments suppresses the appearance of central MTOCs.

Similarly: is there a correlation of central MTOC appearance, Ndc80 phosphorylation/stability of kinetochore attachment and Anaphase I onset? The authors mention that oocytes expressing the 9A mutant go faster into Anaphase.

Thank you for this comment. First, we will investigate whether the levels of Ndc80 phosphorylation at kinetochores has any correlations to the distance to central MTOCs. Second, we will address whether microtubules connect kinetochores to central MTOCs. Third, we will perform the tracking of chromosomes that showed correlated motions to closely positioned MTOCs until anaphase onset.

The observation that "central MTOCs exhibited correlated motions with closely positioned kinetochores" is poorly defined, yet an important observation. Does this mean some sort of short k-fibers remain to connect central MTOCs and kinetochores? Wouldn't one expect that the loss of stable end-on-attachment causes MTOCs to become central? How does this fit into a/the model?

We believe these concerns will be addressed by the experiments/analyses proposed above. First, we will check if central MTOCs are connected to kinetochores by microtubules. Second, we indeed speculate that loss of stable kinetochore-microtubule attachment allows MTOCs to become central. We will test this idea by quantifying the appearance of central MTOCs in Ndc80-9A-expressing oocytes.

Along the same lines: The authors hype their conclusion that kinetochores dominate meiosis I spindle formation based on the observation that loss of kinetochore functions results in less well-organized spindle poles and worse MTOC "confinement". This may mean that kinetochores, together with MTOCs, maintain stable k-fibers in meiosis, as shown here and in Yoshida et al. When one or the other end of k-fibers is destabilized (loss of end-on-attachment, loss of MTOC attachment), the fibers collapse and the remaining minus-or-plus-end associated structure loses its destination. We then see central MTOCs and/or kinetochores at poles. In this respect, the interpretation / discussion should be less "kinetochore-centered".

We agree with your thoughtful comment that the regulations of minus-ends (e.g. MTOCs) and of plus-ends (e.g. kinetochores) are equally relevant for spindle bipolarization. We will tone down our kinetochore-centered view in the Abstract and Discussion and revise them into more balanced statements.

Is there any way to determine the efficiency of Ndc80 knockdown in the gene replacement respective experiment? I share the view of the authors that their method may be more efficient and may explain apparent discrepancies to previous studies on Ndc80-9A (Guy and Homer, 2013) with more dramatic effects on spindle geometry. However, at that point, this remains speculative. For instance, one may also speculate vice versa that the ko strategy used here is less efficient in a maternally dominated system and leaves behind more wt Ndc80, which better compensates defects seen in the 9A mutant.

Our gene deletion strategy (Zp3-Cre Ndc80f/f) resulted in >90% depletion of the Ndc80 protein (estimated by Western blot; Supplementary Figure 1c in Yoshida et al, Nat Commun 2020). On the other hand, Gui and Homer report that their morpholino-based depletion strategy resulted in 60–70% depletion of the Ndc80 protein (estimated by Western blot; Figure 1B in Gui and Homer, Dev Cell 2013). Thus, the depletion was more efficient in our experimental system. We will add this information in the manuscript.

Reviewer #2 (Significance (Required)):

Courtois et al present data on mechanisms governing spindle assembly in mouse oocytes. Mouse oocytes serve as model system for spindle formation in the absence of centriole-based MTOCs. At the onset of meiosis I, numerous MTOCs form, which shape a mass ("ball") of MT nucleated around chromatin into a bipolar structure. Accumulating evidence indicates that kinetochores play an important role in acentriolar spindle formation in mouse oocytes, yet the mechanisms behind kinetochore action remains unclear.

Here, Courtois et al. analyze spindle formation in live mouse oocytes using 3D-time-lapse imaging. They use fluorescently tagged Cep192 to track MTOCs and Histone H2B or CENP-C to visualize chromatin or kinetochores. In the first part, the authors deal with the appearance of "central MTOCs", i.e. aggregates of centrosomal protein(s) that, apparently, fail to remain stably integrated into the spindle pole clusters on MTOCs during spindle formation. The authors convincingly demonstrate that these central MTOCs can be seen in the majority of spindles investigated. They demonstrate that central MTOCs generally come from positions at poles from where they "fall back" towards chromosomes. Central MTOCs may even cross the spindle and end up at opposite poles from where they originated from. Interestingly, central MTOCs are often found next to kinetochores.

In the second part, the authors focus on the role of kinetochores and their stable MT attachment for spindle formation in general and bipolarity/pole organization in particular. The same lab has published data on the role of kinetochores in meiosis I spindle very recently (Yoshida et al. Nat Comm, 2020). Here, they successfully exploit Ndc80 phospho-mutants to compare MTOC distribution in oocytes with reduced or increased end-on-attachment. The data show that stable end-on attachment determines stable MTOC clustering at spindle poles and governs the maintenance of bipolarity and spindle length.

Thank you for your clear description of our study.

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

In order to assemble a bipolar structure, acentrosomal spindles relay on multiple non-centrosomal pathways. Mouse oocytes specifically build bipolar spindles by sorting and clustering of microtubule organizing centers (MTOCs). While microtubule cross-linkers, spindle motors and microtubule nucleators are involved; the role of kinetochores and kinetochore-microtubule attachments in meiotic spindle assembly and maintenance has not been thoroughly tested. Using an impressive combination of live cell imaging and semi-automated image analysis, Courtois et al. quantified MTOC behavior in bipolar mouse oocyte spindles and found an ongoing MTOC sorting in metaphase and instances of MTOC-kinetochore associations. The authors further employed an elegant genetic system to replace NDC80 in maturing oocytes with a mutant almost completely unable to form stable microtubule-kinetochore attachments. The data show lack of MTOC confinement at the spindle poles and increased spindle elongation while maintaining spindle bipolarity. The authors concluded that stable kinetochore-microtubule attachments are required to confine MTOCs at the poles, which in turn sets an optimal spindle length. Overall, the data are of very high quality and clearly presented, the manuscript is easy to follow, and the methods are comprehensively described. One concern is the lack of mechanistic link between the natural metaphase MTOC sorting (Fig. 1-2) and massive MTOC rearrangements observed with the NDC80-9D mutant (Fig. 3). A second concern is that deficient MTOC confinements and spindle elongation observed with the 9D mutant could be due unaligned chromosomes rather than lack of stable kinetochore-microtubule attachments, which is the authors' interpretation.

**Major Points:**

1) Massive MTOC rearrangements (Supplementary Video 6) are reminiscent of spindle assembly defects or spindle collapse. Since these spindles do not reach a normal metaphase and seem to change shape (Supplementary Video 6; 11:10), it is difficult to differentiate between spindle assembly and spindle maintenance defects. Is there a difference in the timing of bipolar spindle assembly for NDC80-9D vs WT? If so, one interpretation is that stable attachments not only ensure MTOC confinement but also contribute to bipolar spindle assembly.

We apologize for the lack of explanation for the spindle dynamics seen in Supplementary Video 6, 11:10. At this time point, the spindle rotated in 3D, which appeared as if the spindle collapsed in the z-projection movie. We will add this explanation into the legend.

Our quantitative analysis of spindle shape in 3D indicated no increased collapse in Ndc80-9D, based on the signals of the spindle marker EGFP-Map4. Moreover, we observed no detectable difference in the timing of the onset of bipolar spindle assembly, as long as we define it with EGFP-Map4 signals. These results are shown in Figure 4B.

2) Fig. 1-2 vs Fig. 3 - It is not clear how the discrete MTOC sorting phenotype presented in Fig. 1-2 relates to the massive MTOC collapse shown in Fig. 3. The natural MTOC sorting and MTOC-kinetochore associations seem to be happening within the bipolar structure confined by the polar MTOCs. The MTOC rearrangements (e.g., Supplementary Video 6) are much more drastic, reminiscent of a spindle collapse. To make a mechanistic link between the phenotypes, it would be useful to use an intermediate NCD80 mutant (ex. NDC80-4D; Zaytsev et al., 2014 JCB) that may support chromosome alignment and maintenance of the canonical bipolar spindle structure, but still show effects on MTOC sorting.

Thank you for your nice suggestion. We will test Ndc80-4D. The construct is ready.

3) Fig. 4 - The authors should provide evidence that unstable kinetochore-microtubule attachments, rather than chromosome-derived signals of misaligned chromosomes (e.g., from Ran or Aurora B), limit spindle elongation. For example, the authors could measure spindle elongation in oocytes with misaligned chromosomes but stable attachments: for example, NDC80-9A oocytes released from an Eg5 inhibition block should carry a number of polar chromosomes with stable attachments. The expectation would be that such spindles form with confined MTOCs and do not elongate as much as NDC80-9D expressing oocytes.

Thank you for this important suggestion. Following your suggestion, we have conducted a pilot experiment using monastrol washout. However, unfortunately, we did not observe increased chromosome misalignment in Ndc80-9A. We will play around experimental conditions.

Moreover, we propose to perform an additional experiment. We will use cohesin depletion with Rec8 TRIM-Away, which will produce chromosome misalignment and reduce kinetochore-microtubule attachment stability. We expect that these oocytes exhibit excessive spindle elongation. Then, we ask if Ndc80-9A, which would force to stabilize kinetochore-microtubule attachment (but fail to align chromosomes due to loss of chromosome cohesion), can suppress excessive spindle elongation.

These experiments will allow us to address direct contribution of kinetochore-microtubule attachment to proper spindle elongation. However, in our opinion, regardless of the results, we cannot exclude the possibility that chromosome alignment contributes to proper spindle elongation, which is indeed an intriguing hypothesis. We will discuss these possibilities in Discussion.

4) Figure 5D - The authors' model suggests that MTOCs are confined due to their connection to stably attached k-fibers. It would be useful to speculate on the molecular mechanism behind the confinement. Does a maximal k-fiber length restrict the elongation, or is there a pulling force exerted by the kinetochores?

Thank you for your thoughtful suggestion. As the reviewer suggests, we speculate that the length of k-fibers is critical for restricting MTOC position and spindle elongation. K-fibers may prevent excessive spindle elongation by anchoring MTOCs at their minus ends. Alternatively, k-fibers may act as a platform that inactivates spindle bipolarizers. We will discuss these possibilities in our revised manuscript.

5) Discussion - Lines 203-204 - "The findings of this study, together with recent studies, suggest a model for how kinetochore-microtubule attachments contribute to acentrosomal spindle assembly (Figure 5D)". - Throughout the paper the authors underscore that biopolar spindles do assembly with the NDC80-9D mutant. The authors should clarify whether spindle assembly is affected by the NDC80-9D mutant or not?

Thank you for your comment. We agree with the reviewer that we should clearly state our conclusion based on the phenotype of the Ndc80-9D mutant. Our conclusion is that stable kinetochore-microtubule attachment fine-tunes bipolar spindle assembly. If oocytes lack stable attachments, they can form a bipolar-shaped spindle composed of microtubule arrays that are largely bipolar, but the spindle becomes too much elongated and lacks MTOCs at its poles. We will explicitly state these ideas in our revised manuscript.

**Minor Points:**

1) Introduction - Lines 38-44 - The authors should cite the role of the Augmin complex in acentrosomal spindle assembly (Watanabe et al., 2016 Cell Reports).

Thank you for your excellent suggestion. We will cite this relevant paper.

2) Results - Lines 55-56 - "However, the precise manipulation of the stability of kinetochore-microtubule attachments has not been tested" - Gui et Homer 2013 studied the outcome of NDC80 depletion and tested the NDC80-9A mutant in the context of oocyte spindle assembly. Although, as the authors point out in the Discussion section, there might be differences in the experimental design that lead to different conclusions, it is not entirely accurate that precise manipulations of attachments stability have not been tested. A different wording (e.g., "has not been comprehensively tested") may be better.

Thank you for your suggestion. We agree that “has not been comprehensively tested” fits better.

3) Results - Lines 162-164 - "Ndc80-9D-expressing oocytes had no significant delay in the onset of spindle elongation, but had significantly faster kinetics of elongation compared to Ndc80-WT- and Ndc80-9D-expressing oocytes" - The authors probably meant "... Ndc80-9A expressing oocytes."

Thank you for pointing out this mistake. We will correct it.

4) Discussion - Lines 239-242 - "... microtubule nucleation in later stages may not be determined by MTOCs but are largely attributed to nucleation within the spindle, as observed by microtubule plus-end tracking in bipolar-shaped spindles (Supplementary Figure 4)." - Strictly speaking, EB3 comets indicate microtubule polymerization rather than nucleation. Microtubule nucleation within the spindle is, however, supported by studies of the Augmin complex (e.g., Watanabe et al., 2016 Cell Rep).

Thank you for your comment. We will correct our wording for EB3 comets and discuss that microtubule nucleation within the spindle is shown in Watanabe et al., 2016 Cell Rep.

5) Discussion - Lines 257-260 - "The lagging MTOCs can be positioned close to kinetochores on bi-oriented chromosomes, underscoring the importance of active error corrections of kinetochore-microtubule attachments during metaphase (Lane and Jones, 2014; Yoshida et al., 2015)." - The reasoning here is not clear. Does the number/persistence of lagging MTOCs correlate with chromosome mis-alignment or with the efficiency/timing of chromosome alignment in WT cells?

We apologize that our discussion was not clear. Previous studies (Lane and Jones, 2014; Yoshida et al., 2015) show that kinetochore-microtubule attachment errors are found on aligned chromosomes during metaphase and must be corrected until anaphase onset in oocytes. We speculate that lagging (or central) MTOCs may be a source of such kinetochore-microtubule attachment errors, although we cannot directly test this hypothesis due to lack of tools to specifically manipulate MTOC positions. We will discuss these points in Discussion.

To check if central MTOCs are correlated with chromosome misalignment, we will perform the tracking of chromosomes that were closely positioned to lagging MTOCs.

6) Discussion - Line 266 - "Yoshida et al., 2020" - This article is cited elsewhere in the text as "Yoshida et al., in press".

Thank you for pointing out these mistakes. We will correct them.

Reviewer #3 (Significance (Required)):

Courtois et al., have found a new mechanism contributing to acentrosomal spindle assembly in mouse oocytes. Although kinetochore-dependent spindle assembly occurs in mitotic cells (e.g., Toso et al., 2009 JCB), only the recent work from the Kitajima lab (Yoshida et al., 2020 Nat Comm; this manuscript) showed that kinetochores also impact acentrosomal spindle assembly in meiosis. The genetic model presented here brings a significant technical advance in dissecting relative contributions of spindle assembly pathways in mouse oocytes (ex. Schuh and Ellenberg 2007 Cell; Watanabe et al., 2016 Cell Rep; Drutovic et al., 2020 EMBO J) and complements current methods used to study meiotic error-correction (e.g., Chmatal et al., 2015 Curr Biol, Yoshida et al., 2015 Dev Cell; Vallot et al., 2018 Curr Biol and many others). This model expands an existing toolbox of techniques allowing complete elimination of the endogenous protein specifically in mature mouse oocytes (Clift et al., 2017 Cell; Clift et al., 2018 Nat Protocols), which is a difficult feat due to a limited capacity of ex-vivo culture (Pfender et al., 2015 Nature). Therefore, the work presented in this manuscript may encourage other researchers to establish similar systems for oocyte-specific manipulations, which will allow more precise insight into oocyte biology.

Expertise keywords: spindle dynamics, chromosome segregation, mitosis, meiosis

We appreciate your comments. Additional experiments following on your constructive comments will further improve our manuscript.

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Referee #3

Evidence, reproducibility and clarity

In order to assemble a bipolar structure, acentrosomal spindles relay on multiple non-centrosomal pathways. Mouse oocytes specifically build bipolar spindles by sorting and clustering of microtubule organizing centers (MTOCs). While microtubule cross-linkers, spindle motors and microtubule nucleators are involved; the role of kinetochores and kinetochore-microtubule attachments in meiotic spindle assembly and maintenance has not been thoroughly tested. Using an impressive combination of live cell imaging and semi-automated image analysis, Courtois et al. quantified MTOC behavior in bipolar mouse oocyte spindles and found an ongoing MTOC sorting in metaphase and instances of MTOC-kinetochore associations. The authors further employed an elegant genetic system to replace NDC80 in maturing oocytes with a mutant almost completely unable to form stable microtubule-kinetochore attachments. The data show lack of MTOC confinement at the spindle poles and increased spindle elongation while maintaining spindle bipolarity. The authors concluded that stable kinetochore-microtubule attachments are required to confine MTOCs at the poles, which in turn sets an optimal spindle length. Overall, the data are of very high quality and clearly presented, the manuscript is easy to follow, and the methods are comprehensively described. One concern is the lack of mechanistic link between the natural metaphase MTOC sorting (Fig. 1-2) and massive MTOC rearrangements observed with the NDC80-9D mutant (Fig. 3). A second concern is that deficient MTOC confinements and spindle elongation observed with the 9D mutant could be due unaligned chromosomes rather than lack of stable kinetochore-microtubule attachments, which is the authors' interpretation.

Major Points:

1) Massive MTOC rearrangements (Supplementary Video 6) are reminiscent of spindle assembly defects or spindle collapse. Since these spindles do not reach a normal metaphase and seem to change shape (Supplementary Video 6; 11:10), it is difficult to differentiate between spindle assembly and spindle maintenance defects. Is there a difference in the timing of bipolar spindle assembly for NDC80-9D vs WT? If so, one interpretation is that stable attachments not only ensure MTOC confinement but also contribute to bipolar spindle assembly.

2) Fig. 1-2 vs Fig. 3 - It is not clear how the discrete MTOC sorting phenotype presented in Fig. 1-2 relates to the massive MTOC collapse shown in Fig. 3. The natural MTOC sorting and MTOC-kinetochore associations seem to be happening within the bipolar structure confined by the polar MTOCs. The MTOC rearrangements (e.g., Supplementary Video 6) are much more drastic, reminiscent of a spindle collapse. To make a mechanistic link between the phenotypes, it would be useful to use an intermediate NCD80 mutant (ex. NDC80-4D; Zaytsev et al., 2014 JCB) that may support chromosome alignment and maintenance of the canonical bipolar spindle structure, but still show effects on MTOC sorting.

3) Fig. 4 - The authors should provide evidence that unstable kinetochore-microtubule attachments, rather than chromosome-derived signals of misaligned chromosomes (e.g., from Ran or Aurora B), limit spindle elongation. For example, the authors could measure spindle elongation in oocytes with misaligned chromosomes but stable attachments: for example, NDC80-9A oocytes released from an Eg5 inhibition block should carry a number of polar chromosomes with stable attachments. The expectation would be that such spindles form with confined MTOCs and do not elongate as much as NDC80-9D expressing oocytes.

4) Figure 5D - The authors' model suggests that MTOCs are confined due to their connection to stably attached k-fibers. It would be useful to speculate on the molecular mechanism behind the confinement. Does a maximal k-fiber length restrict the elongation, or is there a pulling force exerted by the kinetochores?

5) Discussion - Lines 203-204 - "The findings of this study, together with recent studies, suggest a model for how kinetochore-microtubule attachments contribute to acentrosomal spindle assembly (Figure 5D)". - Throughout the paper the authors underscore that biopolar spindles do assembly with the NDC80-9D mutant. The authors should clarify whether spindle assembly is affected by the NDC80-9D mutant or not?

Minor Points:

1) Introduction - Lines 38-44 - The authors should cite the role of the Augmin complex in acentrosomal spindle assembly (Watanabe et al., 2016 Cell Reports).

2) Results - Lines 55-56 - "However, the precise manipulation of the stability of kinetochore-microtubule attachments has not been tested" - Gui et Homer 2013 studied the outcome of NDC80 depletion and tested the NDC80-9A mutant in the context of oocyte spindle assembly. Although, as the authors point out in the Discussion section, there might be differences in the experimental design that lead to different conclusions, it is not entirely accurate that precise manipulations of attachments stability have not been tested. A different wording (e.g., "has not been comprehensively tested") may be better.

3) Results - Lines 162-164 - "Ndc80-9D-expressing oocytes had no significant delay in the onset of spindle elongation, but had significantly faster kinetics of elongation compared to Ndc80-WT- and Ndc80-9D-expressing oocytes" - The authors probably meant "... Ndc80-9A expressing oocytes."

4) Discussion - Lines 239-242 - "... microtubule nucleation in later stages may not be determined by MTOCs but are largely attributed to nucleation within the spindle, as observed by microtubule plus-end tracking in bipolar-shaped spindles (Supplementary Figure 4)." - Strictly speaking, EB3 comets indicate microtubule polymerization rather than nucleation. Microtubule nucleation within the spindle is, however, supported by studies of the Augmin complex (e.g., Watanabe et al., 2016 Cell Rep).

5) Discussion - Lines 257-260 - "The lagging MTOCs can be positioned close to kinetochores on bi-oriented chromosomes, underscoring the importance of active error corrections of kinetochore-microtubule attachments during metaphase (Lane and Jones, 2014; Yoshida et al., 2015)." - The reasoning here is not clear. Does the number/persistence of lagging MTOCs correlate with chromosome mis-alignment or with the efficiency/timing of chromosome alignment in WT cells?

6) Discussion - Line 266 - "Yoshida et al., 2020" - This article is cited elsewhere in the text as "Yoshida et al., in press".

Significance

Courtois et al., have found a new mechanism contributing to acentrosomal spindle assembly in mouse oocytes. Although kinetochore-dependent spindle assembly occurs in mitotic cells (e.g., Toso et al., 2009 JCB), only the recent work from the Kitajima lab (Yoshida et al., 2020 Nat Comm; this manuscript) showed that kinetochores also impact acentrosomal spindle assembly in meiosis. The genetic model presented here brings a significant technical advance in dissecting relative contributions of spindle assembly pathways in mouse oocytes (ex. Schuh and Ellenberg 2007 Cell; Watanabe et al., 2016 Cell Rep; Drutovic et al., 2020 EMBO J) and complements current methods used to study meiotic error-correction (e.g., Chmatal et al., 2015 Curr Biol, Yoshida et al., 2015 Dev Cell; Vallot et al., 2018 Curr Biol and many others). This model expands an existing toolbox of techniques allowing complete elimination of the endogenous protein specifically in mature mouse oocytes (Clift et al., 2017 Cell; Clift et al., 2018 Nat Protocols), which is a difficult feat due to a limited capacity of ex-vivo culture (Pfender et al., 2015 Nature). Therefore, the work presented in this manuscript may encourage other researchers to establish similar systems for oocyte-specific manipulations, which will allow more precise insight into oocyte biology.

Expertise keywords: spindle dynamics, chromosome segregation, mitosis, meiosis

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Referee #2

Evidence, reproducibility and clarity

I am commenting on the work of Courtois et al. as an expert in the biochemistry of spindle formation with a focus on acentriolar assembly.

First and foremost, this a technically excellent study with a number of very interesting and well-documented observations, which are highly relevant for our understanding of the mechanisms of acentriolar spindle formation in the mouse oocyte model. In principle, the manuscript is in a very mature state. However, my major concern at this point would be that there is a break in the story. It starts describing the (very interesting) observation of "central MTOCs". After thoroughly investigating how these behave, the authors stop and look at overall MTOCs distribution after loss of stable MT-kinetochore interactions based on oocytes expressing the Ndc80_9D mutant instead of wt Ndc80. The two parts are experimentally and conceptually not well connected.

Answering the following questions may help to further develop the paper:

1. If I understand the arguments correctly, central MTOCs are an "accident" on the way to complete meiosis I spindle formation, which will eventually be corrected and all MTOCs clustered at the poles. Thus, they may serve as an assay for spindle assembly fidelity and kinetics (?). At this point, the reader is left with the observation without efforts to explain the meaning of this observation, ideally experimentally, or at least in a valid discussion.
2. Enthusiasm for the technically excellent experiments using the Ndc80 variants are somewhat reduced as conclusions from these experiments are published in the parallel paper of the same laboratory (Yoshida et al.). Due to my opinion, it may thus be even more important to connect these observations with the first part described central MTOCs and to clarify their significance.
3. Shown if in Fig. 3B but not fully explained: How does the distribution of what is defined as central MTOCs behave in Ndc80_wt and Ndc80_9A mutant oocytes? Do the variants differ, i.e. are there fewer, or less persistent central MTOCs in the 9A mutant? Would they differ in kinetics of appearance and "rescue" to the poles?
4. Similarly: is there a correlation of central MTOC appearance, Ndc80 phosphorylation/stability of kinetochore attachment and Anaphase I onset? The authors mention that oocytes expressing the 9A mutant go faster into Anaphase.
5. The observation that "central MTOCs exhibited correlated motions with closely positioned kinetochores" is poorly defined, yet an important observation. Does this mean some sort of short k-fibers remain to connect central MTOCs and kinetochores? Wouldn't one expect that the loss of stable end-on-attachment causes MTOCs to become central? How does this fit into a/the model?
6. Along the same lines: The authors hype their conclusion that kinetochores dominate meiosis I spindle formation based on the observation that loss of kinetochore functions results in less well-organized spindle poles and worse MTOC "confinement". This may mean that kinetochores, together with MTOCs, maintain stable k-fibers in meiosis, as shown here and in Yoshida et al. When one or the other end of k-fibers is destabilized (loss of end-on-attachment, loss of MTOC attachment), the fibers collapse and the remaining minus-or-plus-end associated structure loses its destination. We then see central MTOCs and/or kinetochores at poles. In this respect, the interpretation / discussion should be less "kinetochore-centered".
7. Is there any way to determine the efficiency of Ndc80 knockdown in the gene replacement respective experiment? I share the view of the authors that their method may be more efficient and may explain apparent discrepancies to previous studies on Ndc80-9A (Guy and Homer, 2013) with more dramatic effects on spindle geometry. However, at that point, this remains speculative. For instance, one may also speculate vice versa that the ko strategy used here is less efficient in a maternally dominated system and leaves behind more wt Ndc80, which better compensates defects seen in the 9A mutant.

Significance

Courtois et al present data on mechanisms governing spindle assembly in mouse oocytes. Mouse oocytes serve as model system for spindle formation in the absence of centriole-based MTOCs. At the onset of meiosis I, numerous MTOCs form, which shape a mass ("ball") of MT nucleated around chromatin into a bipolar structure. Accumulating evidence indicates that kinetochores play an important role in acentriolar spindle formation in mouse oocytes, yet the mechanisms behind kinetochore action remains unclear.

Here, Courtois et al. analyze spindle formation in live mouse oocytes using 3D-time-lapse imaging. They use fluorescently tagged Cep192 to track MTOCs and Histone H2B or CENP-C to visualize chromatin or kinetochores. In the first part, the authors deal with the appearance of "central MTOCs", i.e. aggregates of centrosomal protein(s) that, apparently, fail to remain stably integrated into the spindle pole clusters on MTOCs during spindle formation. The authors convincingly demonstrate that these central MTOCs can be seen in the majority of spindles investigated. They demonstrate that central MTOCs generally come from positions at poles from where they "fall back" towards chromosomes. Central MTOCs may even cross the spindle and end up at opposite poles from where they originated from. Interestingly, central MTOCs are often found next to kinetochores.

In the second part, the authors focus on the role of kinetochores and their stable MT attachment for spindle formation in general and bipolarity/pole organization in particular. The same lab has published data on the role of kinetochores in meiosis I spindle very recently (Yoshida et al. Nat Comm, 2020). Here, they successfully exploit Ndc80 phospho-mutants to compare MTOC distribution in oocytes with reduced or increased end-on-attachment. The data show that stable end-on attachment determines stable MTOC clustering at spindle poles and governs the maintenance of bipolarity and spindle length.

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

This group has been at the forefront recently of using imaging technologies to understand how chromosome segregation is coordinated in mammalian oocytes, and why errors occur. In the current paper they examine the dynamics of microtubule organising centres (which effectively replace centrioles/centrosomes in oocytes) in MI. The imaging of oocytes in this paper is beautiful. The major findings are (1) that MTOCs that are supposed to be at the spindle pole sometimes end up at the spindle equator, and this is documented very beautifully and (2) the correct positioning of MTOCs at the spindle pole appears to require kinetochore microtubules, as indicated by experiments manipulating the kinetochore component NDC80.

Major Comments

As such the major claims of the paper are basically well supported. However, the analyses are is almost entirely restricted to prometaphase/metaphase, and the conclusions are relatively limited. The salient omission is any analysis of MTOC/chromosome relationship during anaphase. Were the paper to be extended to determine whether the lingering of MTOCs at the spindle equator is related to chromosome segregation error, that would increase the reach and importance of the work substantially. Specifically:

1. Can tracking experiments be performed to determine whether the chromosome that shows movement similarities to the errant MTOC is more/less likely to missegregate? Complete tracking as these authors are expert at should achieve this, or photo-labelling the desired chromosome.
2. Can the position of MTOCs (proportion that linger at the equator) be manipulated in the absence of other defects to determine whether this increases errors (lagging at anaphase, metaphase-II chromosome counting spreads)?
3. The above analysis would have to be well supported by controls showing that these constructs are having no impact on normal anaphase (proportion of oocytes completing meiosis-I, likelihood of lagging chromosomes etc).
4. Related to the above, though I appreciate a fixed metaphase image of MTOC immunofluorescence is presented, the paper is about the dynamics of MTOCs and thus nonetheless relies heavily on the live imaging of cep192. The core results should be confirmed using another (substantially different) MTOC probe. This final comment applies to the current metaphase data, regardless of whether the study is ultimately extended

Significance

As explained above, as presented this paper is largely scientifically sound, but far more limited in scope than this groups other recent papers. As explained above, the paper would be made more impactful and the readership broadened if a relationship between MTOC position/movement and segregation problems were established. Or on the other hand if it were established why some MTOCs sometimes linger at the spindle equator. Whilst to my knowledge this is the first time that equator MTOCs have been documented so carefully, oocyte cell biologists may not find the core observation that MTOCs are occasionally at the spindle equator extremely surprising.

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Reply to the reviewers

We would like to thank Reviewer #1 and #2 for the evaluation of our research and comments to our manuscript. Their comments are highly appreciated and addressed as described below.

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

**Summary:**

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

Here Ha et al. has further developed their Pumilio RNA tagging methodology for the isolation of UV-crosslinked proteins that are suggested to associate with Xist RNA in mouse embryonic stem cells (mESCs). Within this study the authors claim to have found the Lupus antigen RNA binding protein (La) as a novel Xist interacting partner that influences the efficacy of X-chromosome inactivation (XCI). The authors use a number of different techniques such as qPCR, fluorescent imaging, ATAC-SEQ and SHAPE to show aberration of XCI upon La shRNA knockdown. However, this study has significant flaws in the efficient isolation and validation of Xist associated proteins using their FLAG-out methodology. Furthermore, later experiments predominantly focus on cell death/survival assays, which is somewhat troubling given the essential roles La plays in processes such as cell differentiation and proliferation, ribosome biogenesis, transcriptional control and tRNA maturation. I feel the authors need to robustly address the potential effects La knockdown may be having on their mESCs.

Reviewer #1 did not fully understand the basic designs of the experimental systems (FLAG-out and iXist), and completely rejected these experimental systems. Reviewer #1 also ignored the majority of the functional analysis on the candidate protein, Ssb. These issues cannot be addressed by additional experiments

**Major comments:**

*-Are the key conclusions convincing?*

My major concern is in their Xist RNA purification.

First of all, I couldn't find any data on proving the enrichment of Xist RNA itself in their Pumilio pull-down experiment. It would have been useful to show Xist RNA enrichment before benzonase step. Secondly, it is hard to imagine the protocol would successfully isolated Xist RNA-protein complexes from the cell. An earlier report by Clemson et al., (J Cell Biol., 1996) has shown that majority of Xist RNA is still stuck in the nucleus after nuclear matrix prep protocol using detergent, which is not so different from the authors' protocol. Moreover, the authors used UV crosslink, which would have made even harder to purify Xist RNA without sonication. Thirdly, as the tag is located on 5' of Xist RNA, it is rather surprising to see that Spen is not detected in their pulldown. Spen is one of the main functional interactors with Xist, robustly detected by several previous reports. Similarly, other high-affinity binders of Xist such as hnRNP-K and Ciz1 were also lacking from this screen. Finally, the peptides found associated with FLAG-out Xist are extremely low in comparison with other data using glutaraldehyde or formaldehyde crosslinking. For example, HnRNP-M found in Chu et al 2015 has 1120 peptide counts in differentiated cells. The authors here use HnRNP-M as a baseline for specific interactions and show a total of 6 peptide counts in Xist expressing cells and 5 in i-Empty cells (Supplementary excel sheet 1). Similarly, the La protein of interest in this study has 8 counts in i-FLAG-Xist and 6 counts in i-Empty. I struggle to see how this result indicate specific Xist binding. Worryingly this is the starting rationale for the rest of their experiments, it is hard to therefore accept the rest of their conclusions either.

We have detected Xist RNA after Pumilio pull-down, and added the data in the revised manuscript (Figure S1). The enrichment of Xist RNA by Pumilio pull-down is about 75-fold, comparable to the enrichment reported by Minajigi et al.

Two out of three previous studies used similar protocols to prep cell lysates for co-IP, including UV cross-linking and detergent (McHugh et al. 2015 and Minajigi et al. 2015). The major difference between their protocols and ours is the co-IP step. They used antisense oligos to pull-down Xist RNA-protein complex, while we take advantage of the specific interaction between PUF and PBS to pull-down Xist RNA-protein complex. With the data in Figure S1, we are confident that our strategy is successful in isolating Xist RNA

For systematic identification of Xist binding proteins, each method has its own strength and weakness. As we described in the introduction, only 4 proteins were commonly identified by all three studies to systematically identify Xist binding proteins. There is no doubt that our method also missed some authentic Xist binding proteins (false negative) and identified some false positive candidates. Thus, we have to be careful in balancing between the false negative and false positive calls. The reason that we applied the ranking gain to identify Xist binding protein candidates, is to minimize the false negative rate. Meanwhile, we compared our Xist binding protein candidate list with previous identified Xist-binding proteins to enhance the confidence in our candidate lists.

Regardless the strength and weakness of our method, Ssb is also an Xist-binding protein identified by another study (Chu et al. 2015). More importantly, we have provided experimental validation to confirm Ssb’s involvement in XCI and extensive functional analysis to reveal the protein’s mechanistic role in XCI.

The other key conclusion the authors make is from the use of numerous cell death/survival assays for both male and female cell lines. This is extremely troubling in the context of assessing their target protein La. La is involved in multiple RNA maturation events of rRNAs, tRNAs and other polIII transcripts. Furthermore, La has been implicated in binding to the mRNA for Cyclin D1 in both human cells and mouse fibroblasts (NIH/3T3 - male) which show a significant effect on cell proliferation upon siRNA knockdown https://www.nature.com/articles/onc2010425. This, along with the observation that La knock-out blastocysts fail to develop any mice or ES cell lines (male or female) show the effect observed in the authors results is most likely not X-linked cell death https://mcb.asm.org/content/mcb/26/4/1445.full.pdf. The authors need to show that their shRNA KD isn't affecting the proliferation and general fitness of their mESC lines.

The cell death/survival assay was specially designed for analyzing the defect of XCI. The cell death of iXist ESCs upon adding Dox is due to the induction of Xist, which consequently initiates the silencing of the only X chromosome in male cells. Knockdown of genes involved in XCI compromises XCI, thus allowing cell survival. Given the diverse functions of Ssb in cell differentiation and proliferation, ribosome biogenesis, transcriptional control and tRNA maturation, one would expect slow growth and/or cell death of Ssb knockdown cells. Indeed, the result is consistent with our expectation (Figure 2C, without Dox). Nevertheless, more Ssb knockdown cells survive in the presence of Dox, compared with control cells (Figure 2C-E, with Dox), suggesting that Ssb plays an important role in XCI.

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

As discussed above, I feel the authors have not clearly demonstrated Xist specific protein enrichment and haven't proven X-linked cell death. Due to the lack of necessary control experiments as discussed below, I feel the notion that La is involved directly in XCI as an RNA chaperone is currently preliminary/speculative.

The FLAG-out experiment just provided an initial point for the study. We have demonstrated the interaction between Xist and Ssb by RIP. And, Ssb knockdown antagonizes the lethal effect of induced XCI in male cells, allowing more cell to survive. This is contradictory to the diverse house-keeping functions of Ssb, which should lead to slow proliferation or cell death. Therefore, the data here (Figure 2C-E) should suggest a role of Ssb in XCI. In addition, we showed that knockdown of Ssb compromises the silencing of X-linked genes (Figure 2F, 2G, and 3E), the compaction of X chromosome (Figure 3D), Xist cloud formation (Figure 4), epigenetic modifications on Xi (Figure 5), Xist RNA folding (Figure 6F-I), and Xist RNA stability (Figure 7C and D). All these data indicate that Ssb is involved in XCI by regulating Xist RNA folding.

*- 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.*

I would suggest them to show RT-qPCR results of Xist RNA enrichment from the sample after flagIP before benzonase treatment.

We have the data, and added it to Figure S1.

Also, it would have been more convincing if their negative control construct (i-Empty) would contain 25 copies of PBSb RNA at least.

This is a good alternative design of the negative control. Using i-Empty expressing 25 copies of PBSb RNA will allow us subtract the background causing by proteins binding to PBSb RNA. Yet, as discussed above, regardless how we improve the experimental setting, we cannot completely avoid the issue of false positive and false negative. Our goal of the FLAG-out experiment is to generate a list of Xist binding protein candidates, and their binding to Xist and their functions in XCI should be validated by additional experiments. With our current experimental setting, a list of Xist binding protein candidates has been generated, and we have validated the role of Ssb in XCI with subsequent experiments.

In Fig1b, the total amount of proteins loaded on the gel is not equivalent between two lanes. The gel should show equivalent amounts of proteins on the gel. It looks like if the negative control sample had been loaded at the same amount as the one with Xist, the band pattern wouldn't be distinguishable between the two samples. Furthermore, as these samples were used in the following mass spectrometry screen it may suggest that the minimal increase in peptide counts observed in the iXist FLAG-out were due to an increased amount of sample being loaded? No controls are conducted to account for this.

IP samples of i-Empty and i-FLAG-Xist were loaded in the gel in Figure 1b. It is expected that IP sample of i-FLAG-Xist should pull down more proteins than IP samples of i-Empty. The FLAG-PUFb bands (the strongest band in each lane) are about the same amount in two samples, indicating roughly equal amount of loading. After normalization of gel loading according to the FLAG-PUFb bands, the upper part of the i-FLAG-Xist lane showed some unique bands.

For mass spectrometry analysis, the loading of two samples are independent, therefore, to compare the absolute amount of each protein between the two samples does not always provide valuable information. Yet, the relative amount of different proteins within one sample is not affected by the loading amount, thus, more informative. Therefore, we used the ranking information to estimate the relative amount of different proteins in each sample and used the ranking gain to further identify protein candidates.

The authors quantify cell death in figures 2C - E. It seems clear that shSsb 1 and 2 have an effect on cell count even in the absence of Dox. The rescue effect seen upon Dox addition is minimal when compared to Empty + Dox 2D. The authors ∆A-iXist line with and without Ssb KD/Dox would be an informative control on whether the increase in cell survival that they see is X-linked.

As the reviewer pointed out earlier, Ssb plays multiple roles in cellular processes. Inevitably, KD of Ssb leads to slow growth and/or cell death with or without Dox. Thus, it is less meaningful to compare the surviving cell counts in Figure 2D. Rather, the survival rate (Figure 2E) reflects the rescuing effect more precisely. Shown in Figure 2E, both shSsb 1 and 2 increase the survival rate significantly, compared with Empty control.

Moreover, the data in Figure 3B and C demonstrated that Ssb KD compromises the survival of female differentiating cells, but not the survival of male differentiating cells, also indicating a role of Ssb in XCI. With these experiments, it should be sufficient to conclude that Ssb KD affects X-linked cell death/survival in both iXist male ESCs and WT female differentiating cells

The qPCR results used to validate silencing defects show minor changes in expression and also don't show significant silencing of X-linked genes sufficient for cell death. Could this be because only ~ 50 - 60% of Male iXist cells seem to be expressing in the movies and that this will have an effect on the observed qPCR results? Furthermore, it seems counterintuitive that expression in the Empty male cells increases in 48h compared to 14h. Is this due to cell death and positive selection of cells less able to silence their X-chromosome? How would these data look in the female XX line? How would the data look in a ∆A-iXist line in the presence and absence of shSsb/Dox?

First, high-quality live-cell imaging can only be carried out for 2 hours with 2-min time interval. The movies are meant to show the onset of Xist RNA signals. Therefore, they were taken one hour after Dox treatment (figure legend of Figure 4B-D). After overnight Dox treatment, Xist clouds can be seen in majority of cells.

Second, in Fig. 2F-G, we did not include uninduced iXist male ESCs. Therefore, it is impossible to judge whether induction of Xist in this male ESC line results in Xist-dependent silencing at 14 and 48 hr. However, in our previous publication (Li et al., JMB, 2018, 430: 2734-2746), it has been shown that Gpc4, Hprt, Mecp2, G418, and TomatoRed are silenced (4- to 16-fold reduction) at 24 and 48 hours after Dox induction.

Third, the qRT-PCR results in 14 h and in 48 h are not normalized to the same internal control. Thus, they are not directly comparable.

Confusingly, the male line in Fig 3C shows a drop in live cell count at day 6 of differentiation? Surely given their previous results in Fig 2 the Ssb KD should increase cell viability with +Dox? Ssb KD seems to have an adverse effect on ES cells during extended differentiation protocols. In Figure S1 the authors show ~ 8 - 10% survival of male lines during differentiation. Could the recombination of the Xist sequence around the loxP sites enable the cells to outcompete the dead cells? How would iEmpty and ∆A-iXist cells compare here? Have the differentiated cells been tested for their expression of Xist? Additionally, how are there similar live cell counts for male vs female lines when ~90% of male cells die during differentiation? Were more cells plated at day 4? If so, this would bias the competition of male cell survival and therefore make the male line an inappropriate control.

Given the essential role of La during development a control is needed to prove that this death is X-linked in the female 3F1 line. For example, an XO cell line retaining the Cast allele and shSsb expression could show the amount of death caused from shSsb alone independent of X-linked cell death.

The reviewer completely misunderstood the experiment. The severe cell death specifically observed in female differentiating ESCs is a strong evidence showing Ssb is involved in XCI (Figure 3).

The male ESCs in Figure 3C is a WT ESC line without the inducible Xist transgene, in which no XCI occurs upon differentiation. It is completely different from iXist male ESCs with Dox, in which forced Xist induction leads to XCI. Thus, the diverse functions of Ssb might contribute to the slight decrease in live cell count of wild type male cells at day 6 of differentiation.

Figure S2 shows the differentiation of iXist male ESCs with or without Dox. As explained above, forced Xist induction silences the only X chromosome in male cells, resulting in cell death. In addition, XCI occurs more efficiently in differentiation condition (Figure S2) than in pluripotent status (Figure 2C)

During differentiation, female ESCs silence one X chromosome, and the other X chromosome remains active. KD of Ssb compromises XCI, and two X chromosomes in some female differentiating cells maintain active, leading to cell death. The reviewer is correct that we need a control to rule out that the essential role of Ssb during development affects cell survival and death. An XO cell line can be used as a control. Similarly, a male cell line (XY) is also a good control. We already included a male cell line as a control in Figure 3B and 3C.

If I understood correctly, the RNA FISH used dsDNA probes ("Sx9") against 40 kb of the X-inactivation centre (Xic). Surely Tsix or other Xic transcripts will also be visible? Can the authors use their RNA FISH to determine the XX or XO status of their cells? In Figure S5 a number of cells appear to show a single pinpoint of transcription. This could either be low levels of Xist transcripts or Xic transcription from an XO line in which the 129 chromosome is missing. It would be best to solely quantify cells which have two x chromosomes and if a significant amount of X chromosomes have been kicked out, this should be discussed and controlled for.

This is a valid concern, but this concern can be adequately addressed with the available data in the manuscript.

First, if the female Ssb KD cell line is an “XO” cell line, in which the X129 allele is “kicked out”, the RNA allelotyping results should show an absolute “silencing” of the X129 allele. However, in complete contrast to this notion, RNA allelotyping detected “more” RNA transcripts from X129, showing the chromosome-wide XCI defects (Figure 3D).

Second, overexpression of Ssb in Ssb KD female cells restores the Xist clouds and the polycomb marks (Figure S8), suggesting that the Ssb KD female cells are XX, but not XO.

Third, the severe cell death specifically occurred in female Ssb KD lines is also against the “XO” argument (Figure 3B&C).

In Fig6, the authors generated a number of Ssb constructs for a rescue assay. However, these results complicate the matter and raise more questions than they address. It seems odd that the ∆RRM1 does not rescue based on comparison with their putative negative control, ∆NLS. However, the ∆RRM1 + 2 and ∆LAM do rescue the phenotype better than the full length Ssb? This makes no logical sense and highlights the inherent variation in cell viability these generated cell lines seem to show.

Following on from this, figure S7 quantifies the GFP tag mRNA levels, depicting all ∆RRM mutants with expression below ~30%? How can ∆RRM1 or 2 be rescuing in this scenario? Have these lines been tested for their XX or XO status? The loss of an X chromosome would lead to a rescue of the cell death phenotype, which is a process known to occur in XX lines that have been cultured for extended periods of time. Could it also be that the cell lines derived are more or less sensitive to exogenous shRNA expression? Also, further validation is needed to assess the efficiency of KD in these lines as theoretically most of these constructs will be targeted by shRNA? What is the endogenous Ssb expression level in these lines? Where in the mRNA sequence are the shRNAs targeted to? Does this make sense on the relative expression levels of ∆RRM1/2 for example? Further testing of GFP expression could also be assessed by quantitative western blot of GFP or even visualised in their RNA FISH/IF samples (Figure S8), currently neither are shown. In addition, some kind of information of stability of each Ssb protein constructs has not been demonstrated.

Our shRNA targets the LAM domain, so the expression of ∆LAM is not affected by the shRNA. The reviewer is correct that the detected GFP expression levels of ∆RRM1 and ∆RRM2 are too low to be conclusive. We have removed the data point of ∆RRM1 and ∆RRM2. Meanwhile, it is clear that ∆RRM1&2 has a better rescuing effect than ∆NLS, when ∆RRM1&2 and ∆NLS are expressed at similar levels. Ssb is a well known RNA chaperone/RNA helicase. Identifying Ssb is an Xist-binding protein already suggests the functional role of Ssb in XCI. The data of the plasmid rescue experiments further suggests that Ssb is involved in XCI as a RNA chaperone/RNA helicase.

As for the Western blot and GFP fluorescence (IF), we have tried both. Neither of them detected GFP signal, reflecting the low expression level of these GFP fusion proteins. As the reviewers pointed out that the shSsb is not targeting the 5’ or 3’-UTR region, therefore, interfering the exogenous Ssb as well. This might be a reason for the low expression of these GFP fusion proteins.

For the data shown in Figure 7A and B the authors quantify the % of cells with Xist signal. The authors have already shown a defect in Xist visualisation in Ssb KD. Surely it is plausible to assume a faster loss of Xist signal below background in weaker expressing cells. A more appropriate quantification would be the % loss of Xist signal per cell over time.

With Figure 7C and D, the samples have been treated with actinomycin D which globally affects the transcription of cells even the PolIII associated genes Ssb is needed to mature. This treatment could have an added effect on cell mortality and function. Data confirming that actinomycin D doesn't affect the cells disproportionately is needed. The difference in half-life could be attributed to such a treatment.

We agree with the reviewer that monitoring Xist signal loss per cell would be a better way to analyze the data. However, in Xist signal loss experiment, snapshot images were taken at four time points (1h, 2h, 3h and 4h). This is not a time-lapse imaging. High-quality time-lapse imaging can only be done within a 2-hour time period with 2-min time interval. Therefore, cell-tracking cannot be done in this experiment. In addition, even though Ssb KD slows down the formation of Xist cloud within the early phase (3 hours) of Xist induction (Figure 4), prolonged (overnight) Xist induction leads to Xist cloud formation in a significant fraction of Ssb KD cells, and the Xist cloud signals are about the same in WT and Ssb KD cells (Figure 7A, 0 h). Similarly, qRT-PCR also revealed that Xist RNA are at the same level in WT and Ssb KD cells (Figure 7C, 0 h). These data argue against that a faster loss of Xist signal in Ssb KD cells is due to weaker initial Xist signal.

Actinomycin D was added at the last 11 hours of the experiment. During this period, no obvious adverse effects on cells were observed.

In summarising the authors claim that La binds Xist to facilitate folding and appropriate spreading of Xist along the X-chromosome. No direct interaction has been shown, CLIP-seq data would resolve this, however I do understand this is a challenging technique. The authors have instead opted for RIP followed by qPCR (Figure S2). However, this process has a greater potential for non-specific recovery of RNAs via indirect binding. Furthermore, qPCR may also amplify the relative abundance of the RNA detected. As multiple nucleolar proteins came down in the mass spec screen and FLAG-Ssb is being over expressed, it is plausible to assume some transient Xist interactions may arise from nucleolar association at which La will be in high abundance. Positive and negative nuclear RNA controls (e.g. 7SK and U1 snRNA respectively) could be used so to determine the amount of non-specific Protein-RNA interactions in their RIP pull downs. Cytoplasmic actin is not an appropriate control as it is cytosolic.

We have to clarify one point that the mass spec screen analyzed samples pulled down by FLAG-PUFb, but not FLAG-Ssb.

We did not intend to distinguish whether Ssb directly binds Xist or is just associated with Xist. RIP followed by qPCR is sufficient to prove the association between Ssb and Xist RNA.

We can include nuclear RNA as controls, if the reviewer regards RIP as a valid method to show protein and RNA association

Other than this the authors may want to probe (via IF) for the presence of La accumulation on the X? Many other know factors such as Ciz1, hnrnpK and PRC1/2 complexes show clear accumulation on the X. If I understand correctly, there are many La antibodies on the market and endogenous levels on the X could be assessed. These antibodies may be useful in IP's and pull downs also.

Many XCI factors play extensive roles in the cell and are not clearly enriched on Xi, including Spen (Moindrot et al. 2015). We have tried the immunostaining and did not detect Ssb’s enrichment on Xi. Ssb shows a general distribution in the nucleus without a clear enrichment on Xi (data not shown).

*-Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.*

The experiments suggested above are centrally focussed on the cell lines that are currently in the authors possession with maybe exceptions with the ∆A-iXist-shSsb line suggested. However, this should be reasonably quick to obtain given their previous work for this paper. Most experiments suggested will focus on the validation of karyotype, Xist expression, rescue construct expression, further RNA FISH classification and repeating more appropriate positive and negative controls for a number of experiments. In theory this can be obtained relatively simply and quickly from current resources. But with the sheer volume of further experiments that are required here, this may take a significant amount of time.

One vital improvement needed is the replication of mass spec data and the validation of Xist specific recovery and protein enrichment. As it stands this manuscript seems to not have any replicates of the FLAG-out methodology and mass spec data. This is troubling given the poor recovery and specificity of the protein samples obtained. Repeating these experiments would be costly in time and also financially. As it stands, I feel this is essential to conclusively validate their target of interest.

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

The data is presented relatively well, however, it would be beneficial if deailed methods were in the main text and not in a supplementary file. Similarly, more information about the process of differentiation and how cell death/survival was quantified and validated is needed.

The reviewer rejected the basic design of the experimental system and ignored the majority of the functional analysis data. No additional experiment can address these issues

We can include more information in the main text, regarding Ssb. However, there is limited space for the main text, various depending on the journals. Meanwhile, the current citation on Ssb is adequate to emphasize that Ssb is a versatile RNA binding protein involved in a variety of fundamental RNA processing events in the cell.

*- Are the experiments adequately replicated and statistical analysis adequate?*

In the most part yes, however there seems to be no replicates of the FLAG-out mass spec screen which is worrying given the minimal specificity observed in the current data.

As we mentioned above, the FLAG-out experiment only serves as a starting point to generate a list of Xist binding protein candidates. Rather than repeating the FLAG-out experiment, we compared the result of FLAG-out to previously published lists of Xist binding protein candidates. More importantly, additional experiments are carried out to validate the Xist binding proteins identified by FLAG-out.

**Minor comments:**

*- Specific experimental issues that are easily addressable.*

Unfortunately, the majority of experimental issues need to be addressed with more robust data which are highlighted above. However, some image analysis, quantification and classification can be amended relatively easily. For example, the live-cell imaging data should be quantified as loss of signal as discussed and RNA FISH should be used to classify XX positive cells and the XO cells can be discarded from analysis.

We have addressed these issue in the previous sections of this rebuttal.

*- Are prior studies referenced appropriately?*

Most papers regarding Xist pull down and biology are discussed and referenced appropriately. However, the role in which La plays during development and its aberrant affects upon KD are seemingly downplayed. I would like to see more discussion of potential defects that could be caused due to globally altering cellular RNA folding.

We have tried to cite key references about Ssb in development and RNA folding. Due to length limitation, we cannot cite all references in the topic. If necessary, we could discuss the possibility of indirect effect of Ssb KD on XCI through globally altering cellular RNA folding.

*- Are the text and figures clear and accurate?*

For the most part, lots of the figures are clear and accurate. Apart from these exceptions.

1.The Y-axis of Figure 2D is confusing. What does 0.3 as a "sum of area" equate to? 30% of the area was ES cells? This doesn't look to be the case from Fig 2C. Also, how does the intensity of the signal compare? The area may not be a good quantification due to ES cells growing in colonies.

We have revised the Y-axis labelling of Figure 2D to “sum of area cm2”. Thus, “0.3” means that the area of ESCs is 0.3 cm2. ALPP is highly expressed on ES cell surface. ALPP stain usually produce saturated stains on ES cell colonies. Thoroughly stained ES cell colonies, big and small, show similar signal intensity levels. To analyze the “total signal intensity” will be not much different from “sum of area”.

2.In the Movies S1-7 there are boxes around certain cells and marked with "Figure 5a - c". This seems to be incorrect as figure 5 is currently the IF staining of polycomb marks. I assume this is in relation to Figure 4b-d?

We have corrected the labelling mistakes.

3.Similarly, in Movies S1-7, the intensities of Xist foci seem by eye to be similar. In the paper it is claimed that the Xist clouds that do form are lower in intensity. Are the Movies depicting the same range of pixel intensities? If not, this should be amended. Similarly, figure 7 seems to show relatively equivalent RNA signal at 0 h?

All the images were collected using a fixed standard of the microscope and camera setting, and these movies depict the same range of pixel intensities. Movies S1-S3 are WT control, and Movies S4-S7 are Ssb KD cells. The Xist cloud signals are weaker in Movie S4-S7 (also quantified in Figure 4E). For the Xist cloud signal, not only the intensity, but also the area of Xist cloud, have to be taken into account.

The 0 h in Figure 7 is after overnight Dox treatment, and different from the time point in Movies S1-7 (maximum 3 hour Dox treatment, figure legend of Figure 4B-D). The discrepancy can be explained by that knockdown of Ssb only slows down the formation of Xist clouds. After overnight forced expression, the Xist RNA still shows an accumulation in the cells. Figure 7 shows the forced accumulation of Xist RNA after prolonged Dox treatment disappears faster after Dox withdraw.

4.In figure 4A the data is from female XX cells, this should be highlighted to limit confusion with the male iXist data shown below in 4B-E. It would also be helpful to have the male/female icons (as in figure 3B), for each figure that has images of cells. Currently Figure 4, 5, 7, S5 and S8 are lacking these icons.

We have revised the labelling on Figure 3, 4, 5, 7 S6 and S9 (S5 and S8 before revision).

5.No explanation of the Flag-Ssb expression is given for figure S2. Furthermore, is it really necessary to express Flag-Ssb? There are reasonably good antibodies out there for Ssb as this was how it was originally found in Systemic Lupus patients. Also, no data showing the amount of Ssb being overexpressed is shown. This may have big implication to the validity of the RIP-qPCR analysis.

We could perform qRT-PCR to quantify the overexpression level of Flag-Ssb. If required, we could use Ssb antibody to do Western blot to show the amount of Flag-Ssb protein.

*- Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Most of the data is presented reasonably well, but the robustness of the data somewhat retracts from their conclusions. I feel the certainty of their conclusion regarding Xist specific La binding and RNA chaperone activity is still presumptive and should be rewritten unless more robust data can confirm Xist interaction. I would also suggest deciding on the nomenclature for the protein of interest and use either La or Ssb, the continued use of both through the figures and text can get a little confusing to the reader.

In the current literatures, Ssb seems to be commonly used as a gene name and La is used as a protein name. We have revised the manuscript to use one name “Ssb” to describe both the gene and the protein.

Reviewer #1 (Significance (Required)):

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

It was a good trial to use PBSb-PUFb system to purify Xist RNA binding proteins, compared to previous reports had used anti-sense oligo purification using complementary sequence to Xist RNA sequences. But currently the purification still needs further validation and repeats to confirm its use. A potential complementary technique could be to isolate Xist directly by using biotinylated probes against the PBSb sequence.

The authors further claim the identification of a novel Xist RNA chaperone (La/Ssb) which they say facilitates XCI progression. This would be a novel finding in the field; however, the data is currently not robust enough to support this

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

This work has focused on the development of a milder methodology for purifying Xist RNA during XCI. Others have published similar methodologies predominantly focusing on purifying Xist RNA directly with biotinylated probes (McHugh et al. 2015; Minaji et al. 2015; and Chu et al. 2015). Although this method boasts a milder purification method, it seems to be low yielding in Xist specific proteins. Others have shown a more robust identification of bona fide Xist binding proteins which are currently missing in this manuscript. A recent preprint from the Plath lab has identified new factors involved in XCI during differentiation and their tethering/rescue experiments are far more convincing than the ones shown in this manuscript https://www.biorxiv.org/content/10.1101/2020.03.09.979369v1. The candidate protein Ha et al. have identified has multiple roles in developing cells and has shown to be important during mouse development. However, Ha et al do not robustly show that the knockdown of Ssb causes X-linked cell mortality. Alternatively, as would be presumed from Ssb's essential role in many housekeeping short non-coding RNAs, the cell death seems more ubiquitous upon shRNA KD. Therefore, the link the authors are making here are relatively weak.

Ssb KD rescues cell death caused by forced induction of Xist in male ESCs. In addition, Ssb KD leads to cell death in differentiating female ESCs, while it has a negligible effect on cell death in differentiating male ESCs. These data clearly demonstrated X-linked cell survival/mortality by Ssb KD.

Plath lab’s work is different from ours. In their manuscript, the authors report the observation of a protein condensation which is assembled by Xist but sustains in absence of Xist. TDP-43 (a.k.a. Tardbp) happens to be one protein factor involved in the protein condensation and also one candidate protein selected for further validation in our study. In our study, Tardbp KD did not rescue cell death caused by induced XCI in male cells. Thus, Tardbp is not further studied. In the manuscript, we have discussed the possibility that low efficiency of knockdown and redundancy might contribute to the failure in validation of Tardbp

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

The audience may be interested in the novel technique and the finding of a novel Xist binding protein.

*- 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.*

RNA biochemistry and developmental biology

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

**Summary:**

This manuscript describes a novel "FLAG-out" system, where the authors sought to identify Xist RNA binding proteins. The authors focused on a specific protein found in their screen and also identified in several other screens for Xist RNA binding proteins, Ssb/La, and further characterize the role of this protein in XCI. This manuscript describes the loss of Ssb/La and suggest that it predominately impacts the canonical 'cloud' formation of Xist RNA on the X chromosome during XCI initiation. Further, they determine that loss of Ssb/La decreases Xist RNA half-life and alters folding of Xist RNA transcripts. Based on their findings, the authors propose that Ssb/La functions to directly bind and fold Xist RNA transcripts in a manner that stabilizes Xist RNA, allowing for proper 'cloud' formation and successful initiation of XCI.

**Major comments:**

The authors made an interesting findings that the SLE-relevant autoantigen Ssb/La stabilizes Xist RNA transcripts, and there is some evidence that this occurs by binding and maintaining proper folding of Xist RNA. Despite these intriguing observations, there are many parts of the manuscript that need to be addressed in order to support the authors main conclusions.

The most troubling aspect of this manuscript is the persistent use of an artificial XCI system in male cells to draw strong conclusions about the function of Ssb in XCI. This issue is prevalent throughout the manuscript, and I question why the authors chose to perform most of their experiments in male cells when the same experiments can be (and have previously been by other groups) performed in female cells. Using male ESCs and then making conclusions for XCI, which is a female-specific process, is a major concern.

In addition to iXist male ESC line, many experiments, such as cell death/survival (Figure 3B, C), allelotype (Figure 3E), Xist could formation (Figure 4A), H3K27me3 and H2AK119ub IF (Figure 5), were performed in female ESC. We chose to do SHAPE and Xist RNA stability assays in iXist male ESC line, because the onset of XCI is much more synchronized in this system. Moreover, in female cells, Xa causes additional layers of complication/noise in the ATAC-sequencing which may not be fully cleared up by data analysis. On the other hand, inducible Xist expression in male ESCs can be used as an experimental system to recapitulate the silencing step of XCI (Ha et al. 2018; Wutz et al. 2002).

• Out of the 138 identified binding proteins, the authors chose to only validate three: Mybbp1a, Tardbp, and Ssb/La. The logic for choosing these candidates is weak, and the authors are only able to validate 1 out of 3 of these proteins.

In theory, all candidate proteins in the list are possibly involved in XCI. There is no method which can help to make accurate prediction. We did not follow a clear-cut logic in selecting candidates for validation, but we do consider the candidate gene’s knockout phenotype, “early embryonic lethality”, as a phenotype consistent with a critical role of the candidate gene in XCI. Meanwhile, in the manuscript, we have discussed why we chose the three proteins for validation as the following:

“……From the candidate proteins, we shortlisted three proteins for individual validation. Myb-binding protein 1A (Mybbp1a, Q7TPV4) and TAR DNA-binding protein 43 (Tardbp, Q921F2) were selected because they are known transcription repressors (11, 12). The Lupus autoantigen La (P32067, encoding-gene name: Ssb) was selected because systemic lupus erythematosus (SLE) is an autoimmune disease characterized by a strikingly high female to male ratios of 9:1 (13). Moreover, its autoimmune antigen La is a ubiquitous and versatile RNA-binding protein and a known RNA chaperone (14). All the three selected candidates have also been identified as Xist-binding proteins in previous studies (2, 4). Moreover, the knockout of these three genes all lead to early embryonic death. Tardbp knockout causes embryonic lethality at the blastocyst implantation stage (15). Mybbp1a and Ssb knockout affect blastocyst formation (16, 17). Early embryonic lethality is a mutant phenotype consistent with a critical role of the mutated gene in XCI (1)** ……”

We used cell death/survival assay to further validate the role of Xist binding protein candidates in XCI. This is a stringent assay. It requires not only that Xist binding protein candidates bind to Xist, but also that the candidates have to be functionally important in XCI.

Indeed, it has been demonstrated by Plath lab (the BioRxix manuscript mentioned by reviewer 1) that Tardbp (also named TDP-43), together with other RBPs, bind to the E repeat of Xist to form a condensate and create an Xi-domain. Yet, Tardbp KD did not rescue cell death caused by forced XCI in male cells in our studies. Thus, only 1 out of 3 of these candidates is validated and further studied. In the manuscript, we also discussed that low efficiency of knockdown and redundancy might contribute to the failure in validation of Tardbp and Mybbp1a.

• Use of the cell death assay is not strong enough to "confirm that La is involved in induced XCI" as stated by the authors. This is a huge overstatement.

Given the diverse functions of Ssb in cell differentiation and proliferation, ribosome biogenesis, transcriptional control and tRNA maturation, one would expect less surviving Ssb knockdown cells. In contrast, more Ssb knockdown cells survives in the presence of Dox, suggesting that Ssb plays an important role in XCI. Considering the reviewer’s comment, we revised the sentence to “further suggest that Ssb is involved in induced XCI”.

While the authors observed differences in X-linked gene expression after Ssb KD, they did not examine expression of these genes in after KD of either Mybbp1a or Tardbp. Are the changes observed in these genes specific to Ssb KD? Or could there still be alterations of X-linked gene expression in the non-validated KDs? This experiment should be performed and included in the manuscript, either within Fig 2 or in the supplemental. As well, inclusion of a well characterized positive control, for example Hnrnpu, as comparison to Ssb should be included.

Mybbp1a and Tardbp were not validated by the cell death assay. Thus, compared with Ssb, Mybbp1a and Tardbp are less important for XCI functionally. We only focused on Ssb in the subsequent studies. Mybbp1a and Tardbp KD could be additional negative controls. Yet, we have used empty vector as a negative control. We do not need so many controls.

As mentioned, Tardbp indeed binds to Xist RNA. It is very likely that Tardbp KD might alter some X-linked gene expression. This rules out Tardbp KD as a good negative control.

If we do not see any effect of Ssb KD on X-linked gene expression, a positive control is absolutely required. However, we have detected that Ssb KD compromises the silencing of several X-linked gene. A positive control might not be essential.

• The authors perform RIP to validate the interaction of Ssb with Xist, but this is performed in male ES cells with induced Xist RNA and with FLAG-tagged Ssb. Aside from these cells being male, in this system Xist RNA expression is much higher than would be found endogenously. RIP should have been done in female differentiated ESCs if there is in fact a role for XCI.

• The authors need to include more details in the methods section to explain how the FLAG-Ssb is expressed in these cells, and why the authors chose to use a tagged contrast over endogenous Ssb. Due to these issues the result from this experiment is essentially meaningless and is not convincing of Ssb interaction with Xist RNA. There is no reason RIP cannot be performed in female cells, and the authors should repeat this experiment in the relevant experimental condition. As well, if a validated Ssb antibody exists the authors should perform RIP using the endogenous protein.

If required, we could try to perform RIP and/or CLIP using Ssb antibody in female cells.

The authors state in Fig 3A-C that the results of the cell death and differentiation experiments "...support a functional role of La in XCI". The authors state earlier that Ssb is a ubiquitous protein that is embryonic lethal (in both female and males). Based on this, the cell death results shown do not support a functional role of La in XCI as the Ssb KD could be having an indirect affect due to its other developmental functions. This manuscript lacks a direct functional link between Ssb and XCI; more data is necessary.

Given the diverse functions of Ssb in cell differentiation and proliferation, ribosome biogenesis, transcriptional control and tRNA maturation, one would expect less surviving Ssb knockdown cells. In contrast, more Ssb knockdown cells survives in the presence of Dox, suggesting that Ssb plays an important role in XCI.

For the data in Fig 3A-C, Ssb KD causes the death of female differentiating cells, but not male differentiating cells. Therefore, it rules out that the death of female cells is due to the general function of Ssb. Rather, the specific role of Ssb in XCI contributes to the female specific cell death.

In Fig 3D, the authors perform ATAC-seq in inducible male ES cells. The authors claim that the extremely slight reduction in chromatin compaction of the Ssb KD compared to control iXist "directly connect La to the heterochromatinization of Xi, supporting a functional role of La in XCI". This is also an overstatement based on the minimal, and possibly indirect, change in compaction. The positive control i-detaA-Xist sample has significantly less compaction (and thus significantly higher compaction defect) than the Ssb KD again disputing the claim stated above. It is unclear why performing ATAC-seq is even necessary, as Ssb isn't stated to have a function in regulating chromatin architecture. In addition, why the authors performed ATAC-seq in the artificial male XCI system and not in the F1 female cells, and the N of the experiment is unclear. If the authors want to include the ATAC-seq in further revisions it should be repeated n=3 in the female system.

The male induced XCI system provides a more synchronized onset of XCI. More importantly, in the male induced XCI system, only one X chromosome exists, avoiding the interference from the active X chromosome in female cells. If ATAC-seq was performed in female cells, only loci with SNPs can be distinguished. The sequencing reads from Xa will create additional layers of complication/noise which may not be cleared up fully by data analysis

“i-delat-Xist” is a positive control to show the experimental system works. It is not justified to compare the chromatin accessibility of the mutant, which is only a Ssb “knockdown” mutant, and the control “i-delat-Xist”, in which the Repeat A is “deleted”. We admit that ATAC-Seq results did not reveal a drastic difference in chromatin accessibility between the wild type sample and the mutant sample. However, as what we discussed in the manuscript, clear difference can still be seen at the 14 h time point. This is shown clearly by the heatmap (Fig. 3E) and the sequencing coverage profile (Fig. S4A).

• In Fig 6, the authors state in their methods that "The shRNA construct, which worked efficiently against Ssb, was not designed against the 3' UTR of the RNA. Therefore, the shRNA is against some of the rescue plasmid constructs. Nonetheless, transfecting the Ssb knockdown cells with the rescue plasmids should compensate the effect of Ssb knockdown and serve as a rescue assay to study the functional domains of La.". This is troubling and seems like a major experimental issue; the specific rescue constructs that may be impacted by this issue are not stated and should be explicitly mentioned. This becomes more confusing when examining the data from rescue experiments.

We pointed out this issue in the original manuscript. We agree that the experiment was not perfectly designed. In the revision, we added in the information on the shRNA target site. Our shRNA targets the LAM domain, so the expression of ∆LAM is not affected by the shRNA. We agree that the detected GFP expression levels of ∆RRM1 and ∆RRM2 are too low to be conclusive. In the revision, we have removed the data point of ∆RRM1 and ∆RRM2. Meanwhile, it is clear that ∆RRM1&2 has a better rescuing effect than ∆NLS, when ∆RRM1&2 and ∆NLS are expressed at similar levels. Ssb is a well-known RNA chaperone/RNA helicase. Identifying Ssb is an Xist-binding protein already suggests the functional role of Ssb in XCI. The data of the plasmid rescue experiments further suggests that Ssb is involved in XCI as a RNA chaperone/RNA helicase.

If it is necessary, we could redo this experiments using a shSsb targeting 3’-UTR or expressing GFP-Ssb immune to shSsb.

In Figure S7, the expression of the rescue constructs deltaRRM1 and deltaRRM2 is extremely low, yet the authors observe a rescue of the cloud phenotype (fig 6D) from those constructs that reaches almost the level of full length Ssb. This is confusing, and the authors need to address this by performing a western blot to show the protein levels of these rescue constructs and discuss further how such a low level of expression can show a rescue phenotype. The results would also be stronger if the authors examined H3K27me3 and H2AK119ub1 enrichment since they observed decreased overlap of these marks with Xist RNA after Ssb KD. Finally, the authors state that "...all three RNA-binding domains are required for the functionality of La in XCI..." however I have trouble coming to this conclusion based on the above issues. As well, if the authors want to support direct function, they should repeat the RIP experiments with these rescues constructs to show that the domains capable of rescue can still bind to Xist RNA.

Reviewer 1 raised similar concerns. In Figure 6C, the live cell counts of ∆RRM1 and ∆NLS are about the same. It might be due to the low expression level of ∆RRM1 (Figure S7). It is clear that ∆RRM1&2 has a better rescuing effect than ∆NLS, when ∆RRM1&2 and ∆NLS are expressed as similar levels. To make the data more straight forward, we removed the data point of ∆RRM1 and ∆RRM2, because of their low expression levels.

As for the Western blot and GFP fluorescence (IF), we have tried both. Neither of them detected GFP signal, reflecting the low expression level of these GFP fusion proteins. The shSsb is not targeting the 5’ or 3’-UTR region, therefore interfering the exogenous Ssb as well. This might be a reason for the low expression of these GFP fusion proteins. If it is necessary, we could redo this experiments using a shSsb targeting 3’–UTR or expressing GFP-Ssb immune to shSsb.

We deleted the sentence "all three RNA-binding domains are required for the functionality of La in XCI".

**Minor comments:**

The authors may want to consider better highlighting the strengths of their "FLAG-out" system. As written, is it difficult to tell how this system sets them apart from the previously published studies referenced in the text, especially as some of these studies used similar crosslinking conditions and cell types. Additionally, the logic and questions the authors pose in the introduction as to why they performed this project are too general and not very strong. For example, the authors mention how might protein machinery may assemble on Xist RNA, and how might Xist RNA may spread on the X chromosome. However neither of these topics are actually addressed in their experiments or discussion. These are interesting questions, but the authors should either discuss them further within the context of their results or take these questions out. It would also be helpful if the authors could better label Figure 4, as it is unclear in the figure itself that Fig 4A is in reference to female cells, but remaining panels are in male cells.

The inducible XCI in male cells is a valid system to recapitulate the silencing step of XCI. It also provides unique advantages in many experiments, such as ATAC-seq. Meanwhile, we did perform extensive functional analysis on the endogenous XCI process using female cells. However, we do realize that presenting the data of induced XCI in male cells together with the data from female cells is confusing to many readers. We have revised the labelling on Figure 3, 4, 5, 7 S6 and S9 (S5 and S8 before revision).

To understand “how the protein machinery is assembled by Xist” and “how Xist spreads along its host chromosome territory” are not specifically the initial aims of this study. We removed the sentences from the introduction section. However, we believe Ssb may provide clues for the future studies to fully address these questions, and we did provide the following thoughts in the discussion section:

“……Secondly, as Ssb is able to utilize ATP to unwind RNA-RNA and RNA-DNA duplex, it may play a more active role in controlling the structural dynamics of Xist in living cells (14, 23). These structural dynamics may be important for recruiting proteins onto the RNA and spreading of the RNA along its host chromosome territory……”

Reviewer #2 (Significance (Required)):

I am not convinced the this manuscript, as written, has sufficient novelty. Ssb/La has been previously identified to be an Xist RNA binding protein with older/different approaches. However, there are some interesting observations in this manuscript. Major revisions are necessary.

We agree with the reviewer that identification of Ssb as an Xist RNA binding protein is not novel. The novelty of our discovery lies in: 1) we developed a new method for isolating lincRNA associated proteins; 2) we confirmed that Ssb is an important player involved in XCI; 3) we showed that Ssb regulates the folding of Xist RNA, consequently the stability of Xist and the formation of Xist cloud.

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

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Referee #2

Evidence, reproducibility and clarity

Summary:

This manuscript describes a novel "FLAG-out" system, where the authors sought to identify Xist RNA binding proteins. The authors focused on a specific protein found in their screen and also identified in several other screens for Xist RNA binding proteins, Ssb/La, and further characterize the role of this protein in XCI. This manuscript describes the loss of Ssb/La and suggest that it predominately impacts the canonical 'cloud' formation of Xist RNA on the X chromosome during XCI initiation. Further, they determine that loss of Ssb/La decreases Xist RNA half-life and alters folding of Xist RNA transcripts. Based on their findings, the authors propose that Ssb/La functions to directly bind and fold Xist RNA transcripts in a manner that stabilizes Xist RNA, allowing for proper 'cloud' formation and successful initiation of XCI.

Major comments:

The authors made an interesting findings that the SLE-relevant autoantigen Ssb/La stabilizes Xist RNA transcripts, and there is some evidence that this occurs by binding and maintaining proper folding of Xist RNA. Despite these intriguing observations, there are many parts of the manuscript that need to be addressed in order to support the authors main conclusions.

• The most troubling aspect of this manuscript is the persistent use of an artificial XCI system in male cells to draw strong conclusions about the function of Ssb in XCI. This issue is prevalent throughout the manuscript, and I question why the authors chose to perform most of their experiments in male cells when the same experiments can be (and have previously been by other groups) performed in female cells. Using male ESCs and then making conclusions for XCI, which is a female-specific process, is a major concern.

• Out of the 138 identified binding proteins, the authors chose to only validate three: Mybbp1a, Tardbp, and Ssb/La. The logic for choosing these candidates is weak, and the authors are only able to validate 1 out of 3 of these proteins.

• Use of the cell death assay is not strong enough to "confirm that La is involved in induced XCI" as stated by the authors. This is a huge overstatement.

• While the authors observed differences in X-linked gene expression after Ssb KD, they did not examine expression of these genes in after KD of either Mybbp1a or Tardbp. Are the changes observed in these genes specific to Ssb KD? Or could there still be alterations of X-linked gene expression in the non-validated KDs? This experiment should be performed and included in the manuscript, either within Fig 2 or in the supplemental. As well, inclusion of a well characterized positive control, for example Hnrnpu, as comparison to Ssb should be included.

• The authors perform RIP to validate the interaction of Ssb with Xist, but this is performed in male ES cells with induced Xist RNA and with FLAG-tagged Ssb. Aside from these cells being male, in this system Xist RNA expression is much higher than would be found endogenously. RIP should have been done in female differentiated ESCs if there is in fact a role for XCI.

• The authors need to include more details in the methods section to explain how the FLAG-Ssb is expressed in these cells, and why the authors chose to use a tagged contrast over endogenous Ssb. Due to these issues the result from this experiment is essentially meaningless and is not convincing of Ssb interaction with Xist RNA. There is no reason RIP cannot be performed in female cells, and the authors should repeat this experiment in the relevant experimental condition. As well, if a validated Ssb antibody exists the authors should perform RIP using the endogenous protein.

• The authors state in Fig 3A-C that the results of the cell death and differentiation experiments "...support a functional role of La in XCI". The authors state earlier that Ssb is a ubiquitous protein that is embryonic lethal (in both female and males). Based on this, the cell death results shown do not support a functional role of La in XCI as the Ssb KD could be having an indirect affect due to its other developmental functions. This manuscript lacks a direct functional link between Ssb and XCI; more data is necessary.

• In Fig 3D, the authors perform ATAC-seq in inducible male ES cells. The authors claim that the extremely slight reduction in chromatin compaction of the Ssb KD compared to control iXist "directly connect La to the heterochromatinization of Xi, supporting a functional role of La in XCI". This is also an overstatement based on the minimal, and possibly indirect, change in compaction. The positive control i-detaA-Xist sample has significantly less compaction (and thus significantly higher compaction defect) than the Ssb KD again disputing the claim stated above. It is unclear why performing ATAC-seq is even necessary, as Ssb isn't stated to have a function in regulating chromatin architecture. In addition, why the authors performed ATAC-seq in the artificial male XCI system and not in the F1 female cells, and the N of the experiment is unclear. If the authors want to include the ATAC-seq in further revisions it should be repeated n=3 in the female system.

• In Fig 6, the authors state in their methods that "The shRNA construct, which worked efficiently against Ssb, was not designed against the 3' UTR of the RNA. Therefore, the shRNA is against some of the rescue plasmid constructs. Nonetheless, transfecting the Ssb knockdown cells with the rescue plasmids should compensate the effect of Ssb knockdown and serve as a rescue assay to study the functional domains of La.". This is troubling and seems like a major experimental issue; the specific rescue constructs that may be impacted by this issue are not stated and should be explicitly mentioned. This becomes more confusing when examining the data from rescue experiments.

• In Figure S7, the expression of the rescue constructs deltaRRM1 and deltaRRM2 is extremely low, yet the authors observe a rescue of the cloud phenotype (fig 6D) from those constructs that reaches almost the level of full length Ssb. This is confusing, and the authors need to address this by performing a western blot to show the protein levels of these rescue constructs and discuss further how such a low level of expression can show a rescue phenotype. The results would also be stronger if the authors examined H3K27me3 and H2AK119ub1 enrichment since they observed decreased overlap of these marks with Xist RNA after Ssb KD. Finally, the authors state that "...all three RNA-binding domains are required for the functionality of La in XCI..." however I have trouble coming to this conclusion based on the above issues. As well, if the authors want to support direct function, they should repeat the RIP experiments with these rescues constructs to show that the domains capable of rescue can still bind to Xist RNA.

Minor comments:

The authors may want to consider better highlighting the strengths of their "FLAG-out" system. As written, is it difficult to tell how this system sets them apart from the previously published studies referenced in the text, especially as some of these studies used similar crosslinking conditions and cell types. Additionally, the logic and questions the authors pose in the introduction as to why they performed this project are too general and not very strong. For example, the authors mention how might protein machinery may assemble on Xist RNA, and how might Xist RNA may spread on the X chromosome. However neither of these topics are actually addressed in their experiments or discussion. These are interesting questions, but the authors should either discuss them further within the context of their results or take these questions out. It would also be helpful if the authors could better label Figure 4, as it is unclear in the figure itself that Fig 4A is in reference to female cells, but remaining panels are in male cells.

Significance

I am not convinced the this manuscript, as written, has sufficient novelty. Ssb/La has been previously identified to be an Xist RNA binding protein with older/different approaches. However, there are some interesting observations in this manuscript. Major revisions are necessary.

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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).

Here Ha et al. has further developed their Pumilio RNA tagging methodology for the isolation of UV-crosslinked proteins that are suggested to associate with Xist RNA in mouse embryonic stem cells (mESCs). Within this study the authors claim to have found the Lupus antigen RNA binding protein (La) as a novel Xist interacting partner that influences the efficacy of X-chromosome inactivation (XCI). The authors use a number of different techniques such as qPCR, fluorescent imaging, ATAC-SEQ and SHAPE to show aberration of XCI upon La shRNA knockdown. However, this study has significant flaws in the efficient isolation and validation of Xist associated proteins using their FLAG-out methodology. Furthermore, later experiments predominantly focus on cell death/survival assays, which is somewhat troubling given the essential roles La plays in processes such as cell differentiation and proliferation, ribosome biogenesis, transcriptional control and tRNA maturation. I feel the authors need to robustly address the potential effects La knockdown may be having on their mESCs.

Major comments:

-Are the key conclusions convincing?

My major concern is in their Xist RNA purification. First of all, I couldn't find any data on proving the enrichment of Xist RNA itself in their Pumilio pull-down experiment. It would have been useful to show Xist RNA enrichment before benzonase step. Secondly, it is hard to imagine the protocol would successfully isolated Xist RNA-protein complexes from the cell. An earlier report by Clemson et al., (J Cell Biol., 1996) has shown that majority of Xist RNA is still stuck in the nucleus after nuclear matrix prep protocol using detergent, which is not so different from the authors' protocol. Moreover, the authors used UV crosslink, which would have made even harder to purify Xist RNA without sonication. Thirdly, as the tag is located on 5' of Xist RNA, it is rather surprising to see that Spen is not detected in their pulldown. Spen is one of the main functional interactors with Xist, robustly detected by several previous reports. Similarly, other high-affinity binders of Xist such as hnRNP-K and Ciz1 were also lacking from this screen. Finally, the peptides found associated with FLAG-out Xist are extremely low in comparison with other data using glutaraldehyde or formaldehyde crosslinking. For example, HnRNP-M found in Chu et al 2015 has 1120 peptide counts in differentiated cells. The authors here use HnRNP-M as a baseline for specific interactions and show a total of 6 peptide counts in Xist expressing cells and 5 in i-Empty cells (Supplementary excel sheet 1). Similarly, the La protein of interest in this study has 8 counts in i-FLAG-Xist and 6 counts in i-Empty. I struggle to see how this result indicate specific Xist binding. Worryingly this is the starting rationale for the rest of their experiments, it is hard to therefore accept the rest of their conclusions either.

The other key conclusion the authors make is from the use of numerous cell death/survival assays for both male and female cell lines. This is extremely troubling in the context of assessing their target protein La. La is involved in multiple RNA maturation events of rRNAs, tRNAs and other polIII transcripts. Furthermore, La has been implicated in binding to the mRNA for Cyclin D1 in both human cells and mouse fibroblasts (NIH/3T3 - male) which show a significant effect on cell proliferation upon siRNA knockdown https://www.nature.com/articles/onc2010425. This, along with the observation that La knock-out blastocysts fail to develop any mice or ES cell lines (male or female) show the effect observed in the authors results is most likely not X-linked cell death https://mcb.asm.org/content/mcb/26/4/1445.full.pdf. The authors need to show that their shRNA KD isn't affecting the proliferation and general fitness of their mESC lines.

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

As discussed above, I feel the authors have not clearly demonstrated Xist specific protein enrichment and haven't proven X-linked cell death. Due to the lack of necessary control experiments as discussed below, I feel the notion that La is involved directly in XCI as an RNA chaperone is currently preliminary/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.

I would suggest them to show RT-qPCR results of Xist RNA enrichment from the sample after flagIP before benzonase treatment.

Also, it would have been more convincing if their negative control construct (i-Empty) would contain 25 copies of PBSb RNA at least.

In Fig1b, the total amount of proteins loaded on the gel is not equivalent between two lanes. The gel should show equivalent amounts of proteins on the gel. It looks like if the negative control sample had been loaded at the same amount as the one with Xist, the band pattern wouldn't be distinguishable between the two samples. Furthermore, as these samples were used in the following mass spectrometry screen it may suggest that the minimal increase in peptide counts observed in the iXist FLAG-out were due to an increased amount of sample being loaded? No controls are conducted to account for this.

The authors quantify cell death in figures 2C - E. It seems clear that shSsb 1 and 2 have an effect on cell count even in the absence of Dox. The rescue effect seen upon Dox addition is minimal when compared to Empty + Dox 2D. The authors ∆A-iXist line with and without Ssb KD/Dox would be an informative control on whether the increase in cell survival that they see is X-linked.

The qPCR results used to validate silencing defects show minor changes in expression and also don't show significant silencing of X-linked genes sufficient for cell death. Could this be because only ~ 50 - 60% of Male iXist cells seem to be expressing in the movies and that this will have an effect on the observed qPCR results? Furthermore, it seems counterintuitive that expression in the Empty male cells increases in 48h compared to 14h. Is this due to cell death and positive selection of cells less able to silence their X-chromosome? How would these data look in the female XX line? How would the data look in a ∆A-iXist line in the presence and absence of shSsb/Dox?

Confusingly, the male line in Fig 3C shows a drop in live cell count at day 6 of differentiation? Surely given their previous results in Fig 2 the Ssb KD should increase cell viability with +Dox? Ssb KD seems to have an adverse effect on ES cells during extended differentiation protocols. In Figure S1 the authors show ~ 8 - 10% survival of male lines during differentiation. Could the recombination of the Xist sequence around the loxP sites enable the cells to outcompete the dead cells? How would iEmpty and ∆A-iXist cells compare here? Have the differentiated cells been tested for their expression of Xist? Additionally, how are there similar live cell counts for male vs female lines when ~90% of male cells die during differentiation? Were more cells plated at day 4? If so, this would bias the competition of male cell survival and therefore make the male line an inappropriate control. Given the essential role of La during development a control is needed to prove that this death is X-linked in the female 3F1 line. For example, an XO cell line retaining the Cast allele and shSsb expression could show the amount of death caused from shSsb alone independent of X-linked cell death.

If I understood correctly, the RNA FISH used dsDNA probes ("Sx9") against 40 kb of the X-inactivation centre (Xic). Surely Tsix or other Xic transcripts will also be visible? Can the authors use their RNA FISH to determine the XX or XO status of their cells? In Figure S5 a number of cells appear to show a single pinpoint of transcription. This could either be low levels of Xist transcripts or Xic transcription from an XO line in which the 129 chromosome is missing. It would be best to solely quantify cells which have two x chromosomes and if a significant amount of X chromosomes have been kicked out, this should be discussed and controlled for.

In Fig6, the authors generated a number of Ssb constructs for a rescue assay. However, these results complicate the matter and raise more questions than they address. It seems odd that the ∆RRM1 does not rescue based on comparison with their putative negative control, ∆NLS. However, the ∆RRM1 + 2 and ∆LAM do rescue the phenotype better than the full length Ssb? This makes no logical sense and highlights the inherent variation in cell viability these generated cell lines seem to show. Following on from this, figure S7 quantifies the GFP tag mRNA levels, depicting all ∆RRM mutants with expression below ~30%? How can ∆RRM1 or 2 be rescuing in this scenario? Have these lines been tested for their XX or XO status? The loss of an X chromosome would lead to a rescue of the cell death phenotype, which is a process known to occur in XX lines that have been cultured for extended periods of time. Could it also be that the cell lines derived are more or less sensitive to exogenous shRNA expression? Also, further validation is needed to assess the efficiency of KD in these lines as theoretically most of these constructs will be targeted by shRNA? What is the endogenous Ssb expression level in these lines? Where in the mRNA sequence are the shRNAs targeted to? Does this make sense on the relative expression levels of ∆RRM1/2 for example? Further testing of GFP expression could also be assessed by quantitative western blot of GFP or even visualised in their RNA FISH/IF samples (Figure S8), currently neither are shown. In addition, some kind of information of stability of each Ssb protein constructs has not been demonstrated.

For the data shown in Figure 7A and B the authors quantify the % of cells with Xist signal. The authors have already shown a defect in Xist visualisation in Ssb KD. Surely it is plausible to assume a faster loss of Xist signal below background in weaker expressing cells. A more appropriate quantification would be the % loss of Xist signal per cell over time.

With Figure 7C and D, the samples have been treated with actinomycin D which globally affects the transcription of cells even the PolIII associated genes Ssb is needed to mature. This treatment could have an added effect on cell mortality and function. Data confirming that actinomycin D doesn't affect the cells disproportionately is needed. The difference in half-life could be attributed to such a treatment.

In summarising the authors claim that La binds Xist to facilitate folding and appropriate spreading of Xist along the X-chromosome. No direct interaction has been shown, CLIP-seq data would resolve this, however I do understand this is a challenging technique. The authors have instead opted for RIP followed by qPCR (Figure S2). However, this process has a greater potential for non-specific recovery of RNAs via indirect binding. Furthermore, qPCR may also amplify the relative abundance of the RNA detected. As multiple nucleolar proteins came down in the mass spec screen and FLAG-Ssb is being over expressed, it is plausible to assume some transient Xist interactions may arise from nucleolar association at which La will be in high abundance. Positive and negative nuclear RNA controls (e.g. 7SK and U1 snRNA respectively) could be used so to determine the amount of non-specific Protein-RNA interactions in their RIP pull downs. Cytoplasmic actin is not an appropriate control as it is cytosolic.

Other than this the authors may want to probe (via IF) for the presence of La accumulation on the X? Many other know factors such as Ciz1, hnrnpK and PRC1/2 complexes show clear accumulation on the X. If I understand correctly, there are many La antibodies on the market and endogenous levels on the X could be assessed. These antibodies may be useful in IP's and pull downs also.

-Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

The experiments suggested above are centrally focussed on the cell lines that are currently in the authors possession with maybe exceptions with the ∆A-iXist-shSsb line suggested. However, this should be reasonably quick to obtain given their previous work for this paper. Most experiments suggested will focus on the validation of karyotype, Xist expression, rescue construct expression, further RNA FISH classification and repeating more appropriate positive and negative controls for a number of experiments. In theory this can be obtained relatively simply and quickly from current resources. But with the sheer volume of further experiments that are required here, this may take a significant amount of time. One vital improvement needed is the replication of mass spec data and the validation of Xist specific recovery and protein enrichment. As it stands this manuscript seems to not have any replicates of the FLAG-out methodology and mass spec data. This is troubling given the poor recovery and specificity of the protein samples obtained. Repeating these experiments would be costly in time and also financially. As it stands, I feel this is essential to conclusively validate their target of interest.

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

The data is presented relatively well, however, it would be beneficial if deailed methods were in the main text and not in a supplementary file. Similarly, more information about the process of differentiation and how cell death/survival was quantified and validated is needed.

- Are the experiments adequately replicated and statistical analysis adequate?

In the most part yes, however there seems to be no replicates of the FLAG-out mass spec screen which is worrying given the minimal specificity observed in the current data.

Minor comments:

- Specific experimental issues that are easily addressable.

Unfortunately, the majority of experimental issues need to be addressed with more robust data which are highlighted above. However, some image analysis, quantification and classification can be amended relatively easily. For example, the live-cell imaging data should be quantified as loss of signal as discussed and RNA FISH should be used to classify XX positive cells and the XO cells can be discarded from analysis.

- Are prior studies referenced appropriately?

Most papers regarding Xist pull down and biology are discussed and referenced appropriately. However, the role in which La plays during development and its aberrant affects upon KD are seemingly downplayed. I would like to see more discussion of potential defects that could be caused due to globally altering cellular RNA folding.

- Are the text and figures clear and accurate?

For the most part, lots of the figures are clear and accurate. Apart from these exceptions.

1.The Y-axis of Figure 2D is confusing. What does 0.3 as a "sum of area" equate to? 30% of the area was ES cells? This doesn't look to be the case from Fig 2C. Also, how does the intensity of the signal compare? The area may not be a good quantification due to ES cells growing in colonies.

2.In the Movies S1-7 there are boxes around certain cells and marked with "Figure 5a - c". This seems to be incorrect as figure 5 is currently the IF staining of polycomb marks. I assume this is in relation to Figure 4b-d?

3.Similarly, in Movies S1-7, the intensities of Xist foci seem by eye to be similar. In the paper it is claimed that the Xist clouds that do form are lower in intensity. Are the Movies depicting the same range of pixel intensities? If not, this should be amended. Similarly, figure 7 seems to show relatively equivalent RNA signal at 0 h?

4.In figure 4A the data is from female XX cells, this should be highlighted to limit confusion with the male iXist data shown below in 4B-E. It would also be helpful to have the male/female icons (as in figure 3B), for each figure that has images of cells. Currently Figure 4, 5, 7, S5 and S8 are lacking these icons.

5.No explanation of the Flag-Ssb expression is given for figure S2. Furthermore, is it really necessary to express Flag-Ssb? There are reasonably good antibodies out there for Ssb as this was how it was originally found in Systemic Lupus patients. Also, no data showing the amount of Ssb being overexpressed is shown. This may have big implication to the validity of the RIP-qPCR analysis.

- Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Most of the data is presented reasonably well, but the robustness of the data somewhat retracts from their conclusions. I feel the certainty of their conclusion regarding Xist specific La binding and RNA chaperone activity is still presumptive and should be rewritten unless more robust data can confirm Xist interaction. I would also suggest deciding on the nomenclature for the protein of interest and use either La or Ssb, the continued use of both through the figures and text can get a little confusing to the reader.

Significance

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

It was a good trial to use PBSb-PUFb system to purify Xist RNA binding proteins, compared to previous reports had used anti-sense oligo purification using complementary sequence to Xist RNA sequences. But currently the purification still needs further validation and repeats to confirm its use. A potential complementary technique could be to isolate Xist directly by using biotinylated probes against the PBSb sequence. The authors further claim the identification of a novel Xist RNA chaperone (La/Ssb) which they say facilitates XCI progression. This would be a novel finding in the field; however, the data is currently not robust enough to support this.

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

This work has focused on the development of a milder methodology for purifying Xist RNA during XCI. Others have published similar methodologies predominantly focusing on purifying Xist RNA directly with biotinylated probes (McHugh et al. Minaji et al and Chu et al.). Although this method boasts a milder purification method, it seems to be low yielding in Xist specific proteins. Others have shown a more robust identification of bona fide Xist binding proteins which are currently missing in this manuscript. A recent preprint from the Plath lab has identified new factors involved in XCI during differentiation and their tethering/rescue experiments are far more convincing than the ones shown in this manuscript https://www.biorxiv.org/content/10.1101/2020.03.09.979369v1. The candidate protein Ha et al have identified has multiple roles in developing cells and has shown to be important during mouse development. However, Ha et al do not robustly show that the knockdown of Ssb causes X-linked cell mortality. Alternatively, as would be presumed from Ssb's essential role in many housekeeping short non-coding RNAs, the cell death seems more ubiquitous upon shRNA KD. Therefore, the link the authors are making here are relatively weak.

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

The audience may be interested in the novel technique and the finding of a novel Xist binding protein.

- 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.

RNA biochemistry and developmental biology

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Reply to the reviewers

General comments

We thank all three reviewers for providing their thoughtful and insightful review comments of our manuscript. We appreciate that the reviewers recognized the significance and impact of our work - “Very little imaging has been done on CAR synapses and to our knowledge this is the first live cell imaging study describing CAR microclustsers” (Reviewer 2); “This is an evolving field and little is known to date. Hence, this study could represent an insightful and important advance to the field” (Reviewer 3). A broad audience from both basic and clinical research sides will be interested in this work: “_This study will have a broad audience. Both scientists that study basic T cell signaling as well as clinicians that use CAR Ts will be interested in this study” (_Reviewer 2); “Audience is to both basic immunologist and cancer biologists” (Reviewer 3).

Meanwhile, we understand that the reviewers have raised a few major and minor issues, which we attempted to address. Most importantly, as suggested by both reviewer 1 and 3, we performed new experiments showing that LAT is not required for microcluster formation of the 1st generation of CAR (new Fig 4 and EV5). This finding suggests that the CAR-independent signaling is due to the intrinsic CAR architecture, and is not dependent on the co-signaling domains of CD28 and 4-1BB.

With the successful solutions to other issues, we believe the manuscript has been significantly improved and is ready for publication. Below we will provide point-to-point responses to each reviewer’s comments.

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

The authors compare the TCR alone to a CAR that contains signaling modules from three receptors- TCR, CD28 and 41BB. The data quality if good and the experiments done are. The difference is quite clear, and I would even like to see a little more of the evidence related to failure of the TCR system.

We appreciate the general positive comment of this reviewer.

More specifically:

Su and colleagues show that a third generation CAR with TCR zeta, CD28 and 41BB signal transduction pathways can activate a T cell for microcluster formation and Gads/SLP-76 recruitment, but not IL-2 production, without LAT. This is surprising because LAT is generally considered, as is up held here, as an essential adapter protein for T cell activation. However, this is not a "fair" experiment as the CAR has sequences from TCR, and two co-stimulatory receptor- CD28 and 41BB. It would be important and very straight-forward to test first and second generation CARs to determine if LAT independence is a function of the CAR architecture itself, or the additional costimulatory sequences. If it turns out that a first generation CAR with only TCR sequences can trigger LAT independent clustering and SLP-76 recruitment then the comparison would be fair and no additional experiment would be needed to make the point that the CAR architecture is intrinsically LAT independent. If the CD28 and/or 41BB sequences are needed for LAT independence then the fair comparison would be to co-crosslink TCR, CD28 and 41BB (an inducible costimulator such that anti-CD27 might be substituted to have a constitutively expressed receptor with this similar motifs) should be cross-linked with the TCR to make this a fair comparison between the two architectures.

We agree with the reviewer that it is critical to make a “fair” comparison between TCR and CAR by testing the 1st generation CAR, which only contains the TCR/CD3z domain. Our new data showed that LAT is not required for microcluster and synapse formation of the 1st generation of CAR, in both Jurkat and primary T cells (new Fig 4 and EV5). This result is similar to our previously reported result from the 3rd generation CAR, although the 1st generation CAR induced less IL-2 production and CD69 expression in LAT null cells than the 3rd generation CAR did (new Fig 6). This suggests that the LAT-independent signaling is intrinsic to the CAR architecture, as the reviewer suggested. The co-signaling domains from CD28 and 4-1BB contribute to, but are not required for bypassing LAT to transduce the CAR signaling.

The authors may want to cite work from Vignali and colleagues that even the TCR has two signaling modules- the classical ZAP-70/LAT module that is responsible to IL-2 and a Vav/Notch dependent module that controls proliferation. Its not clear to me that the issue raised about distinct signaling by CARs is completely parallel to this, but its interesting that Vignali also associated the classical TCR signaling pathway as responsible for IL-2 with an alterive pathways that uses the same ITAMs to control distinct functions. See Guy CS, Vignali KM, Temirov J, Bettini ML, Overacre AE, Smeltzer M, Zhang H, Huppa JB, Tsai YH, Lobry C, Xie J, Dempsey PJ, Crawford HC, Aifantis I, Davis MM, Vignali DA. Distinct TCR signaling pathways drive proliferation and cytokine production in T cells. Nat Immunol. 2013;14(3):262-70.

We appreciate the reviewer’s mentioning this paper from Vignali’s group. It provides insights into understanding LAT-independent signaling in CAR T cells. We cited this paper and added a discussion about the mechanism of LAT-independent signaling.

I would be very interested to see a movie of the LAT deficient T cells interacting with the anti-CD3 coated bilayers in Figure 2A. Since OKT3 has a high affinity for CD3 and is coated on the surface at a density that should engage anti-CD3 I'm surprised there is no clustering even simply based on mass action. The result looks almost like a dominant negative effect of LAT deficiency on a high affinity extracellular interaction. It would be interesting to see how this interface evolves or if there is anti-adhesive behavior that emerges.

We now presented a movie showing the detailed process of LAT deficient GFP-CAR T cells landing on the bilayers coated with OKT3 (new Movie EV5), in which the bright field images delineate the locations of the cells, the OKT3 signal marks TCR, and the GFP signal marks CAR proteins on the plasma membranes. No TCR clusters (as indicated by OKT3) were formed during the landing process. We think the binding of bilayer-presented OKT3 to TCR is not sufficient to trigger TCR microclusters. However, TCR microclusters could form in LAT-deficient cells if OKT3 is presented by glass surface. This point is raised by reviewer 2. We added a discussion on the difference between bilayer and glass-presented OKT3 in inducing microcluster formation.

Reviewer #1 (Significance (Required)):

While it interesting that the CAR is LAT independent, its obvious that the signalling networks are different as the CAR has two sets of motifs that are absent in the TCR, so the experiments as presented are not that insightful about the specific nature of the differences that lead to the different outcomes. At present its not a particularly well controlled experiment as the third gen CAR is changing too many things in relation to the TCR for the experiment to be interpreted. It would be easy to address this is a revised manuscript. To publish as is the discussion would need to acknowledge these limitations. The work is preliminary as science, but it might be useful to T cell engineering field to have this information as a preliminary report, which might be an argument for adding discussion of limitations, but going forward without more detailed analysis of mechanism.

This is an excellent point and we have addressed it. See our response above on the new data of the 1st generation CAR.

Reviewer #2 (Evidence, reproducibility and clarity):

Summary:

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

In this study, the authors have interrogated CAR signaling by imaging CD19-CAR microclusters as well as T cell signaling molecules recruited to CAR microclusters. They report differences spatial assembly between CAR and TCR microclusters that form on a lipid bilayer containing ligand. They also report that LAT is not required for CAR microcluster formation, recruitment of downstream signaling molecules or IL-2 production in Jurkat cells, while in primary T cells IL-2 production by CARs show more of a LAT dependence. From these observations, they conclude that CAR T cells have a rewired signaling pathway as compared to T cells that signal through the TCR.

Major comments:

• Are the key conclusions convincing?

The conclusions made by the authors about CAR microclusters are convincing. However, the conclusion that there is a "rewired signaling network" different from TCR microclusters needs to be more convincingly demonstrated in side-by-side comparisons of TCR and CAR microclusters and synapses.

1. One of the key conclusions in this study is that CAR microclusters form in the absence of LAT, but TCR microclusters require LAT (in JCam2.5 cells in Fig. 2 and primary T cells in Fig. 4B). The requirement of LAT for formation of TCR microclusters is surprising, given multiple reports (one of which the authors have cited) that TCRz and ZAP70 clusters form normally in the absence of LAT (pZAP microclusters form normally in JCam2.5 cells Barda-Saad Nature Immunology 2005 Figure 1; TCRz clusters form normally in LAT CRISPR KO Jurkat cells Yi et al., Nature Communications, 2019 Figure 5). The authors should carefully evaluate TCRz and ZAP70 clusters (that form upstream of LAT) in their assays.

We thank the reviewer for raising this excellent point. LAT-independent TCR clusters were reported in the two papers mentioned by the reviewer, which we think is convincing. However, there is a key difference in the experimental settings between these two papers and ours. We use supported lipid bilayer to present MOBILE TCR-activating antibody to activate T cells, whereas these two papers used IMMOBILE TCR-activating antibody attached to the cover glass. We reasoned that the mobile surface of supported lipid bilayer more closely mimics the antigen-presenting cell surface where antigens are mobile on the membrane. We added a new discussion about the difference between supported lipid bilayer and cover glass-based activation.

We agree with the reviewer on the careful evaluation of TCR and ZAP70 clusters. We had showed the data of TCR clusters as marked by TCR-interacting OKT3 (Fig 3A). We performed new experiments on ZAP70 clusters (new Fig EV3). Our data suggest that, similar to TCR clusters, ZAP70 clusters are not formed in LAT-deficient T cells, if activated by OKT3, but are formed if activated by CD19.

1. The authors make major conclusions about LAT dependence and independence of TCR and CAR microclusters respectively, by using JCam2.5 Jurkat cells and CRISPR/Cas9 edited primary cells. Of relevance to this conclusion, differences in the phosphorylation status of ZAP70 and SLP76 have been described between JCam2.5 cells lacking LAT (in which LAT was found to be deleted by gamma radiation) and J.LAT cells (in which LAT was specifically deleted by CRISPR/Cas9 in Lo et al Nature Immunology 2018). Of importance, pZAP and pSLP76 appeared fairly intact in J.LAT cells, but absent in JCam2.5 cells (Lo et al., Nat Immunol. 2018, Supp Fig 2). Therefore, the authors should evaluate TCRz, ZAP70, Gads and SLP76 in TCR and CAR microclusters in J.LAT cells. This may partly explain the discrepancy in LAT requirement for IL-2 production in JCam2.5 cells and primary cells with LAT CRISPRed out.

Jcam2.5 is a classical well-characterized LAT-deficient cell line that has been continuously used in the T cell signaling field (Barda-Saad Nature Immunology 2005, Rouquette-Jazdanian A, Mol. Cell, 2012; Balagopalan L, J Imm. 2013; Carpier J, J Exp Med, 2018; Zucchetti A, Nat. Comm. 2019). We agreed with the concern that the reviewer raised on the absence of pZAP70 and pSLP76 in JCam2.5 cells. As the reviewer suggested, we obtained J.LAT, which is LAT null but has intact pZAP70 and pSLP76. We introduced CAR into J.LAT and the wild-type control and performed the clustering assay as we did for Jcam2.5. Our results showed that, similar to Jcam2.5, CAR forms robust microclusters in J.LAT cells (new Fig EV2). More importantly, we presented data confirming the LAT-independent CAR clustering, SLP76 phosphorylation, and IL-2 production in human primary T cells (Fig 7). Therefore, the data from three independent cell sources support our conclusion on LAT-independent CAR signal transduction.

1. Since the authors are reporting differences between CAR synapses and TCR synapses, the authors should show side by side comparison of CAR and TCR synapses in Figure 1F.

We focused on characterizing CAR synapse in this manuscript and did not make any conclusion on the difference between TCR and CAR synapse. We are cautious about comparing CAR synapse to TCR synapse for technical reasons: it is critical to use antigen-specific TCRs (e.g. mouse OTI as a common model) to study the TCR synapse pattern so that the study will be physiologically relevant. However, we use human T cell line and human primary T cells for the CAR study. The technical barrier to introduce an antigen-specific TCR complex into these cells, and to activate these cells by purified peptide-MHC complex, is very high. And the result is interesting, but beyond the scope of the current work.

1. The authors should evaluate Gads microcluster formation in response to TCR stimulation via OKT3 (in Figure 4A). Given that it has been reported that TCRz, Grb2 and c-Cbl are recruited to microclusters in Jurkat cells lacking LAT by CRISPR deletion (Yi et al., Nature Communications, 2019), it is important to establish the differences between TCR microclusters and CAR microclusters in side by side comparisons in their assay system.

As the reviewer suggested, we evaluated Gads microcluster formation with TCR stimulation and found that Gads did not form microclusters in LAT-deficient cells (new Fig 5A). Because we only made conclusions on the Gads-SLP76 pathway, we think investigating Grb2 and c-Cbl microcluster, though interesting, is beyond the scope of this manuscript.

1. Similar to the comment about Gads above, the authors should evaluate pSLP76 microcluster formation in response to TCR stimulation via OKT3 in primary T cells lacking LAT in Figure 4C, i.e. side by side comparisons of pSLP76 in TCR and CAR synapses (with and without LAT) should be shown.

We totally agree and performed new experiment on pSLP76 in human primary T cells. Our data suggested that, similar to Jurkat, pSLP76 microclusters remain intact in LAT null primary cells (new Fig 7D and 7E).

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

1. The data shown in Figure 3C shows a reduction in conjugate formation from 80% (WT) to 30% (LAT -). This is a severe reduction and does not support the authors' claim in the corresponding Figure legend that "LAT is dispensable for cell conjugate formation between Jurkat T cells expressing CAR and Raji B cells" and the Abstract that "LAT.....is not required for....immunological synapse formation". Statistical analysis for variance should be shown here.

We agree with the reviewer’s judgement. This cell conjugation analysis was performed using Jcam2.5 cells. As pointed by the reviewer, Jcam2.5 has additional defects in ZAP70 and SLP76 in addition to the lack of LAT. Therefore, we performed the same analysis again using J.LAT cells, which was recommended by the reviewer. Our new data showed that J.LAT cells form conjugates with Raji B cells in a similar rate as the wild-type cells do, as evaluated by statistical analysis (new Fig 6A). Therefore, we think these new data support the claim that LAT is dispensable for cell conjugate formation.

1. In a similar vein, based on data from Movie S5 (where in a single cell, CAR microclusters translocate from cell periphery to center), and Figure 3C where (as described above in point 1) conjugate formation appears to be severely reduced, the authors conclude in the Results and Abstract that "LAT....is not required for actin remodeling following CAR activation". This conclusion is not supported by the data and the authors should remove this claim. Alternatively, actin polymerization in CAR expressing cells (that are LAT sufficient and deficient) can be easily evaluated using phalloidin or F-Tractin.

As suggested by the reviewer, we evaluated actin polymerization in TCR or CAR stimulated cells using a filamentous actin reporter F-tractin. Our data showed that LAT is required for TCR-induced but not CAR-induced actin polymerization (new Fig 5C). Therefore, our results support the claim that LAT is not required for actin remodeling following CAR activation.

• Would additional experiments be essential to support the claims of the paper?<br> Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

Yes. Please see major comments above.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

Yes. It should take 3 months to complete these experiments, since reagents and experimental systems to do these experiments already exist.

• Are the data and the methods presented in such a way that they can be reproduced?<br> Yes. Methods are clearly explained.

We appreciate the reviewer’s recognition of the clarity of the methods part.

• Are the experiments adequately replicated and statistical analysis adequate?

There is no statistical analysis to evaluate differences between samples in Figures 3 and 4. These must be included.

We now added statistical analysis in Fig 5B and 6A (old figure 3 and 4).

Minor comments:

• Specific experimental issues that are easily addressable.

Please see Major Comments above. We believe that the recommended experiments are not difficult to execute since reagents exist and experimental systems are already set up.

• Are prior studies referenced appropriately?

Authors reference 13 and 14 for the following sentence in Results section 2: "Deletion or mutation of LAT impairs formation of T cell microclusters". However, in Reference 14 Barda-Saad et al., actually show that pZAP clusters are intact in JCam2.5 cells lacking LAT. Perhaps authors should clarify that LAT (and downstream signaling molecule) microclusters are impaired when LAT is deleted or mutated.

As the reviewer suggested, we now clarified that clustering of LAT downstream binding partners is impaired when citing reference (Barda-Saad et al).

• Are the text and figures clear and accurate?

Yes. But would be helpful if authors specify what "control" is in Fig. 3B and C. In Figure 3B it is lipid bilayers without CD19, while in 3C it is K562 cells that do not express CD19.

We now specified “control” in the figure.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Would be helpful if authors specify in every Figure or at least Figure legend the experimental bilayer system/ligand used, since they use both OKT3 and CD19 as ligands in the paper.

We now specified the ligand in the figure or legend.

Reviewer #2 (Significance):

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

If CAR microclusters and synapses are appropriately compared in a side by side comparison with TCR microclusters and synapses (as described in comments above), this study will be a conceptual advance in the field of CAR signaling. CAR microclusters have not been studied previously.

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

Very little imaging has been done on CAR synapses and to our knowledge this is the first live cell imaging study describing CAR microclusters.

We appreciate this reviewer’s comment on our work as a conceptual advance in understanding CAR signaling.

• State what audience might be interested in and influenced by the reported findings.<br> This study will have a broad audience. Both scientists that study basic T cell signaling as well as clinicians that use CAR Ts will be interested in this study.

We appreciate this reviewer’s recognition of the broad audience of this manuscript.

• 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.

T cell signaling and imaging of proximal T cell signaling responses.

Reviewer #3 (Evidence, reproducibility and clarity):

This manuscript by Dong and colleagues characterizes the molecular requirements and consequences of engaging a third-generation chimeric antigen receptor (CAR) directed to CD19. Utilizing a biological system of JCaM2.5, a Jurkat T cell mutant with dramatically low levels of LAT, expressing a CAR directed to CD19 fused to the cytoplasmic tails of CD28, 4-1BB and CD3z that is activated by CD19/ICAM1 reconstituted lipid bilayers, the authors demonstrate LAT is not required for microcluster formation, immunologic synapse formation or recruitment of GADS and pSLP76 to the plasma membrane. In contrast, LAT was required for anti-CD3 mediated microcluster formation and pSLP76 recruitment to the plasma membrane. However, LAT does appear to contribute to efficient synapse formation, PIP2 hydrolysis and IL-2 secretion when CAR+ JCaM2.5 or primary T cells are presented with Raji B cells, respectively. These data provide intriguing insights into the molecular requirements for third-generation CAR-T cell functions. The authors have developed quite a nice system to understand the molecular contributions for CAR-T function. A few suggestions are provided here to further enhance the accuracy and significance of the findings:

1. The authors can address whether the LAT-independent effects are due to the attributes of third generation CAR-Ts with inclusion of CD28 and 4-1BB cytoplasmic domains or whether these differences are intrinsic to all CAR-Ts (e.g., first and second generation CARs).

This is an excellent point. We have included new data showing LAT-independent cluster formation of the 1st generation CAR in both Jurkat and primary T cells (new Fig 4 and EV5). Therefore, we favor the second possibility as pointed by the reviewer that LAT-independent effects are intrinsic to CAR architecture.

1. Since a first-generation CAR-T forms non-conventional synapses (Davenport, et al., PNAS 2018), the authors should consider more detailed kinetic analysis to understand the formation and dissolution of the constituents of the synapse with their third generation CAR. This should include measurements of the duration of microcluster and synapse formation as well as further analysis of c- and p-SMAC constituents (e.g., LFA-1, TALIN, LCK and pSLP76) over time.

We agree with the reviewer on a more detailed characterization of the CAR synapse. We measured the duration of the unstable CAR synapse and time from cell landing to the start of retrograde flow (new Fig 2C). We also determined the localization of CD45, a marker for d-SMAC (new Fig 2D). We found that the formation of dSMAC is also not common in CAR T synapse, strengthening our conclusion that CAR forms non-typical immunological synapse.

1. The authors utilize two different activation platforms. While using CD19/ICAM1 reconstituted bilayers, CAR+ JCaM2.5 or CAR+ primary T cells demonstrate no differences compared to wildtype JCaM2.5 cells in the parameters studied. However, when using Raji B cells, the CAR+ JCaM2.5 cells or CAR+ primary T cells demonstrate a more intermediate phenotype with respect to cell conjugate formation (Figure 3C) and IL-2 production (Figure 4D). The authors should analyze whether the differences attributed to the different outcomes may be due to the stimulation mode. For example, is c-SMAC assembly and GADS or pSLP76 recruitment to the plasma membrane still LAT-independent when activated with Raji B cells?

As the reviewer suggested, we examined c-SMAC assembly in Raji B cells conjugated with CAR T cells. We found that the majority of CAR do not form cSMAC (new Fig EV4), which is consistent with the result from the bilayer activation system. Since both Gads and SLP76 are cytosolic proteins, they keep largely in the cytosolic pool which obscures their recruitment and clustering on the plasma membrane when imaged by confocal microscopy at the cross-section of cell-cell synapse.

1. The authors should consider whether CAR expression level affects their observations. For example, do lower levels of CAR expression make the system LAT-dependent? Further, what is the level of the CAR relative to endogenous TCR expression on their primary T cells.

We agree with the reviewer that it is informative to determine if LAT-independent signaling is dose dependent. We tried to measure the CAR concentration relative to the endogenous TCR/CD3z. By western blot using two different antibodies against CD3z, we detected TCR/CD3z expression, but found no bands corresponding to CAR. We believe this reflects a low expression of CAR in our system, which is confirmed by FACS. The general low expression of CAR makes it challenging to sort an even lower CAR-expressing population. Therefore, we sought alternative ways to determine the dose-dependence; we titrated the CD19 concentrations on the bilayer. As shown in the new Figure EV1, CAR formed microclusters similarly in the wild-type versus LAT-deficient cells in a wide range of CD19 concentration. Therefore, we conclude that the LAT-independent cluster formation is robust at low antigen density as well.

Minor comment:

1. Since JCaM2.5 has differences when compared to the parental Jurkat E6.1 T cell line, the authors should utilize JCaM2.5 reconstituted with wildtype LAT as a comparator.<br> Agreeing with this reviewer, we recognized that Jcam2.5 was generated by mutagenesis which may result in protein expression difference for genes besides Lat. As suggested by reviewer1, we used J.LAT, a genuine LAT knockout cell line that is generated by CRISPR-mediated gene targeting, to perform the clustering assay (new Fig EV2). Our results showed that, similar to Jcam2.5, CAR but not the TCR formed microclusters in J.LAT cells.

Reviewer #3 (Significance):

The mechanism(s) by which CAR-Ts function is of high significance from both scientific and clinical viewpoints. From a scientific viewpoint, it provides important basic mechanistic information of how T cells are being activated to kill tumor cells. By understanding the molecular requirements, additional generations of CARs can be designed to provide greater efficacy, overcome resistance and possibly less toxicity.

This is an evolving field and little is known to date. Hence, this study could represent an insightful and important advance to the field.

Audience is to both basic immunologist and cancer biologists.

We appreciate this reviewer’s comments on the high significance of our work to the field of both basic immunology and clinical application.

My expertise is in T cell signaling, T cell biology and immunotherapy.

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Referee #3

Evidence, reproducibility and clarity

This manuscript by Dong and colleagues characterizes the molecular requirements and consequences of engaging a third-generation chimeric antigen receptor (CAR) directed to CD19. Utilizing a biological system of JCaM2.5, a Jurkat T cell mutant with dramatically low levels of LAT, expressing a CAR directed to CD19 fused to the cytoplasmic tails of CD28, 4-1BB and CD3 that is activated by CD19/ICAM1 reconstituted lipid bilayers, the authors demonstrate LAT is not required for microcluster formation, immunologic synapse formation or recruitment of GADS and pSLP76 to the plasma membrane. In contrast, LAT was required for anti-CD3 mediated microcluster formation and pSLP76 recruitment to the plasma membrane. However, LAT does appear to contribute to efficient synapse formation, PIP2 hydrolysis and IL-2 secretion when CAR+ JCaM2.5 or primary T cells are presented with Raji B cells, respectively. These data provide intriguing insights into the molecular requirements for third-generation CAR-T cell functions.

The authors have developed quite a nice system to understand the molecular contributions for CAR-T function. A few suggestions are provided here to further enhance the accuracy and significance of the findings:

1. The authors can address whether the LAT-independent effects are due to the attributes of third generation CAR-Ts with inclusion of CD28 and 4-1BB cytoplasmic domains or whether these differences are intrinsic to all CAR-Ts (e.g., first and second generation CARs).
2. Since a first-generation CAR-T forms non-conventional synapses (Davenport, et al., PNAS 2018), the authors should consider more detailed kinetic analysis to understand the formation and dissolution of the constituents of the synapse with their third generation CAR. This should include measurements of the duration of microcluster and synapse formation as well as further analysis of c- and p-SMAC constituents (e.g., LFA-1, TALIN, LCK and pSLP76) over time.
3. The authors utilize two different activation platforms. While using CD19/ICAM1 reconstituted bilayers, CAR+ JCaM2.5 or CAR+ primary T cells demonstrate no differences compared to wildtype JCaM2.5 cells in the parameters studied. However, when using Raji B cells, the CAR+ JCaM2.5 cells or CAR+ primary T cells demonstrate a more intermediate phenotype with respect to cell conjugate formation (Figure 3C) and IL-2 production (Figure 4D). The authors should analyze whether the differences attributed to the different outcomes may be due to the stimulation mode. For example, is c-SMAC assembly and GADS or pSLP76 recruitment to the plasma membrane still LAT-independent when activated with Raji B cells?
4. The authors should consider whether CAR expression level affects their observations. For example, do lower levels of CAR expression make the system LAT-dependent? Further, what is the level of the CAR relative to endogenous TCR expression on their primary T cells.

Minor comment:

1. Since JCaM2.5 has differences when compared to the parental Jurkat E6.1 T cell line, the authors should utilize JCaM2.5 reconstituted with wildtype LAT as a comparator.

Significance (Required)

The mechanism(s) by which CAR-Ts function is of high significance from both scientific and clinical viewpoints. From a scientific viewpoint, it provides important basic mechanistic information of how T cells are being activated to kill tumor cells. By understanding the molecular requirements, additional generations of CARs can be designed to provide greater efficacy, overcome resistance and possibly less toxicity.

This is an evolving field and little is known to date. Hence, this study could represent an insightful and important advance to the field.

Audience is to both basic immunologist and cancer biologists.

My expertise is in T cell signaling, T cell biology and immunotherapy.

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Referee #2

Evidence, reproducibility and clarity

Summary:

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

In this study, the authors have interrogated CAR signaling by imaging CD19-CAR microclusters as well as T cell signaling molecules recruited to CAR microclusters. They report differences spatial assembly between CAR and TCR microclusters that form on a lipid bilayer containing ligand. They also report that LAT is not required for CAR microcluster formation, recruitment of downstream signaling molecules or IL-2 production in Jurkat cells, while in primary T cells IL-2 production by CARs show more of a LAT dependence. From these observations, they conclude that CAR T cells have a rewired signaling pathway as compared to T cells that signal through the TCR.

Major comments:

Are the key conclusions convincing?

The conclusions made by the authors about CAR microclusters are convincing. However, the conclusion that there is a "rewired signaling network" different from TCR microclusters needs to be more convincingly demonstrated in side-by-side comparisons of TCR and CAR microclusters and synapses.

1. One of the key conclusions in this study is that CAR microclusters form in the absence of LAT, but TCR microclusters require LAT (in JCam2.5 cells in Fig. 2 and primary T cells in Fig. 4B). The requirement of LAT for formation of TCR microclusters is surprising, given multiple reports (one of which the authors have cited) that TCR and ZAP70 clusters form normally in the absence of LAT (pZAP microclusters form normally in JCam2.5 cells Barda-Saad Nature Immunology 2005 Figure 1; TCR clusters form normally in LAT CRISPR KO Jurkat cells Yi et al., Nature Communications, 2019 Figure 5). The authors should carefully evaluate TCR and ZAP70 clusters (that form upstream of LAT) in their assays.
2. The authors make major conclusions about LAT dependence and independence of TCR and CAR microclusters respectively, by using JCam2.5 Jurkat cells and CRISPR/Cas9 edited primary cells. Of relevance to this conclusion, differences in the phosphorylation status of ZAP70 and SLP76 have been described between JCam2.5 cells lacking LAT (in which LAT was found to be deleted by gamma radiation) and J.LAT cells (in which LAT was specifically deleted by CRISPR/Cas9 in Lo et al Nature Immunology 2018). Of importance, pZAP and pSLP76 appeared fairly intact in J.LAT cells, but absent in JCam2.5 cells (Lo et al., Nat Immunol. 2018, Supp Fig 2). Therefore, the authors should evaluate TCR, ZAP70, Gads and SLP76 in TCR and CAR microclusters in J.LAT cells. This may partly explain the discrepancy in LAT requirement for IL-2 production in JCam2.5 cells and primary cells with LAT CRISPRed out.
3. Since the authors are reporting differences between CAR synapses and TCR synapses, the authors should show side by side comparison of CAR and TCR synapses in Figure 1F.
4. The authors should evaluate Gads microcluster formation in response to TCR stimulation via OKT3 (in Figure 4A). Given that it has been reported that TCR, Grb2 and c-Cbl are recruited to microclusters in Jurkat cells lacking LAT by CRISPR deletion (Yi et al., Nature Communications, 2019), it is important to establish the differences between TCR microclusters and CAR microclusters in side by side comparisons in their assay system.
5. Similar to the comment about Gads above, the authors should evaluate pSLP76 microcluster formation in response to TCR stimulation via OKT3 in primary T cells lacking LAT in Figure 4C, i.e. side by side comparisons of pSLP76 in TCR and CAR synapses (with and without LAT) should be shown.

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

1. The data shown in Figure 3C shows a reduction in conjugate formation from 80% (WT) to 30% (LAT -). This is a severe reduction and does not support the authors' claim in the corresponding Figure legend that "LAT is dispensable for cell conjugate formation between Jurkat T cells expressing CAR and Raji B cells" and the Abstract that "LAT.....is not required for....immunological synapse formation". Statistical analysis for variance should be shown here.
2. In a similar vein, based on data from Movie S5 (where in a single cell, CAR microclusters translocate from cell periphery to center), and Figure 3C where (as described above in point 1) conjugate formation appears to be severely reduced, the authors conclude in the Results and Abstract that "LAT....is not required for actin remodeling following CAR activation". This conclusion is not supported by the data and the authors should remove this claim. Alternatively, actin polymerization in CAR expressing cells (that are LAT sufficient and deficient) can be easily evaluated using phalloidin or F-Tractin.

Would additional experiments be essential to support the claims of the paper?<br> Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

Yes. Please see major comments above.

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

Yes. It should take 3 months to complete these experiments, since reagents and experimental systems to do these experiments already exist.

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

Yes. Methods are clearly explained.

Are the experiments adequately replicated and statistical analysis adequate?

There is no statistical analysis to evaluate differences between samples in Figures 3 and 4. These must be included.

Minor comments:

Specific experimental issues that are easily addressable.

Please see Major Comments above. We believe that the recommended experiments are not difficult to execute since reagents exist and experimental systems are already set up.

Are prior studies referenced appropriately?

Authors reference 13 and 14 for the following sentence in Results section 2: "Deletion or mutation of LAT impairs formation of T cell microclusters". However, in Reference 14 Barda-Saad et al., actually show that pZAP clusters are intact in JCam2.5 cells lacking LAT. Perhaps authors should clarify that LAT (and downstream signaling molecule) microclusters are impaired when LAT is deleted or mutated.

Are the text and figures clear and accurate?

Yes. But would be helpful if authors specify what "control" is in Fig. 3B and C. In Figure 3B it is lipid bilayers without CD19, while in 3C it is K562 cells that do not express CD19.

Do you have suggestions that would help the authors improve the presentation of their data and conclusions?<br> Would be helpful if authors specify in every Figure or at least Figure legend the experimental bilayer system/ligand used, since they use both OKT3 and CD19 as ligands in the paper.

Significance (Required)

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

If CAR microclusters and synapses are appropriately compared in a side by side comparison with TCR microclusters and synapses (as described in comments above), this study will be a conceptual advance in the field of CAR signaling. CAR microclusters have not been studied previously.

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

Very little imaging has been done on CAR synapses and to our knowledge this is the first live cell imaging study describing CAR microclusters.

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

This study will have a broad audience. Both scientists that study basic T cell signaling as well as clinicians that use CAR Ts will be interested in this study.

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.

T cell signaling and imaging of proximal T cell signaling responses.

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Referee #1

Evidence, reproducibility and clarity

The authors compare the TCR alone to a CAR that contains signaling modules from three receptors- TCR, CD28 and 41BB. The data quality if good and the experiments done are. The difference is quite clear, and I would even like to see a little more of the evidence related to failure of the TCR system.

More specifically:

Su and colleagues show that a third generation CAR with TCR zeta, CD28 and 41BB signal transduction pathways can activate a T cell for microcluster formation and Gads/SLP-76 recruitment, but not IL-2 production, without LAT. This is surprising because LAT is generally considered, as is up held here, as an essential adapter protein for T cell activation. However, this is not a "fair" experiment as the CAR has sequences from TCR, and two co-stimulatory receptor- CD28 and 41BB. It would be important and very straight-forward to test first and second generation CARs to determine if LAT independence is a function of the CAR architecture itself, or the additional costimulatory sequences. If it turns out that a first generation CAR with only TCR sequences can trigger LAT independent clustering and SLP-76 recruitment then the comparison would be fair and no additional experiment would be needed to make the point that the CAR architecture is intrinsically LAT independent. If the CD28 and/or 41BB sequences are needed for LAT independence then the fair comparison would be to co-crosslink TCR, CD28 and 41BB (an inducible costimulator such that anti-CD27 might be substituted to have a constitutively expressed receptor with this similar motifs) should be cross-linked with the TCR to make this a fair comparison between the two architectures.

The authors may want to cite work from Vignali and colleagues that even the TCR has two signaling modules- the classical ZAP-70/LAT module that is responsible to IL-2 and a Vav/Notch dependent module that controls proliferation. Its not clear to me that the issue raised about distinct signaling by CARs is completely parallel to this, but its interesting that Vignali also associated the classical TCR signaling pathway as responsible for IL-2 with an alterive pathways that uses the same ITAMs to control distinct functions. See Guy CS, Vignali KM, Temirov J, Bettini ML, Overacre AE, Smeltzer M, Zhang H, Huppa JB, Tsai YH, Lobry C, Xie J, Dempsey PJ, Crawford HC, Aifantis I, Davis MM, Vignali DA. Distinct TCR signaling pathways drive proliferation and cytokine production in T cells. Nat Immunol. 2013;14(3):262-70.

I would be very interested to see a movie of the LAT deficient T cells interacting with the anti-CD3 coated bilayers in Figure 2A. Since OKT3 has a high affinity for CD3 and is coated on the suface at a density that should engage anti-CD3 I'm surprised there is no clustering even simply based on mass action. The result looks almost like a dominant negative effect of LAT deficiency on a high affinity extracellular interaction. It would be interesting to see how this interface evolves or if there is anti-adhesive behavior that emerges.

Significance

While it interesting that the CAR is LAT independent, its obvious that the signalling networks are different as the CAR has two sets of motifs that are absent in the TCR, so the experiments as presented are not that insightful about the specific nature of the differences that lead to the different outcomes. At present its not a particularly well controlled experiment as the third gen CAR is changing too many things in relation to the TCR for the experiment to be interpreted. It would be easy to address this is a revised manuscript. To publish as is the discussion would need to acknowledge these limitations. The work is preliminary as science, but it might be useful to T cell engineering field to have this information as a preliminary report, which might be an argument for adding discussion of limitations, but going forward without more detailed analysis of mechanism.

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Reply to the reviewers

Rebuttal to reviewers ReviewCommons manuscript # RC-2020-00281

We would like to thank the reviewers and editors of Review Commons for evaluating our manuscript entitled “Transcriptional comparison of Testicular Adrenal Rest Tumors with fetal and adult tissues” and providing their valuable comments. We have listed the reviewers’ comments along with our response and amendments below.

Board Advice on initial submission:

This seems to be a study mainly relevant to the field of Testicular Adrenal Rest Tumors (TART). It presents the first RNAseq profiling of these tumors in multiple human samples at different stages. This has the potential to advance knowledge in this particular field. It would be less interesting to researchers interested in tissue spatial transcriptomics in general, since the experimental and computational tools are quite standard, but the findings may be important to the TART field.

Response: Indeed, this is the first study using transcriptomics to characterize Testicular Adrenal Rest Tumors, a frequent occurrence in patients with Congenital Adrenal Hyperplasia. It is also the first to find that the reported adrenal and testicular features of these tumors can be found in a single cell. We therefore believe this study is not only of interest to those working in the TART field, but also in development, endocrinology and andrology in general.

Comments Reviewer #1:

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

**Summary:**

The manuscript by Schroder M., et al describes the whole transcriptome of testicular adrenal rest tumors (TART) and shows that TART tissue is characteristically similar to adult adrenal and testicular rather than fetal adrenal and testicular tissues. The authors propose that their previous claim that TART is derived from an undifferentiated pluripotent progenitor is likely untrue and claim that TART likely originates from a mature cell type with both adrenal and testicular characteristics. The authors describe a unique cell type most similar to the adult adrenal, but with variable testis-specific gene expression patterns. The finding of overexpressed genes associated with ECM remodeling is interesting and may provide insight into the natural history of these tumors. A strength of the study is the number of tissue samples since surgery for these rare tumors is usually not performed.

**Major Comments:**

• The key conclusions are mostly based on RNA studies, thus their claims are preliminary.

Response: We agree that a major part of our conclusions is based on RNA studies. Although indeed primarily based on transcriptomics, this claim is, in our opinion, not preliminary as the identity of TART cells can definitively be deduced from their expression profile. Our second key conclusion, i.e. that TART cells comprise both adrenal and testicular features within the same, unique, TART specific cell, is based on immunohistochemistry of adrenal and testis-specific enzymes.

In Figure 1/Result p. 3: Authors claim that there were no exclusive HSD17B3 staining cells without CYP11B1, however Figure 1 looks like there are exclusively green (HSD17B) areas (especially TART3). The authors need to address this. It appears as if there are mature Leydig cells. This is important because the presence of Leydig cells would affect the interpretation of the findings.

Response: We do understand the concern of the reviewer. Aspecific background staining for HSD17B3 in TART samples complicated the differentiation between specific and background staining. This can be seen when comparing the staining in HSD17B3-positive (Leydig) cells with the background staining in non-Leydig cells in testis tissue and in a portion of TART cells. In TART, we found that cells with high intensity, specific HSD17B3 staining all also showed CYP11B1 staining, but not vice-versa. However, we do acknowledge that due to this -most likely background- staining, the occurrence of mature Leydig cells in TART cannot be completely excluded based on our results.

Therefore, we have tried to be more careful in our claims in the results section (page 3; TART cells express adrenal- and Leydig cell-specific steroidogenic enzymes paragraph) and we have addressed this in the discussion section (page 5/6):

High background staining for HSD17B3 complicated the differentiation between specific and background staining. For some cells this exclusive HSD17B3 staining might have been specific and therefore, despite that most HSD17B3-positive cells were positive for CYP11B1, the absence of mature Leydig cells in TART could not be guaranteed by these results.

Discussion: authors state that based on their previous observations that fetal Leydig cells have both adrenal and testis developmental potential. It was speculated that TART might have been derived from a totipotent progenitor cell type, but the current study shows that these tumors lack similarities with fetal tissues. Thus, the authors claim that these tumors are not derived from the transdifferentiation of pluripotent cells. However what is the origin of this mature distinct cell type? Is it not possible that this distinctive cell type is derived from a common progenitor since the testis and adrenal gland are derived from the same adrenogonadal primordium? Lack of similarities with fetal tissues at this late stage of development does not necessarily rule out a common progenitor origin.

Response: In this study, we compared the TART transcriptome with fetal tissues, as we hypothesized these might be similar considering the likely progenitor origin of TART cells. However, this was not the case, and we showed that the transcriptomic profile of TART resembles the transcriptomic profile of mature cell types, rather than their fetal counterparts. Therefore, we conclude that the hypothesis that TART arises from progenitor cells is not supported by our data. The reviewer is correct that we did not prove that it is not derived from pluripotent cells. We have therefore added the following text to the discussion:

Although we here find that the transcriptome of TART tissues are clearly distinct from fetal tissues, we did not prove that TART does not originate from fetal Leydig cells. TART being derived from a multipotent progenitor cell is still possible as we initially hypothesized, given the fact that TART is likely already present in utero and its resemblance to both testis and adrenal tissues which derive from a common primordium. Therefore, we were surprised to find TART to be more like adult adrenal and testis tissue, raising the possibility of TART being derived from a ‘mature’ progenitor cell type, i.e. adult stem Leydig cells or adrenal progenitor cells, that under influence of high ACTH levels and/or the localization in the testicular region might differentiate into a distinct cell type that expresses both adrenal- and testis-specific markers. However, this remains to be established.

**Minor Comment:**

In Methods: Was RNA isolated from FFPE sections or frozen tissue?

We agree that this was not clearly mentioned enough in our original manuscript, as both frozen (RNA isolation) and FFPE (IHC) material was used. We have now clarified in the methods section that the RNA was retrieved from frozen tissue samples (page 8; RNA isolation, library preparation, and sequencing paragraph).

Reviewer #1 (Significance (Required)):

This first study of transcriptome analysis of TART provides useful insight into the characteristics of these rare tumors that commonly develop in males with classic CAH. This study provides a foundation for further investigation of the biological pathways contributing to the development of TART, the most common cause of male infertility in CAH. This study is of interest to endocrinologists. Reviewed by a pediatric endocrinologist and molecular biologist - we are not completely aware of the sequencing analysis but are familiar with clustering and enrichment analysis.

Comments Reviewer #3:

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

The manuscript by Schröder et al describes the transcriptome sequencing of TARTs in CAH/CS in order to sort out the origin of TARTs. This is an interesting subject and the manuscript is well-written but I have a few comments that could be addressed.

• Some parts of the Results should be in the Methods and some in the Discussion. In the Results only the results should be given.

Response: We agree that we have incorporated some methodological sentences and some concluding remarks in the results sections to, in our opinion, improve the flow of the manuscript. As the manuscript guidelines differ between journals, we have for now decided not to change this. We will do so if this is wanted by the concerning journal.

Normally TARTs are not removed or biopsied, if not by mistake... Thus, most centers would not have tissue samples of TARTs at all. How come you have so many samples available?

Response: We thank the reviewer for highlighting this. As indeed TARTs are not routinely removed, the number of TART tissues included in our dataset is unique. Most of the TART samples were already obtained in 2004 because of reported pain and discomfort and in an attempt to improve semen quality in these patients. Removal of those particular TART samples have led to new insights that removal of longstanding TART did not improve semen parameters, nor parameters of pituitary-gonadal function (Claahsen-van der Grinten et al., 2007). Therefore, to date, the only indication for surgery for the removal of longstanding TART is the relief of pain or discomfort.

Ref 2 and 3 are rather old and similar. Could newer review references be used instead?

Response: We have changed those two references for a more recent review by Dr. Witchel on Congenital Adrenal Hyperplasia, who addresses both statements in a more recent review (Witchel, 2017).

Reviewer #3 (Significance (Required)):

New and significant study. Very interesting for people dealing with CAH patients.

References

Claahsen-van der Grinten, H. L., Otten, B. J., Takahashi, S., Meuleman, E. J. H., Hulsbergen-van de Kaa, C., Sweep, F. C. G. J., & Hermus, A. R. M. M. (2007). Testicular adrenal rest tumors in adult males with congenital adrenal hyperplasia: Evaluation of pituitary-gonadal function before and after successful testis-sparing surgery in eight patients. Journal of Clinical Endocrinology & Metabolism, 92(2), 612-615. doi:10.1210/jc.2006-1311

Witchel, S. F. (2017). Congenital Adrenal Hyperplasia. J Pediatr Adolesc Gynecol, 30(5), 520-534. doi:10.1016/j.jpag.2017.04.001

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Referee #2

Evidence, reproducibility and clarity

The manuscript by Schröder et al describes the transcriptome sequencing of TARTs in CAH/CS in order to sort out the origin of TARTs. This is an interesting subject and the manuscript is well-written but I have a few comments that could be addressed.

1. Some parts of the Results should be in the Methods and some in the Discussion. In the Results only the results should be given.
2. Normally TARTs are not removed or biopsied, if not by mistake... Thus, most centers would not have tissue samples of TARTs at all. How come you have so many samples available?
3. Ref 2 and 3 are rather old and similar. Could newer review references be used instead?

Significance

New and significant study. Very interesting for people dealing with CAH patients.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript by Schroder M., et al describes the whole transcriptome of testicular adrenal rest tumors (TART) and shows that TART tissue is characteristically similar to adult adrenal and testicular rather than fetal adrenal and testicular tissues. The authors propose that their previous claim that TART is derived from an undifferentiated pluripotent progenitor is likely untrue and claim that TART likely originates from a mature cell type with both adrenal and testicular characteristics. The authors describe a unique cell type most similar to the adult adrenal, but with variable testis-specific gene expression patterns. The finding of overexpressed genes associated with ECM remodeling is interesting and may provide insight into the natural history of these tumors. A strength of the study is the number of tissue samples since surgery for these rare tumors is usually not performed.

Major Comments:

1. The key conclusions are mostly based on RNA studies, thus their claims are preliminary.

2. In Figure 1/Result p. 3: Authors claim that there were no exclusive HSD17B3 staining cells without CYP11B1, however Figure 1 looks like there are exclusively green (HSD17B) areas (especially TART3). The authors need to address this. It appears as if there are mature Leydig cells. This is important because the presence of Leydig cells would affect the interpretation of the finidings

3. Discussion: authors state that based on their previous observations that fetal Leydig cells have both adrenal and testis developmental potential. It was speculated that TART might have been derived from a totipotent progenitor cell type, but the current study shows that these tumors lack similarities with fetal tissues. Thus, the authors claim that these tumors are not derived from the transdifferentiation of pluripotent cells. However what is the origin of this mature distinct cell type? Is it not possible that this distinctive cell type is derived from a common progenitor since the testis and adrenal gland are derived from the same adrenogonadal primordium? Lack of similarities with fetal tissues at this late stage of development does not necessarily rule out a common progenitor origin.

Minor Comment:

In Methods: Was RNA isolated from FFPE sections or frozen tissue?

Significance

This first study of transcriptome analysis of TART provides useful insight into the characteristics of these rare tumors that commonly develop in males with classic CAH. This study provides a foundation for further investigation of the biological pathways contributing to the development of TART, the most common cause of male infertility in CAH. This study is of interest to endocrinologists. Reviewed by a pediatric endocrinologist and molecular biologist - we are not completely aware of the sequencing analysis but are familiar with clustering and enrichment analysis.

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Reply to the reviewers

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

The manuscript entitled "Vasohibin-1 mediated tubulin detyrosination selectively regulates secondary sprouting and lymphangiogenesis in the zebrafish trunk" by de Oliveira investigates the function of the carboxylpeptidase Vasohibin during the formation of the zebrafish trunk vasculature and reports a requirement of Vasohibin for secondary sprout formation and in particular the formation the lymphatic vasculature.

Having established the expression of Vasohibin in sorted ECs of 24 hpf embryos, the remaining study addresses the function of Vasohibin in this cell type. It is largely based on the use of a splice-site interfering morpholino. Particular commendable is the analysis, demonstrating that the KD of vash-1 indeed results in a significant reduction of detyrosination in endothelial tubulin. Findings in the vascular system then include: (i) the detection of increased division and hence supernumerous cells occurring selectively in 2nd sprouts from the PCV; (ii) an increased persistence of the initially formed 3 way connections with ISV and artery; (iii) reduced formation of parachordal lymphangioblasts and (iv) a reduced number of somites with a thoracic duct segment; (v) frequent formation of lumenized connections between PLs (where present) and ISV. To demonstrate specificity, the approach was repeated with a different morpholino and defects were partially rescued by MO-insensitive RNA.

Possible additional and relevant information could include data on a vash-1 promotor mutant to independently verify the MO-based functional analysis. Mutants would also allow analysis of further development, are the defects leading to the demise of the fish or is a later regeneration and normalization of the lymphatic vasculature observed?

We agree that a mutant would be desirable to validate the phenotypic analysis of the morpholinos used, and would also allow for further analysis. However, this is not achievable within a reasonnable time frame, especially in the context of current work restrictions.

In addtion to the two splice morpholinos currently used to knockdown vash-1 expression, we will use an ATG morpholino to further investigate our observations and hypothesis regarding the role of vash-1 in lymphatic vessels formation. We will also validate it by westernblot and attempt to rescue it with mRNA.

We have not investigated the phenotype past 4 dpf. We will add investigation of lymphatics and morphology at 5 dpf.

In addition, are other lymphatic vessel beds like the cranial lymphatics affected?

Using the Tg[fli1a:EGFP]y7 line, we have not been able to identify apparent differences in other vascular beds including the cranial lymphatics. However a detailed fine-grained investigation of the cranial vascular bed has not been performed. Given the focus of the present study on the trunk vasculature to understand the mechanisms of vash-1, we feel that a detailed analysis of cranial lymphatics would at this stage be somewhat out of scope.

PLs have been demonstrated to be at least partially guided in their movement by the CXCR4/SDF1 system and SVEP1. Has the expression of these factors been tested in vash-1 KDs?

We have not investigated the potential role of the CXCR4/SDF1 system and SVEP1 in vash-1 regulation of lymphangiogenesis. We will investigate the expression of cxcr4a, cxcl12a, cxcl12b and svep1 by in situ hibridization upon vash-1 knockdown.

With regards to the frequently observed connections of PLs and ISVs in vash-1 morphants, can the proposed lumen formation of these shunts be demonstrated e.g. by injection of Q-dots or microbeads into the circulation?

Although the lumenisation is very clear thanks to the membrane targeted expression of the label in this line, we will further analyse whether these abberant ISV to ISV connection can be perfused by Q-dots injections.

Concerning the mechanisms of these defects, is it possible to analyse the asymmetric cell division leading to 2nd sprouts in greater detail? Is the same number or are more cells sprouting form PCV and can the fli1ep:EGFP-DCX cell line in fixed samples be used to identify the spindle orientation in dividing cells?

We agree with the reviewer and plan to use the Tg[fli1ep:EGFP-DCX] fish line to investigate spindle asymmetry in uninjected embryos, as well as compare the spindle in control MO and vash-1 KD embryos. Vash-1 has been shown to regulate spindle formation in osteosarcoma cells (Liao et al., 2019). We will attempt to clarify whether this function is conserved in endothelial cells and contributes to the control of endothelial cell proliferation during initiation and formation of secondary sprouting.

We also agree that it is important to look at the PCV in the begining of secondary sprouting and will clarify whether the sprouting is initiated by an increased number of cells.

**Minor issues:** Page 5, Mat & Meth, please spell out PTU at its first mention.

This has been corrected accordingly (see page 4).

Page 6 Mat & Meth, Secondary sprout and 3-way connection parameters: The number of nuclei was assessed in each secondary sprouts (del s, singular) just prior...

This has been corrected accordingly (see page 5).

Page 16, 8th line from bottom: Recent work demonstrated that a secondary sprout either contributes (add s) to remodelling a pre-existing ISV into a vein, or forms (add s)a PLs (Geudens et al., 2019).

This has been corrected accordingly (see page 16).

Page 25, Legend to Fig. 2D-G: "...G,G' shows quantification of dTyr signal upon vash-1 KD..." Fig2 G,G' show immunostaining rather than quantification of the dTyr signal, which is shown Fig. 2H-J

This has been corrected accordingly (see page 26).

Fig. 1D / Fig. 2H-J please increase weight of the error intervals and / or change colour for improved visibility

This has been corrected accordingly (Fig. 1D and 2H-J), and we added n.s. to Fig. 1D.

Reviewer #1 (Significance (Required)):

Taken together the manuscript is comprehensively written and the study provides a conclusive analysis of the MO-mediated KD of Vasohibin in zebrafish embryonic development presenting significant novel findings. Known was a generally inhibitory function of Vasohibin on vessel formation and its enzymatic activity as a carboxylpeptidase responsible for tubulin detyrosination, affecting spindle function and mitosis. New is the detailed analysis of the Vasohibin KD on zebrafish trunk vessel formation and the description of a selective impairment of 2nd sprout formation. The manuscript is of interest for vascular biologists.

REFEREES CROSS-COMMENTING

I fully concur with the comments of reviewer #2, all three reviews find that this study is of significant interest to the vascular biology community as the relevance of tubulin detyrosination for developmental angiogenesis has not been investigated. Also all three reviews highlight the potential limitations of the use of splice morpholinos (suggested alternatives include ATG morpholinos and CRIPR mutants), the requirement to provide further evidence for a endothelial cell autonomous defect and the need to clarify some of the data representation.

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

**Summary:**

The manuscript by Bastos de Oliveira et al. describes an important investigation of the endothelial tubulin detyrosination during vascular development. Namely, they found detyronised microtubules in secondary sprouts, which is absent in MO-vash-1 treated embryos. The authors use the vash-1 morpholino approach to uncover the developmental consequences of suppressed detyrosination in angiogenesis and lymphangiogenesis in vivo in zebrafish. By a combination of transgenic lines, immunohistochemistry and time-lapse imaging, Bastos de Oliveira et al., have found that Vash-1 is a negative regulator of secondary sprouting in zebrafish. The authors showed that in the absence of Vash-1 more cells are present in the secondary sprouts due to increased cell proliferation; however lymphatic vascular network fails to form. The current manuscript requires additional experimental evidence to support the conclusions. Please see below the major technical concerns and minor comments.

**Major comments:**

-This study is based on analysis of the phenotypes observed in embryos injected with vash-1 morpholino. The authors use two different types of splice morpholinos, perform rescue experiments with RNA, and validate one MO-vash-1 with western blot. Morpholinos are not trivial to work with, and the results are variable hence additional controls need to be included, as following the recommendation put together by the zebrafish community (Stainier et, al., Plos Genetics, 2017). As the severity of the phenotypes comparing MO1 with MO2 is different and MO-vash-1 embryos appear developmentally delayed (Figure 2D-F and 5E-F overall size seem to be affected), additional MO is required, for example, ATG-MO or generation of CRISPR mutant would be favourable. All the morpholino used need to be validated using an antibody, RT-PCR and qPCR. It is essential to carry out the rescue experiments for all the MO used in this study and following the guidelines. Including the dose-response curve, data would be informative.

We agree with the reviewer and the recommendations of the zebrafish community. We will investigate the phenotypes with another KD strategy, such as the ATG-Morpholino suggested by the reviewer. We will also supply more validation of the MO2 including RNA rescue and westernblot (already included in Fig. 5 I).

We added dose-response curves (Supp. Figure 1 E,G) and a developmental morphology assessment for the morpholino 1 (Supp. Figure 1 A,B).

Given our extensive analysis of the effects of vash-1 KD, we believe the embryos in 2F are not developmentally delayed. However, the image in figure 2F does give that impression, and therefore may have triggered the reviewer’s concerns. We double checked and found that due to an oversight, we included a picture from a slightly different region of the trunk in comparision to Fig. 2D. We will add pictures of the same trunk region (Fig.2D-F) as we have done in all other figures. We nonetheless supply a supplementary figure 1 showing and quantifying the development of the analysed vash-1 morphants.

-In addition to EC, the levels of dTyr are lower in MO-vash-1 in neural tube and neurons spanning the trunk (Figrue 2 D-G'). These have been previously shown to be important for secondary sprouting. Is it possible that the observed phenotypes in the secondary sprouting are due to defects in these neurons?

We agree with the reviewer that a potential contribution of altered neuronal differentiation to the vascular phenotype should be clarified. We will assess the morphology of the neurons and their dendrites relevant for pathfinding (Lim et al., 2011) in vash-1 KD embryos, using a pan-neuronal zebrafish line, as well as via immunostaining against alpha-tubulin. Should we find evidence for changes in neuronal cells, we will attempt to clarify a cell autonomous role of vash-1 by transplantation experiments.

-Embryo number used in this study appears to be low especially in figure 3G, 5D, 5G, to conclude draw conclusions from these experiments, the number of embryos used should be higher than 20. Figure 4J please specify how many embryos were used.

We will increase the number of embryos per condition to a minimum of 20 embryos and update the averages in the text for 3G (control: 7 and vash-1 KD: 11 embryos).

In 5D and 5G each point is an embryo and more than 20 embryos per condition were used (in 5D 23-35 embryos per condition, in 5G 60-63 embryos/condition), we corrected the legend 5D and 5G (see page 27) and made it clear that each point in the graph corresponds to one embryo (5D- percentage of PLs associated with veins in each embryo; 5G- percentage of somites with toraxic duct in each embryo).

In 4J, 18 embryos were used for control (about 3 sprouts/embryo– 52 sprouts quantified) and 7 embryos for vash-1* KD condition (about 3 sprouts/embryo – 24 sprouts quantified). We corrected the number of control sprouts in the legend and added the number of embryos to increase clarity (see page 27).

-The authors hypothesise that VASH acts in the sprouting endothelial cells, based on the Q-PCR in Figure 1. However, in this experiment all EC have been sorted thus this remains ambiguous in which cell types vash-1 is expressed. Please provide the expression pattern for vash-1 across the developmental stages the phenotypes are observed.

We agree with the reviewer that it would be beneficial to understand the expression pattern of vash-1 in wild type embryos. We plan to perform in situ hybridization for vash-1 mRNA.

-Throughout the manuscript the authors refer the lymphatic identity, however, there is no evidence in the paper that the identity status has been assessed. To support these claims Prox1 immunohistochemistry or analysis of prox1 expression in the reporter line would be appropriate.

We agree with the reviewer and plan to perform a Prox1 immunostaining (Koltowska et al., 2015) in vash-1 KD embryos at 34-36 hpf (secondary sprouting) to investigate Prox1 levels upon vash-1 KD.

**Minor comments:**

-The authors refer to the literature where overexpression of VASH suppresses the angiogenesis. As the RNA injections were used in rescue experiments, the data of vash-1 RNA injections into the wild-type embryos would be beneficial.

We have injected vash-1 RNA into a control morpholino injected embryos (28 control embryos, 14 Vash-1 RNA injected embryos) and we observed a significant decrease in PLs at 52 hpf (average of -control: 87,5% somites with PLs to 67% somites with PLs in vash-1 RNA embryos). This could be due to a decrease of secondary sprouting, which would be in accordance with the current literature that vash-1 overexpression is anti-angiogenic. We will further investigate and add the results to figure 5. Figure 1. vash-1* mRNA injection leads to a decrease in somites with PLs (preliminary).

-In figures 2J, 3J, 3K, 3N, 4J, 5C, 5D and 5G the N number was set for examples as the number of sprouts, the number of somites with TD, number of ISV. To strengthen the observation in the manuscript quantification of the sprouts, PL, vISVs and lymphatic phenotypes with N set as the number of embryos would be more informative. Indicating the number of embryos used, in the graphs, would be helpful.

We agree with the reviewer and have added embryo numbers in all legends and graphs. In 2J, 3J, 3K, 4J each point is a sprout, a cell division or an ISV, corresponding to the N. We agree that the number of embryos could be more clearly stated, so we added the number of embryos analysed in the figure legend and will add them in the graphs.

In 5C, 5D and 5G each point corresponds to an embryo (clarified in the legend of Fig. 5- see page 27).

Fig. 5C refers to the percentage of somites with PLs in each embryo, 5D refers to percentage of the existing PLs in one embryo connected to a venous ISV, 5G corresponds to percentage of somites with a TD segment in each embryo.

-In Figure 5A, B and D the authors quantify what they refer to as a lumenised connection between the vISVs and PL. In the control image (second star), a somewhat lumenised structure is present, clarification of how the scores were set is missing.

In Fig. 5C we show a quantification of the percentage of somites with PLs per embryo, by counting the PLs identified with an asterisk in Fig. 5A-B. PLs are normally not lumenised, with few exceptions also ocurring in wild-type – see Fig. 4 in (S Isogai et al., 2001).

In Fig. 5D we quantified the proportion of PLs associated/connected with venous ISvs (see Methods section page 6), by 52 hpf in control and vash-1 morphants.

In 5B and 5F,F‘, the arrowheads identify lumenised PLs present in vash-1 KD embryos. We will add a quantification of kdr-l:ras-Cherry positive ISV-to-ISV connections, corresponding to the lumenised endothelial connections, since kdr-l:ras-Cherry signal labels endothelial (and not lymphatic) cells and is particularly strong at the luminal endothelial membrane of the vessel.

-In Figure 3 E and F the authors show the excessive sprouting phenotype between controls and Mo-vash-1. The images presented are taking from different parts of the embryos (middle of the trunk vs plexus region), hampering the comparison between the two groups. The quantification of the phenotypes in both experimental groups should be in the same region of the embryo, as the local difference can occur. It is key to provide representative images to support these observations.

The images presented are representative of the phenotype quantified, and the time-lapses were done in comparable regions of the zebrafish trunk (+- 1-2 somites in both groups due to drift during image aquisition), making the comparison possible.

-Figure 1D the vash-1 expression levels in EC seem very variable in this graph, therefore no conclusion can be drawn from this data, especially as the authors do not provide the p-values.

We added n.s. in the graph, to make it clear that the difference between developmental stages is not significant, potentially due to high biological variability between embryos, as seen in two primer pairs. We believe that presenting this biological variability is of importance to the readers.

We write on page 12 about this result: „During the sprouting phase (24hpf), vash-1 expression was 5-7 times higher in endothelial than in non-ECs, decreasing at 48 hpf (Fig. 1C-D). Although these results are not significant, they were independently confirmed with a second primer set.”. The only conclusion we made from this data is that Vash-1 is dynamically expressed in the zebrafish endothelium during development, as we now added in the discussion (page 14).

-In the introduction, the authors state: 'Although primary and secondary sprouts appear morphologically similar, with tip and stalk cells' - Please provide the reference that supports the claim that secondary sprouts have tip-stalk cells morphology/organisation.

Although many studies have investigated primary and secondary sprouting, identifying both shared as well as distinct molecular regulation, and show morphological details that are apparently similar, a formal claim that secondary sprouts show tip and stalk cell identities and behaviour is hard to find. Given that this is not relevant for the central findings of the work, we modified the sentence and added a reference “Although primary and secondary sprouts appear morphologically similar, with tip and stalk cells” (Sumio Isogai et al., 2003)…” See page 2.

We also updated the discussion for consistency: “Although the cellular mechanisms of primary and secondary sprouting in zebrafish appear very similar, with tip cell selection and guided migration and stalk cell proliferation, secondary sprouting utilises alternative signalling pathways and entails a unique specification step that establishes both venous ISVs and lymphatic structures.” (see page 15)

-The authors refer the increased cell division phenotypes observed in the movies, however, the movie files have not been available to the reviewers.

We will provide the movies.

Reviewer #2 (Significance (Required)):

This is an important study as uncovering the mechanistic details of angiogenic and lymphangiogenic negative regulators is of high value with the potential for therapeutic developments. To date, Vash-1 has been only studied in the context of tumour angiogenesis, vasculature in diabetic nephropathy and pulmonary arterial hypertension, and it remains unclear what is its role during development and how does it regulate vascular network formation. The tyrosination status of microtubule in endothelial cells is understudied. This study revealed, previously uncharacterised detyrosinated microtubules in endothelial cells in vivo. And further dissects how this process might be regulated, brings unique insights into the vascular biology field and beyond. Thus, delving into the cell biological mechanism such as microtubule dynamics and modification in vivo in embryo context is a significant step forward in setting new standards in the field.

I am developmental biologist who has experience in model organisms such as zebrafish and mouse. The main focus of my work is on developmental angiogenesis and lymphangiogenesis.

REFEREES CROSS-COMMENTING

After reading the other reviews comments, it seems that we all agree that this study is of high value to vascular biology field and beyond bringing novel findings.

Importantly the reviewers' comments are in line with each other and have identified several commonalities that should be addressed. Such as: Further validation of Morpholinos, or using alternative methods to replicate the findings. additional evidence that the observed phenotypes are primary due to vash-1 requirement within EC, and not due to the secondary effect in other cells such as CXCR4/SDF1 system and SVEP1, neurons or general delay of the embryos Further evidence of for VASH expression pattern the number of embryos used in the experiments, and how the data is represented.

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

Vasohibin-1 (Vash-1) is known to detyrosinate microtubules (MTs) and limit angiogenesis. Using in vivo live imaging and whole mount immunofluorescence staining of zebrafish trunk vasculature, Bastos de Oliveira et al. show that the MT detyrosination role of Vash-1 is conserved in zebrafish and that Vash-1 is essential for limiting venous sprouting and subsequent formation of lymphatics. Their findings suggest a role for MT detyrosination in lympho-venous cell specification.

**Major comments:**

1 . The authors claim that Vash-1 regulates secondary sprouting and lymphangiogenesis by detyrosinating MTs. However, no direct evidence of this link is provided in the manuscript. The authors only separately show that knockdown of vash-1 affects MT detyrosination and secondary sprouting and lymphangiogenesis. They have not shown a causative effect. The authors should therefore qualify the above stated claim as speculative. In other words, the authors should mention that their data only suggests that disruption of MT detyrosination is the underlying cause for aberrant secondary sprouting and lymphangiogenesis in vash-1 KD embryos.

We agree with the reviewer about the lack of evidence to state that the disruption of microtubule detyrosination leads to aberrant secondary sprouting. Although we believe this is the most parsimonius explanation for the secondary sprouts behavioural defects as cell division is disturbed and microtubule detyrosination is implicated in cell division (Barisic et al., 2015), we want to make clear that our data currently only suggest a specific role of microtubule detyrosination in secondary sprouting. Examples of this are page 14 of the discussion „These results suggest that Vash-1-driven microtubule detyrosination limits excessive venous EC sprouting and proliferation during lympho-venous development in zebrafish.” as well as the abstract.

We also corrected the sentence in the discussion (page 14): “In this study, we identified Vash-1-mediated microtubule detyrosination as a cellular mechanism as a novel regulator of EC sprouting from the PCV and the subsequent formation of lymphatic vessels in the zebrafish trunk.”

To avoid any overstatement, we also propose the following title change: Vasohibin-1 mediated tubulin detyrosination selectively regulates secondary sprouting and lymphangiogenesis in the zebrafish trunk.

As detailed in response to comment 2 below, we will however attempt to investigate the direct connection. Depending on the outcome, we will adapt conclusions and title accordingly.

2 . In order to provide more compelling evidence for a direct relationship between MT tyrosination and lymphangiogenesis, the authors could try mutating the carboxypeptidase domain of vash-1 or overexpressing a dominant negative transcript (that contains a mutated carboxypeptidase domain). If this gives the same phenotypes as the vash-1 morphants, it would indicate that the carboxypeptidase activity of Vash-1 (in detyrosinating MTs) is responsible for limiting secondary sprouting and promoting specification of lymphatics. This suggested experiment is fairly realistic in terms of both time and resources. For example, since the authors already have the human vash-1 cDNA cloned, making a dominant negative transcript from this would take around two weeks, imaging and analysis of embryos injected with this mRNA would take another four weeks. Therefore, in total, the suggested experiment would take around 6 weeks. Although the alternative experiment, that is, making a carboxypeptidase domain mutant of vash-1 would be a better choice in terms of reproducibility and long-term use of a stable line, it would admittedly take a relatively larger amount of time. Therefore, the ultimate choice would depend on the authors.

We will investigate this further by cloning and expressing a mutated vash-1 cDNA which translates a validated catalytically dead Vash-1 (Nieuwenhuis et al., 2017). However, this mutant has not been shown to function as dominant negative, so it is unclear whether it can be used as a dominant negative mutant.

3 . Both the data and methods are presented in a way that ensures reproducibility. The statistical analysis is very well done, in that the authors were very prudent in their choice of statistical tests. However, in many figures and subfigures (Fig. 2B, H-J; Fig. 3G, J, K, N; Fig. 4J; Fig. 5J), the number of replicates was not mentioned and instead only the sample size was stated. Whether this was just an oversight or if it should be taken to mean that the analysis was performed on just one replicate is unclear. The authors need to clarify this aspect of their analysis. Further, In Fig. 2H-J, Fig. 3G,J, K, N and Fig. 4J, the total number of data points in control MO vs vash-1 KD seem to be quite different. In other words, there seem to be a lot more data points in one experimental condition than the other. Does this difference fall within the acceptable range? If the authors were to compare a similar number of data points between the two experimental conditions, would the results of the statistical analysis still be the same?

We apreciate this comment and clarified the replicate numbers in the figure legends: Fig. 2B- 3 replicates (page 25), Fig. 2 H-J- quantification is 1 replicate (page 26), Fig. 2 D-G is representative of 3 replicates (page 25). Fig. 3 G,J,K,N – quantification is from 1 replicate (page 26), Fig. 3 B,C,E,F,H,I are representative of 2 experimental replicates (page 26). Fig. 4J – quantification is 1 replicate (page 27), Fig. 4 A-F is representative of 3 replicates (page 27). Fig. 5 J correspondes to 1 replicate (page 28).

We plan to increase replicates and numbers in quantifications shown in Fig. 3 G,J,K,N and Fig. 5 J as they are relevant for the conclusions of the manuscript, and adapt the text.

The quantifications of immunostaining signals are comparable between different samples of the same experiment but technically not easy accross different experiments, due to some variability of the immunostaining. However, the pattern we report in the quantifications and representative pictures is consistentely detected (reduced dTyr signal upon vash-1 KD in Fig 2 D-G; higher dTyr intensity in secondary rather than primary sprouts in Fig. 4 A-F). We added in the legend that the pictures of the embryos in these figures are representative of 3 biological replicates (see page 25 and 27).

We recognise the unequal sample size in control and vash-1 KD groups in Fig. 2H-J, Fig. 3G,J, K, N and Fig. 4J. Generally, the vash-1 KD group shows more variance than the control group (see Fig. 3 J-N, 4J for example), hence the reason why we analysed a higher sample size.

In the planned experiments (repeating quantifications of Fig. 3 J-N), we will analyse a similar number of embryos.

We corrected the figure legend of 2 H-J on the number of ISVs - 108 ISVs from 7 embryos for control and 150 ISVs for vash-1 KD, from 9 embryos (see page 26).

4 . The authors only provide KD data on the function of vash-1 using morpholinos. According to several recent guidelines concerning the use of morpholinos, this is not widely accepted in the zebrafish community as sufficient to provide robust insight into gene function. Please refer for example to the following publication: Guidelines for morpholino use in zebrafish, Stainier et al., PLOS Genetics, 2017. The generation of a vash-1 mutant is a necessary requirement for backing up morpholino KD data. Further, even though the authors state that embryos were selected on the pre-established criteria that they have normal morphology, beating heart, and flowing blood, certain morphological differences between control MO injected and vash-1 KD embryos could be observed in some figures. In Fig. 2D, F and Fig. 5A, B, E, F the vash-1 KD embryos seem smaller (extend of the dorso-ventral axis) than control MO injected embryos. The authors need to provide images showing the overall morphology of morpholino injected embryos and need to provide evidence that morpholino injections do not cause developmental delays.

We agree that a mutant would be desirable to validate the phenotypic analysis of the morpholinos used, and would also allow for further analysis. However, this is not achievable within a reasonnable time frame, especially in the context of current work restrictions. We have added a sentence about the need to confirm the loss of function phenotype with vash-1 mutants in the discussion (see page 14).

In addtion to the two morpholinos currently used to knockdown vash-1 expression, we will use an ATG morpholino to further investigate our observations and hypothesis regarding the role of vash-1 in lymphatic vessels formation. We will also validate it by westernblot and attempt to rescue it with mRNA.

We added a supplementary figure with pictures and quantifications of antero-posterior (Sup. Figure 1 C) and dorso-ventral length (Sup. Figure 1 D) of the analysed control and vash-1 morpholino injected embryos‘ development at 24, 34, 52 and 4dpf which shows no significant developmental delay and morphological defect. There is some occurrence of curvature of the tail at 34-52 hpf.

We added a sentence in the Methods section (pages 10) to clarify the morphant’s morphology and dosage-response curves.

We observe a 1-2 hour developmental delay of both the control and the vash-1 KD embryos compared to uninjected wild-type embryos, which led us to chose the 52 hpf time point to investigate the PLs. In uninjected embryos they are usually developed by 48hpf (Hogan et al., 2009).

Fig. 2 D shows a more anterior region of the zebrafish trunk than Fig. 2F (the tail has a smaller dorso-ventral length)- we will provide more comparable pictures from the same region.

Fig. 5B is slightly tilted – we will provide a picture with the same orientation.

Fig. 5 E and F have a similar length from dorsal aorta to the dorsal longitudinal anastomotic vessel. However, we appreciate a difference in the sub intestinal vascular plexus (SIVP), which is consistently underdeveloped in the vash-1 KD embryos.

Figure 2- vash-1 deficient embryos show underdeveloped intestinal vascular system at 4 dpf.

**Minor comments:**

a. The authors should back their qPCR data for vash-1 expression (Figure 1) by standard mRNA in situ hybridization, given the large degree of variability in vash-1 expression. Do they observe a dynamic expression in the vasculature using this technique?

We agree with the reviewer that an in situ hybridization would be beneficial to understand the expression pattern of vash-1 in wild type embryos. Accordingly, we will look at vash-1 expression by in situ hybridization in WT embryos.

The number of nuclei per sprout in Fig. 3J does not correspond with the number of divisions per sprout presented in Fig. 3K. The authors observe one or two cell divisions per sprout in ctr MO injected embryos (Fig. 3K), however, Fig. 3J shows that the majority of ctr. sprouts contains only one cell. This is even more dramatic for vash-1 MO injected embryos, which can have up to four divisions, therefore should contain six cells. However, the maximum number of cells the authors report is three to four cells. How do these observations go together?

We believe these quantifications are not contradicting. The number of endothelial nuclei was assessed just prior to the connection to the ISV and the cell division quantification was done in a time-lapse from the time of secondary sprout emergence until the resolution of the 3-way connection. It is expected that there are more cell divisions during a longer time frame, as cells migrate dorsally or ventrally out of the sprout.

Fig. 5I and J have the same data points for control MO and vash-1 MO1. Does this mean that both graphs are from the same experiment? If so, the authors could combine the two graphs into one. If the two graphs are not from the same experiment, both would need to have independent controls.

Fig 5 I and J are indeed from the same experiment. They are now combined into one graph (see Fig. 5 J).

d. The percentage of somites with PLs in vash-1 MO1 injected embryos in Fig. 5I is half the value shown in Fig. 5C. Although this kind of variability might be expected in biological samples, perhaps the authors could briefly discuss the issue and its implications on reproducibility in the manuscript so as to have the readers be aware of it, especially since the rescue of the vash-1 morpholino phenotype back to 50% from 25% is the same value the authors observed in the vash-1 KD alone in Fig. 5C. Here the value is 50% for the morpholino injection.

We added a sentence discussing the phenotypic variability in the discussion (see page 16), and we added a dosage response curve for the PLs (Sup. Figure 1 F), showing that embryos injected with the same amount of morpholino show variability in the percentage of somites with PLs at 52hpf. We added a more representative picture of PLs for vash-1 morphant in Fig. 5I ( Y-axis of Fig. 2H and 4J correspond to ratios, which have no units. Nontheless, we added AU/AU to these graphs to make it clearer. We added the bars in Fig. 5D.

It would help to have an inference or conclusion at the end of each results section.

We added one conclusion sentence per results section (see pages 11-14).

Reviewer #3 (Significance (Required)):

Conceptual: As per my knowledge, this is the first study that looks at microtubule modifications in the context of a vertebrate organism past the gastrulation stage, as opposed to similar studies that have been done in cell culture or invertebrates (S. cerevisiae, C. elegans and D. melanogaster). Moreover, this study is one of few that address a novel link between the cytoskeleton and the process of cell fate specification.

Previous studies have separately shown that Vash-1 limits angiogenesis and detyrosinates MTs. The current study combines the two observations in the context of endothelial cells, and hypothesizes that perhaps the function of Vash-1 in limiting angiogenesis and at the same time promoting lymphatic development could be due to its role in MT modification at the molecular level and the consequent effect of this on cell division and/or fate specification at the cellular level. In short, this study aims to connect the long-standing gap in knowledge between cytoskeletal modifications and cell dynamics (in particular, division and specification) in a vertebrate organism. I therefore believe that the current study would be an exciting finding for research communities that study cytoskeletal influence on cellular dynamics and also those in the broad area of vascular biology.

My field of expertise relates to vascular biology, specifically developmental angiogenesis and the behavior of endothelial cells in zebrafish.

References

Barisic, M., Silva E Sousa, R., Tripathy, S. K., Magiera, M. M., Zaytsev, A. V., Pereira, A. L., Janke, C., Grishchuk, E. L., & Maiato, H. (2015). Microtubule detyrosination guides chromosomes during mitosis. Science, 348(6236), 799–803. https://doi.org/10.1126/science.aaa5175

Hogan, B. M., Bos, F. L., Bussmann, J., Witte, M., Chi, N. C., Duckers, H. J., & Schulte-Merker, S. (2009). Ccbe1 is required for embryonic lymphangiogenesis and venous sprouting. Nature Genetics, 41(4), 396–398. https://doi.org/10.1038/ng.321

Isogai, S, Horiguchi, M., & Weinstein, B. M. (2001). The vascular anatomy of the developing zebrafish: an atlas of embryonic and early larval development. Developmental Biology, 230(2), 278–301. https://doi.org/10.1006/dbio.2000.9995

Isogai, Sumio, Lawson, N. D., Torrealday, S., Horiguchi, M., & Weinstein, B. M. (2003). Angiogenic network formation in the developing vertebrate trunk. Development, 130(21), 5281–5290. https://doi.org/10.1242/dev.00733

Kimura, H., Miyashita, H., Suzuki, Y., Kobayashi, M., Watanabe, K., Sonoda, H., Ohta, H., Fujiwara, T., Shimosegawa, T., & Sato, Y. (2009). Distinctive localization and opposed roles of vasohibin-1 and vasohibin-2 in the regulation of angiogenesis. Blood, 113(19), 4810–4818. https://doi.org/10.1182/blood-2008-07-170316

Koltowska, K., Lagendijk, A. K., Pichol-Thievend, C., Fischer, J. C., Francois, M., Ober, E. A., Yap, A. S., & Hogan, B. M. (2015). Vegfc Regulates Bipotential Precursor Division and Prox1 Expression to Promote Lymphatic Identity in Zebrafish. Cell Reports, 13(9), 1828–1841. https://doi.org/10.1016/j.celrep.2015.10.055

Liao, S., Rajendraprasad, G., Wang, N., Eibes, S., Gao, J., Yu, H., Wu, G., Tu, X., Huang, H., Barisic, M., & Xu, C. (2019). Molecular basis of vasohibins-mediated detyrosination and its impact on spindle function and mitosis. Cell Research, June. https://doi.org/10.1038/s41422-019-0187-y

Lim, A. H., Suli, A., Yaniv, K., Weinstein, B., Li, D. Y., & Chien, C. Bin. (2011). Motoneurons are essential for vascular pathfinding. Development, 138(21), 4813. https://doi.org/10.1242/dev.075044

Nicenboim, J., Malkinson, G., Lupo, T., Asaf, L., Sela, Y., Mayseless, O., Gibbs-Bar, L., Senderovich, N., Hashimshony, T., Shin, M., Jerafi-Vider, A., Avraham-Davidi, I., Krupalnik, V., Hofi, R., Almog, G., Astin, J. W., Golani, O., Ben-Dor, S., Crosier, P. S., … Yaniv, K. (2015). Lymphatic vessels arise from specialized angioblasts within a venous niche. Nature, 522(7554), 56–61. https://doi.org/10.1038/nature14425

Nieuwenhuis, J., Adamopoulos, A., Bleijerveld, O. B., Mazouzi, A., Stickel, E., Celie, P., Altelaar, M., Knipscheer, P., Perrakis, A., Blomen, V. A., & Brummelkamp, T. R. (2017). Vasohibins encode tubulin detyrosinating activity. Science, 358(6369), 1453–1456. https://doi.org/10.1126/science.aao5676

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Referee #3

Evidence, reproducibility and clarity

Vasohibin-1 (Vash-1) is known to detyrosinate microtubules (MTs) and limit angiogenesis. Using in vivo live imaging and whole mount immunofluorescence staining of zebrafish trunk vasculature, Bastos de Oliveira et al. show that the MT detyrosination role of Vash-1 is conserved in zebrafish and that Vash-1 is essential for limiting venous sprouting and subsequent formation of lymphatics. Their findings suggest a role for MT detyrosination in lympho-venous cell specification.

Major comments:

1 . The authors claim that Vash-1 regulates secondary sprouting and lymphangiogenesis by detyrosinating MTs. However, no direct evidence of this link is provided in the manuscript. The authors only separately show that knockdown of vash-1 affects MT detyrosination and secondary sprouting and lymphangiogenesis. They have not shown a causative effect. The authors should therefore qualify the above stated claim as speculative. In other words, the authors should mention that their data only suggests that disruption of MT detyrosination is the underlying cause for aberrant secondary sprouting and lymphangiogenesis in vash-1 KD embryos.

2 . In order to provide more compelling evidence for a direct relationship between MT tyrosination and lymphangiogenesis, the authors could try mutating the carboxypeptidase domain of vash-1 or overexpressing a dominant negative transcript (that contains a mutated carboxypeptidase domain). If this gives the same phenotypes as the vash-1 morphants, it would indicate that the carboxypeptidase activity of Vash-1 (in detyrosinating MTs) is responsible for limiting secondary sprouting and promoting specification of lymphatics. This suggested experiment is fairly realistic in terms of both time and resources. For example, since the authors already have the human vash-1 cDNA cloned, making a dominant negative transcript from this would take around two weeks, imaging and analysis of embryos injected with this mRNA would take another four weeks. Therefore, in total, the suggested experiment would take around 6 weeks. Although the alternative experiment, that is, making a carboxypeptidase domain mutant of vash-1 would be a better choice in terms of reproducibility and long-term use of a stable line, it would admittedly take a relatively larger amount of time. Therefore, the ultimate choice would depend on the authors.

3 . Both the data and methods are presented in a way that ensures reproducibility. The statistical analysis is very well done, in that the authors were very prudent in their choice of statistical tests. However, in many figures and subfigures (Fig. 2B, H-J; Fig. 3G, J, K, N; Fig. 4J; Fig. 5J), the number of replicates was not mentioned and instead only the sample size was stated. Whether this was just an oversight or if it should be taken to mean that the analysis was performed on just one replicate is unclear. The authors need to clarify this aspect of their analysis. Further, In Fig. 2H-J, Fig. 3G,J, K, N and Fig. 4J, the total number of data points in control MO vs vash-1 KD seem to be quite different. In other words, there seem to be a lot more data points in one experimental condition than the other. Does this difference fall within the acceptable range? If the authors were to compare a similar number of data points between the two experimental conditions, would the results of the statistical analysis still be the same?

4 . The authors only provide KD data on the function of vash-1 using morpholinos. According to several recent guidelines concerning the use of morpholinos, this is not widely accepted in the zebrafish community as sufficient to provide robust insight into gene function. Please refer for example to the following publication: Guidelines for morpholino use in zebrafish, Stainier et al., PLOS Genetics, 2017. The generation of a vash-1 mutant is a necessary requirement for backing up morpholino KD data. Further, even though the authors state that embryos were selected on the pre-established criteria that they have normal morphology, beating heart, and flowing blood, certain morphological differences between control MO injected and vash-1 KD embryos could be observed in some figures. In Fig. 2D, F and Fig. 5A, B, E, F the vash-1 KD embryos seem smaller (extend of the dorso-ventral axis) than control MO injected embryos. The authors need to provide images showing the overall morphology of morpholino injected embryos and need to provide evidence that morpholino injections do not cause developmental delays.

Minor comments:

a. The authors should back their qPCR data for vash-1 expression (Figure 1) by standard mRNA in situ hybridization, given the large degree of variability in vash-1 expression. Do they observe a dynamic expression in the vasculature using this technique?

b. The number of nuclei per sprout in Fig. 3J does not correspond with the number of divisions per sprout presented in Fig. 3K. The authors observe one or two cell divisions per sprout in ctr MO injected embryos (Fig. 3K), however, Fig. 3J shows that the majority of ctr. sprouts contains only one cell. This is even more dramatic for vash-1 MO injected embryos, which can have up to four divisions, therefore should contain six cells. However, the maximum number of cells the authors report is three to four cells. How do these observations go together?

c. Fig. 5I and J have the same data points for control MO and vash-1 MO1. Does this mean that both graphs are from the same experiment? If so, the authors could combine the two graphs into one. If the two graphs are not from the same experiment, both would need to have independent controls.

d. The percentage of somites with PLs in vash-1 MO1 injected embryos in Fig. 5I is half the value shown in Fig. 5C. Although this kind of variability might be expected in biological samples, perhaps the authors could briefly discuss the issue and its implications on reproducibility in the manuscript so as to have the readers be aware of it, especially since the rescue of the vash-1 morpholino phenotype back to 50% from 25% is the same value the authors observed in the vash-1 KD alone in Fig. 5C. Here the value is 50% for the morpholino injection.

e. The Y-axis label is missing in Fig. 2H and Fig. 4J. Figure 5D lacks bars showing median and standard deviation.

f. It would help to have an inference or conclusion at the end of each results section.

Significance

Conceptual: As per my knowledge, this is the first study that looks at microtubule modifications in the context of a vertebrate organism past the gastrulation stage, as opposed to similar studies that have been done in cell culture or invertebrates (S. cerevisiae, C. elegans and D. melanogaster). Moreover, this study is one of few that address a novel link between the cytoskeleton and the process of cell fate specification.

Previous studies have separately shown that Vash-1 limits angiogenesis and detyrosinates MTs. The current study combines the two observations in the context of endothelial cells, and hypothesizes that perhaps the function of Vash-1 in limiting angiogenesis and at the same time promoting lymphatic development could be due to its role in MT modification at the molecular level and the consequent effect of this on cell division and/or fate specification at the cellular level. In short, this study aims to connect the long-standing gap in knowledge between cytoskeletal modifications and cell dynamics (in particular, division and specification) in a vertebrate organism. I therefore believe that the current study would be an exciting finding for research communities that study cytoskeletal influence on cellular dynamics and also those in the broad area of vascular biology.

My field of expertise relates to vascular biology, specifically developmental angiogenesis and the behavior of endothelial cells in zebrafish.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The manuscript by Bastos de Oliveira et al. describes an important investigation of the endothelial tubulin detyrosination during vascular development. Namely, they found detyronised microtubules in secondary sprouts, which is absent in MO-vash-1 treated embryos. The authors use the vash-1 morpholino approach to uncover the developmental consequences of suppressed detyrosination in angiogenesis and lymphangiogenesis in vivo in zebrafish. By a combination of transgenic lines, immunohistochemistry and time-lapse imaging, Bastos de Oliveira et al., have found that Vash-1 is a negative regulator of secondary sprouting in zebrafish. The authors showed that in the absence of Vash-1 more cells are present in the secondary sprouts due to increased cell proliferation; however lymphatic vascular network fails to form. The current manuscript requires additional experimental evidence to support the conclusions. Please see below the major technical concerns and minor comments.

Major comments:

-This study is based on analysis of the phenotypes observed in embryos injected with vash-1 morpholino. The authors use two different types of splice morpholinos, perform rescue experiments with RNA, and validate one MO-vash-1 with western blot. Morpholinos are not trivial to work with, and the results are variable hence additional controls need to be included, as following the recommendation put together by the zebrafish community (Stainier et, al., Plos Genetics, 2017). As the severity of the phenotypes comparing MO1 with MO2 is different and MO-vash-1 embryos appear developmentally delayed (Figure 2D-F and 5E-F overall size seem to be affected), additional MO is required, for example, ATG-MO or generation of CRISPR mutant would be favourable. All the morpholino used need to be validated using an antibody, RT-PCR and qPCR. It is essential to carry out the rescue experiments for all the MO used in this study and following the guidelines. Including the dose-response curve, data would be informative.

-In addition to EC, the levels of dTyr are lower in MO-vash-1 in neural tube and neurons spanning the trunk (Figrue 2 D-G'). These have been previously shown to be important for secondary sprouting. Is it possible that the observed phenotypes in the secondary sprouting are due to defects in these neurons?

-Embryo number used in this study appears to be low especially in figure 3G, 5D, 5G, to conclude draw conclusions from these experiments, the number of embryos used should be higher than 20. Figure 4J please specify how many embryos were used.

-The authors hypothesise that VASH acts in the sprouting endothelial cells, based on the Q-PCR in Figure 1. However, in this experiment all EC have been sorted thus this remains ambiguous in which cell types vash-1 is expressed. Please provide the expression pattern for vash-1 across the developmental stages the phenotypes are observed.

-Throughout the manuscript the authors refer the lymphatic identity, however, there is no evidence in the paper that the identity status has been assessed. To support these claims Prox1 immunohistochemistry or analysis of prox1 expression in the reporter line would be appropriate.

Minor comments:

-The authors refer to the literature where overexpression of VASH suppresses the angiogenesis. As the RNA injections were used in rescue experiments, the data of vash-1 RNA injections into the wild-type embryos would be beneficial.

-In figures 2J, 3J, 3K, 3N, 4J, 5C, 5D and 5G the N number was set for examples as the number of sprouts, the number of somites with TD, number of ISV. To strengthen the observation in the manuscript quantification of the sprouts, PL, vISVs and lymphatic phenotypes with N set as the number of embryos would be more informative. Indicating the number of embryos used, in the graphs, would be helpful.

-In Figure 5A, B and D the authors quantify what they refer to as a lumenised connection between the vISVs and PL. In the control image (second star), a somewhat lumenised structure is present, clarification of how the scores were set is missing.

-In Figure 3 E and F the authors show the excessive sprouting phenotype between controls and Mo-vash-1. The images presented are taking from different parts of the embryos (middle of the trunk vs plexus region), hampering the comparison between the two groups. The quantification of the phenotypes in both experimental groups should be in the same region of the embryo, as the local difference can occur. It is key to provide representative images to support these observations.

-Figure 1D the vash-1 expression levels in EC seem very variable in this graph, therefore no conclusion can be drawn from this data, especially as the authors do not provide the p-values.

-In the introduction, the authors state: 'Although primary and secondary sprouts appear morphologically similar, with tip and stalk cells' - Please provide the reference that supports the claim that secondary sprouts have tip-stalk cells morphology/organisation.

-The authors refer the increased cell division phenotypes observed in the movies, however, the movie files have not been available to the reviewers.

Significance

This is an important study as uncovering the mechanistic details of angiogenic and lymphangiogenic negative regulators is of high value with the potential for therapeutic developments. To date, Vash-1 has been only studied in the context of tumour angiogenesis, vasculature in diabetic nephropathy and pulmonary arterial hypertension, and it remains unclear what is its role during development and how does it regulate vascular network formation. The tyrosination status of microtubule in endothelial cells is understudied. This study revealed, previously uncharacterised detyrosinated microtubules in endothelial cells in vivo. And further dissects how this process might be regulated, brings unique insights into the vascular biology field and beyond. Thus, delving into the cell biological mechanism such as microtubule dynamics and modification in vivo in embryo context is a significant step forward in setting new standards in the field.

I am developmental biologist who has experience in model organisms such as zebrafish and mouse. The main focus of my work is on developmental angiogenesis and lymphangiogenesis.

REFEREES CROSS-COMMENTING

After reading the other reviews comments, it seems that we all agree that this study is of high value to vascular biology field and beyond bringing novel findings.

Importantly the reviewers' comments are in line with each other and have identified several commonalities that should be addressed. Such as: Further validation of Morpholinos, or using alternative methods to replicate the findings. additional evidence that the observed phenotypes are primary due to vash-1 requirement within EC, and not due to the secondary effect in other cells such as CXCR4/SDF1 system and SVEP1, neurons or general delay of the embryos Further evidence of for VASH expression pattern the number of embryos used in the experiments, and how the data is represented.

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Referee #1

Evidence, reproducibility and clarity

The manuscript entitled "Vasohibin-1 mediated tubulin detyrosination selectively regulates secondary sprouting and lymphangiogenesis in the zebrafish trunk" by de Oliveira investigates the function of the carboxylpeptidase Vasohibin during the formation of the zebrafish trunk vasculature and reports a requirement of Vasohibin for secondary sprout formation and in particular the formation the lymphatic vasculature.

Having established the expression of Vasohibin in sorted ECs of 24 hpf embryos, the remaining study addresses the function of Vasohibin in this cell type. It is largely based on the use of a splice-site interfering morpholino. Particular commendable is the analysis, demonstrating that the KD of vash-1 indeed results in a significant reduction of detyrosination in endothelial tubulin. Findings in the vascular system then include: (i) the detection of increased division and hence supernumerous cells occurring selectively in 2nd sprouts from the PCV; (ii) an increased persistence of the initially formed 3 way connections with ISV and artery; (iii) reduced formation of parachordal lymphangioblasts and (iv) a reduced number of somites with a thoracic duct segment; (v) frequent formation of lumenized connections between PLs (where present) and ISV. To demonstrate specificity, the approach was repeated with a different morpholino and defects were partially rescued by MO-insensitive RNA.

Possible additional and relevant information could include data on a vash-1 promotor mutant to independently verify the MO-based functional analysis. Mutants would also allow analysis of further development, are the defects leading to the demise of the fish or is a later regeneration and normalization of the lymphatic vasculature observed? In addition, are other lymphatic vessel beds like the cranial lymphatics affected? PLs have been demonstrated to be at least partially guided in their movement by the CXCR4/SDF1 system and SVEP1. Has the expression of these factors been tested in vash-1 KDs? With regards to the frequently observed connections of PLs and ISVs in vash-1 morphants, can the proposed lumen formation of these shunts be demonstrated e.g. by injection of Q-dots or microbeads into the circulation? Concerning the mechanisms of these defects, is it possible to analyse the asymmetric cell division leading to 2nd sprouts in greater detail? Is the same number or are more cells sprouting form PCV and can the fli1ep:EGFP-DCX cell line in fixed samples be used to identify the spindle orientation in dividing cells?

Minor issues: Page 5, Mat & Meth, please spell out PTU at its first mention.

Page 6 Mat & Meth, Secondary sprout and 3-way connection parameters: The number of nuclei was assessed in each secondary sprouts (del s, singular) just prior...

Page 16, 8th line from bottom: Recent work demonstrated that a secondary sprout either contributes (add s) to remodelling a pre-existing ISV into a vein, or forms (add s)a PLs (Geudens et al., 2019).

Page 25, Legend to Fig. 2D-G: "...G,G' shows quantification of dTyr signal upon vash-1 KD..." Fig2 G,G' show immunostaining rather than quantification of the dTyr signal, which is shown Fig. 2H-J

Fig. 1D / Fig. 2H-J please increase weight of the error intervals and / or change colour for improved visibility

Significance

Taken together the manuscript is comprehensively written and the study provides a conclusive analysis of the MO-mediated KD of Vasohibin in zebrafish embryonic development presenting significant novel findings. Known was a generally inhibitory function of Vasohibin on vessel formation and its enzymatic activity as a carboxylpeptidase responsible for tubulin detyrosination, affecting spindle function and mitosis. New is the detailed analysis of the Vasohibin KD on zebrafish trunk vessel formation and the description of a selective impairment of 2nd sprout formation. The manuscript is of interest for vascular biologists.

REFEREES CROSS-COMMENTING

I fully concur with the comments of reviewer #2, all three reviews find that this study is of significant interest to the vascular biology community as the relevance of tubulin detyrosination for developmental angiogenesis has not been investigated. Also all three reviews highlight the potential limitations of the use of splice morpholinos (suggested alternatives include ATG morpholinos and CRIPR mutants), the requirement to provide further evidence for a endothelial cell autonomous defect and the need to clarify some of the data representation.

Reviewer #3:

Kim et al. studied the roles of GATA1 binding and H3K27ac on chromatin interactions associated with binding of the architectural factor CTCF. The authors focused on a TAD and sub-TAD surrounding the human beta-globin locus. The sub-TAD that is flanked by tissue-invariant CTCF sites that form contacts with each other only in erythroid cells. Loss of GATA1 binding at the beta-globin enhancer (LCR) and perturbation of H3K27ac affects some CTCF associated contacts, both involving the sub-TAD as well as the (tissue-invariant) TAD boundaries.

The mechanisms by which tissue specific contacts are established are of great interest in the field. However, while this report provides some correlative data to support a link between H3K27ac and CTCF contacts, the study in its current form is too preliminary and failed to address alternative explanations.

1) A major concern for this study: the MEL/chr11 cell line might not be a suitable model system. The CTCF/Rad21 binding profiles in the MEL/chr11 seem quite different from normal human erythroid cells. Specifically, the signals of CTCF binding at C4, C5 and C6 are almost at the baseline (Fig2A/B and Fig3D/E) in MEL/chr11. However, those sites should have comparable CTCF binding strength with C3 and C7, (e.g. Fig2E). The diminished CTCF binding at the C4-C6 sites might affect the sub-TAD structures in MEL/chr11 cells.

2) Loss of GATA1 binding at HS2 or HS3 affects GATA1 binding at other sites as well. It is also possible that loss of GATA1 binding impairs binding by other nuclear factors that might be involved in sub-TAD formation. The same holds for histone modifications other than H3K27ac. This should be discussed.

3) Fig.2: the correlation between H3K27ac and CTCF contacts does not hold at all examined sites. For example, H3K27ac is reduced also at C7 and C3 that maintain contacts. Same in Fig.3 where increases in H3K27ac is also increased near CTCF sites whose contacts don't increase.

4) Fig.2: total H3 is reduced at C5 to the same extent as asH3. How was H3K27ac normalized?

5) Why were p300 inhibition experiments done in K562 cells? In Fig2E and Fig4D it seems that the H3K27ac signals are not concordant between MEL/chr11 and K562 cells. For example, in Fig2E, the H3K27ac at C3 site is very strong in the MEL/chr11; However, in Fig4D, the H3k27ac signal at C3 site is near baseline. The H3K27ac signals also suggest that the MEL/chr11 cell line is different from normal human erythroid cells and also the leukemia cell line K562. The different H3K27ac profiles at CTCF binding sites confound the interpretation.

6) Fig1E, the interactions between HS5-3'HS1 (C4-C5) were not significantly changed in the HS3/HS2 mutated MEL/chr11 cells. Actually this well known interaction between HS5-3'HS1 was not even detected by 3C in the WT control MEL/chr11 cells, contrary to previous studies. Again, this suggests that the MEL/chr11 cell line is not an ideal system for this study. The reduced interactions between beta-globin and C5/HS5 could be the result of loss of GATA1 binding but not CTCF. For clarity it would be better to plot the 3C data scale to the actual genomic distance.

7) The authors should make clearer distinctions throughout whether they are considering supposedly tissue-invariant CTCF contacts near the TAD boundaries or the tissue-specific sub-TAD. It appears that both can change upon their perturbations.

8) Data mining: "acetylation level was decreased remarkably in the boundaries of longer interactions (over than 100 Kb)" why is this remarkable? How does contact distance inform the role of H3K27ac? What is the correlation genome wide between H3K27ac and CTCF ChIA PET? This could be done using data sets from a variety of cell types.

9) Fig.6A: GATA1 knock down seems to affect H3K27 broadly and not any more extensively (or even less) at CTCF sites.

Reviewer #2:

The authors analyzed long and short range chromatin interactions in erythroid cell lines after perturbation of globin associated enhancers, histone acetylation, GATA1 expression, or CBP/p300 expression. The data show that CTCF binding sites are associated with high levels of H3K27 acetylation in the context of short range interactions. Deletion of GATA1 binding sites in the human LCR in hypersensitive sites 2 or 3 caused a reduction in H3K27ac at nearby CTCF sites and impaired the interaction of those sites, without interfering with the binding of CTCF or the cohesin subunit Rad21. Treatment of cells with TSA or inhibition of CBP/p300 or GATA1 expression had a similar effect.

The manuscript provides interesting and novel observations with respect to GATA1 binding and H3K27ac at nearby CTCF sites. However, the mechanism(s) by which GATA1 modulates H3K27ac levels at CTCF sites remain(s) unknown.

Specific comments.

1) One possible interpretation of the results, which has not been addressed by the authors, is that the reduction in histone acetylation levels may modulate the stiffness of chromatin, which may particularly affect short-range interactions.

2) Figure 3: TSA treatment also affects other histone acetylation events. This should be mentioned. Furthermore, the data in Figure 3D are not consistent with data in Figure 1E with respect to the control cells. In Figure 1E it is shown that the anchor C5 interacts with beta and C6, Figure 3C shows no interactions between these elements.

3) Figure 4: There is no description of how the CBP/p300 depleted cells were generated. Was this a single shRNA? If so, it would be important to repeat the experiment using a second shRNA targeting a different region of the RNA to avoid off-target effects. Furthermore, it would be important to show the CBP/p300 binding pattern across the globin locus and the CTCF sites. Does H3K27ac at the CTCF sites correlate with CBP/p300 binding? These data should be available from K562 cells.

4) Figure 6: there is no description of how the GATA1 depleted cells were generated. Again, was this a single shRNA?

Reviewer #1:

In this study, Kim et al described the GATA1-dependent histone H3K27ac on a subset of CTCF binding sites and CTCF-mediated chromatin interactions in erythroid cells. The authors generated a GATA1 binding site deletion in MEL cells and observed impaired CTCF-mediated interactions around the beta-globin gene cluster. They further modulated H3K27ac by TSA treatment of CBP/p300 knockdown, and noted that altered H3K27ac affected interactions between a subset of CTCF sites. The authors further performed global correlation analysis between public ChIA-PET and H3K27ac in K562 cells with or without GATA1 depletion, and presented evidence supporting a modest effect of H3K27ac at some CTCF sites upon depletion of GATA1 in K562 cells. Based on these findings, the authors concluded that GATA1-dependent H3K27ac mediates erythroid-specific chromatin interactions between CTCF sites.

Overall, this manuscript provides molecular details of the role of GATA1-mediated transcriptional programs in regulating chromatin interactions between CTCF sites. The experiments related to GATA1 binding site mutations were well designed and executed. The authors also make use of existing public datasets to extend the analysis to global scales. However, the current study falls short in providing strong evidence to support several conclusions due to a combination of insufficient data and suboptimal data quality. The overall conclusions that GATA1 regulates chromatin interactions through H3K27ac-mediated effects do not significantly extend our current understanding based on previous studies in the authors' group (Kang et al., 2017 BBA 1860:416) and others (Hsu et al., 2017 Mol Cell 66:102). The lack of replicate experiments for several ChIP-seq studies limited the robustness of relevant conclusions.

In summary, although the current study provides additional insights into the role of GATA1-dependent transcriptional programs in regulating CTCF-mediated chromatin interactions, the overall findings were not developed in sufficient depth in light of previous studies and some conclusions were not sufficiently supported by the evidence.

Major points:

1) The authors previously showed that interactions between CTCF sites associated with sub-TADs are dependent on the binding of GATA1 to LCR enhancers (Kang et al., 2017 BBA 1860:416). In this study, the authors provided further details of the relationship between GATA1 binding, H3K27ac, and CTCF-mediated interactions. These data provide additional insights into the molecular mechanisms of GATA1-mediated effect on chromatin interactions, although they do not add significantly to previous studies from these authors and others (e.g. Hsu et al., 2017 Mol Cell 66:102).

2) To determine the effect of GATA1 binding site KO on CTCF-mediated interactions, the authors performed 3C-qPCR analysis (Fig. 1E). Given the higher resolution and ability to quantitatively contextualize the data obtained from next-gen sequencing based 3C methods, I recommend these be done in the future. Similar for the studies in Figs. 3B-E and 4E.

3) Page 5, line 115-117. It is stated that 'when it is compared to the results from knocking down GATA-1...'; however, no results from GATA-1 knockdown were included for the comparison. These studies would be helpful to determine whether the effect is directly caused by loss of GATA1 binding at the LCR enhancers.

4) It is unclear whether GATA1 site KO also affected H3K27ac signals at other CTCF-bound chromatin regions besides the b-globin gene cluster (C3 to C7). For example, in Fig. 2E, it would be helpful to include C2 and C8 regions in the ChIP-seq track as controls. Additional analyses of global changes of H3K27ac and CTCF binding also will be helpful to determine whether the effect is limited to the b-globin gene cluster.

5) In Fig. 3, to determine the effect of H3K27ac on chromatin interactions, the authors treated the cells with the HDAC inhibitor TSA. A major caveat of these studies is related to the pleiotropic effects of TSA on global H3K27ac and gene expression, thus the indirect effects on chromatin interactions due to altered gene regulation and/or erythroid maturation. This limitation should be discussed.

6) In Fig. 5, it would be important to include analyses by separating CTCF binding sites depending on whether or not they are associated with TAD boundaries. Is there correlation between the range of CTCF-mediated interactions and TAD boundary? These studies will provide a global assessment of the findings based on the beta-globin gene cluster in Figs. 1-4.

7) The effects of GATA1 knockdown on H3K27ac signals at CTCF binding sites at the global or selected regions are marginal (Fig. 6A, C,D, noting the scales of y-axis not started with 0 in Fig. 6C,D). It is unclear whether this is due to suboptimal data quality (see below) or limited effects at a global scale. These results raise questions about the extent to which the GATA1-mediated effect on H3K27ac at CTCF sites and CTCF-mediated interactions in erythroid cells.

8) There are concerns about the quality of several genomic datasets including H3K27ac ChIP-seq that may limit the robustness of relevant analyses. Specifically, the quality of H3K27ac ChIP-seq in K562 cells is suboptimal and no apparent H3K27ac enrichment is noted at the CTCF-binding sites (C3, C4, C6 and C7). Comparing Fig. 2E with Figs. 4D and 6A, the signal-to-noise ratio is highly variable in different experiments. No replicate experiment or quality control analysis was provided.

Preprint Review

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Summary

This study investigates the relationship between the binding of the transcription factor GATA-1 and histone acetylation on CTCF sites in the same genomic region. Although the reviewers find this work interesting, they raise concerns about the strength of the novel conclusions that can be drawn at this stage. Specifically, the reviewers are concerned about the strength of the data supporting a specific role of GATA1 binding in regulating CTCF-associated sub-TAD interactions (Reviewer #1 and #3), the lack of technical details on several key experiments (Reviewer #1, #2 and #3), the lack of consideration of alternative interpretations on GATA1- and/or H3K27ac-mediated chromatin regulation (Reviewer #2 and #3), and the use of MEL/chr11 cell line as the experimental model system (Reviewer #1 and #3).

Reviewer #3:

The manuscript by Sahm et al. describes the transcriptomic comparison of breeders and non-breeders in two species of mole rats from genus Fukomys. The remarkable aspect of Fukomys mole rats is that the breeders live significantly longer than workers. The authors produced new breeder couples by pairing animals from different family groups and then compared their transcriptomes to non-breeders of the same age from the original colonies.

There were very few differences identified between breeders and non-breeders. Most transcriptomic changes were confined to gonads and endocrine glands. This is somewhat unsurprising and these organs become active for breeding. The pathways that became activated were related to ribosome biogenesis, protein translation, and MYC signaling, which all reflect physiological activation of these tissues in breeders.

Interestingly, some activation of these signaling pathways was also observed in non-gonadal tissues, which contradicts the common dogma that downregulation of these pathways is associated with lifespan extension. This is a remarkable result that suggests that short-lived model organisms may not correctly reflect signaling effects required for longevity in long-lived species. The authors also point out to higher glucocorticoid levels in workers and speculate that that may be showing Cushing's like syndrome.

Overall, this is an important study of high interest.

Items to address:

1) It is not clear how long were the animals maintained in a breeder status prior to analysis.

2) Figure 3A, the rationale for the comparison of changes in young breeder versus non breeder animals to changes that occur with age over time is unclear.

3) Figure 4, were the changes driven by gonads mainly? How many were non-gonadal? For example, in Figure 2, muscle showed 0 DEGs by status, but in pathway analysis we see upregulation of pathways. Please explain.

4) Table 2: TOR is downregulated in breeders while ribosome processes are upregulated, please explain.

5)The finding of Cushing's syndrome needs more support. Please consider comparing Cushing's related transcriptome changes as a whole to the changes observed in mole rats, otherwise this conclusion may need to be toned down.

Reviewer #2:

Sahm et al. have analyzed gene expression of 22 samples across 15 tissues of Fukomys mole rat, and with these resources, they try to explain why breeders and non-breeders have different lifespans in those species. Below I highlight key aspects of the approach (and related conclusions, or lack thereof) that I believe represent serious issues. One positive note, again, the questions and data of this paper that I believe are highly interesting and important if the author can pursue it in a more focused and solid way.

1) First, in my opinion, the discussion of the paper is not well synthesized, and the content does not help the reader for the aim of study and of what is discussed in the title (e.g., HPA) and abstract. While the entire discussion fails to build logics between HPA stress and aging in mole rats, it tells the story of intervention and hypothesis testing instead, with the last of the results immediately jumping into comparisons of positive selection genes and DEG (It is unclear why it is relevant even one gene is found under positive selection).

2) Given hundreds of samples have been sequenced in the paper, there is no extensive examination of batch effect, which could ultimately, in its present form, put all the results (e.g., DEG analysis, pathways enrichment, multifactors analysis) and conclusions at high risk. Particularly, the PCA analysis has indicated the species, tissue, and the combination of both variables accounted for 98.4 % of the total variance in the data set--it becomes more important to know how the authors have organized the sequencing strategy.

3) Unsophisticated use of enrichment analysis on pathways likely leads to misleading conclusions - a large portion of the analyses presented use an unreasonable approach to identify genes with expression shift across tissues and species to make conclusions that I believe are largely misleading about genes important for longevity. The authors identify pathways that have overall (gene-wide) changes in gene expression as p values looks like a potential indication of expression shift. While this approach MAY be lucky enough to catch a few of these 'true positives", the VAST majority of what it will identify will be pathways with global accumulated changes (which is what the point would be), but rather small pathways or pathways fully of with wired p values or undetectable expression (and thus perhaps some of the least important genes). Then, the extension of these approaches to pathways further muddies the waters of any discussions. The approaches for detecting affected global pathways have been the subject of a very large body of literature, and there are well developed hierarchical/empirical models for testing these hypotheses that the authors have not referred to. And, of course, it is strongly encouraged that the authors formulate a new model/index to reevaluate pathways analysis as the data and experimental design is unique compared to other studies.

4) Last but not the least, small KEGG set, i.e., KEGG, that with very few genes could also be confusing such whole categories analysis. The author should check this potential bias using random sampling 'pseudo-KEGG set' with the same gene number and/or identify a threshold to filter each true KEGG category considered.

Reviewer #1:

This is a primarily descriptive study reporting gene expression differences between breeding and non-breeding individuals of two long-lived Fukomys species. These mole rat species are interesting for this type of analysis because it has been previously shown that breeders live ~2-fold longer than non-breeders. Thus, it may be possible to learn about mechanisms that determine longevity by studying differences between breeders and non-breeders. Although the manuscript is primarily descriptive, there is value in observational data sets such as this, which can be hypothesis generating and can spur future, more mechanistic studies. A lot of analyses are presented - with many different comparisons of differentially expressed genes, GO terms, etc. - but they have not yet produced a lot in terms of true biological insight. As it was largely limited to gene expression, it is also a bit one-dimensional. The data will likely be of interest and value to scientists who study the comparative biology of aging and systems biology of aging, but without additional biological insights derived from the data, the manuscript will probably not capture the interest of a broad scientific audience or even the broader gerontology community.

My largest concerns with the content of this manuscript are related to interpretation of the data. While this type of comparative gene expression analysis can generate hypotheses, it cannot strongly support or refute causal relationships without additional experimentation. The authors repeatedly appear to interpret correlative observations with causation and make claims that overreach the data. The title itself is a good example of this where the authors claim "the HPA stress axis shapes aging rates". There is no direct evidence to support this claim or others similar in nature throughout the manuscript.

Another area of overinterpretation is with respect to the relevance of these findings as a test of the validity of prior aging theories or mechanisms. It seems very likely that this is a somewhat unique evolutionary case where upon the switch from non-breeder to breeder there is a dramatic rewiring of physiology at many levels (transcriptional, translational, post-translational, metabolome, epigenome, etc.). Simply because this switch does not match patterns seen in longevity interventions such as caloric restriction, reduced GH/IGF-1 signaling, or mTOR inhibition does not refute or call into question literature describing potential mechanisms for how those interventions act. It likely simply reflects that this is a different path to achieve longevity.

Specific comments:

• The title is problematic as described above.
• The first sentence in the abstract is problematic as it implies causality between sexual activity/reproduction and longevity. Sexual activity/reproduction are associated with life expectancy. It is interesting to consider whether these two things could perhaps be uncoupled in this animal, as has been shown for reduced fecundity and longevity in invertebrate models.
• The phrase "oppose crucial findings" in the abstract is also problematic. First, the word "crucial" does not seem to make sense in this context. What makes them crucial? Second, it is intuitive and expected, indeed perhaps required, that reproduction would be associated with anabolic processes, and this study does not show causality between the observed changes in these processes and longevity, so it does not actually "oppose" the prior findings in genetic models with reduced IGF-1/GH signaling where lifespan is extended.
• I have a problem with the premise that it is possible to "confirm or falsify" results from cross-species or intra-species studies through the type of approach taken here as implied in line 47. Confirming or falsifying results implies something about the quality of the prior data itself. I assume what the authors mean is confirming or falsifying the underlying hypotheses or assumptions. Even that is questionable, however, since the mechanisms by which longevity are determined could simply be different within species versus across species versus cases like this where you have dramatically different life expectancies in breeders versus non-breeders.
• I thought the discussion of the GH/IGF-1 results was fairly balanced, but I would encourage the authors to consider more deeply the within species versus across species observations in the literature. The evidence for reduced GH/IGF-1 increasing lifespan comes from within species studies and appears to hold true from worms to dogs and likely in humans as well, although the correlation between body size and lifespan is a bit more complicated in humans for obvious reasons. Within species, smaller individuals who have reduced GH/IGF-1 tend to live longer - that's a correlation. In worms, flies, and mice a reduction in growth signaling has been shown to be sufficient - and very likely causal - for enhanced longevity through genetic and pharmacological studies. The comment that these interventions are all performed during development is not exactly true - in mice rapamycin at least works in adulthood and even when only given transiently or intermittently in adulthood. Across species, larger species tend to live longer. Perhaps the mechanisms going from non-breeders to breeders more resemble the evolutionary longevity strategies that have been taken at the species level rather than the mechanism that appear to determine longevity within species. Personally, I don't see this as a contradiction or a controversy within the field.
• I find the "short-lived" versus "long-lived" species argument to be overly speculative and arbitrary. Interventions such as CR, mTOR inhibition, reduced IGF-1, etc. extend lifespan at least from worms to mice, which is a >50-fold difference in lifespan. Mice to people is ~30-fold. Compared to mice, worms are shorter-lived (by a fold difference metric) than mice are compared to humans.
• The authors state that breeders and non-breeders have "massively diverging aging rates", but I think it is important to keep in mind that differences in lifespan do not necessarily imply differences in aging rate. Especially going from the long-lived state to the short-lived state. Perhaps there is good evidence that functional and molecular declines and diseases/pathologies of aging are accelerated in the non-breeders and delayed in the breeders, which would support this assertion, but this is unclear from the manuscript.
• The phrase "unilaterally described as harmful" in the conclusion is simply not true. GH/IGF-1 signaling limits lifespan in worms, flies, and mice but none of the papers cited unilaterally claim that it is harmful. In fact, some of those same papers note that high GH/IGF-1 signaling often confers a selective advantage in terms of faster maturation and reproduction. So, at the species level, this is beneficial. Even at the individual level, high GH/IGF-1 may be associated with better outcomes in the wild where predation is a factor. High GF/IGF-1 in these species is detrimental (only?) in the context of aging/longevity in a relatively safe laboratory environment at the individual level.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

Summary

Mole-rats live in social colonies that contain two breeders and many non-breeding workers. This study looks at gene expression between breeding and non-breeding individuals of two long-lived mole-rat species in the genus Fukomys. The large lifespan difference between breeders and non-breeders has made these animals an important model system for the study of aging, and the data collection reported in this manuscript is very impressive. The paper is descriptive data, with limited data analyses and experimental support for the conclusions. However, given the scale and rarity of the dataset, it will be a valuable resource for the aging research community once the quality and physiological relevance of the data are demonstrated by additional bioinformatic analyses and experimental validations.

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Reply to the reviewers

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Response to Reviewers

We are grateful to the Reviewers for their thoughtful and helpful assessment of our work. Below we include a point-by-point response to the Reviewers' critiques concerning the interpretation of our results and the power of our system to elucidate key dynamics of fission yeast homology-directed repair (HDR). We appreciate that the Reviewers judged our assay to be a valuable new tool for studying DSB repair in S. pombe. In general, the Reviewers also felt that our data provides new insights into homology search during HDR in fission yeast, including 1) that multiple DSB-donor encounters often precede repair and 2) that the activity of the helicase Rqh1, which dissolves strand invasion structures, alters the kinetics and efficiency of HDR in S. pombe. The Reviewers also raised several concerns with regards to 1) some technical aspects of the experimental approach, 2) the display of the data, and 3) the interpretation of the data. The Reviewers requested additional experiments to address the efficacy of our 5 minute observational time window and the rate of spontaneous damage in the Rqh1 null background, which we are able to provide in a resubmission. We will also clarify experimental details that the Reviewers found confusing in the original text. Lastly, the Reviewers highlighted minor needed figure adjustments that we will incorporate.

Point-by-point Response:

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

Vines et al adapted a system that has been used in S. cerevisiae to study the homology search and homologous recombination repair events by live cell imaging. The authors utilized a system they set up in a fission yeast strain that has a fluorescently tagged endonuclease induced DSB site and monitored RAD52 focus formation in both haploid and diploid cells. The main findings presented are that multiple strand invasion events occur during DSB repair and the role of Rqh1 in promoting these multiple events. For example, cells with Rqh1 loss either have a single strand invasion event that quickly leads to repair or a very long extensive repair time. Overall the results are intriguing with new insight into DSB repair being presented.*

We appreciate the Reviewer’s recognition that our work provides new insights into homology-directed repair (HDR) in fission yeast.

The manuscript would benefit from having another system to help to support or validate the key findings and/or the use of some mutants to help uncouple the different roles of Rad51 and/or Rqh1.

While we agree with the Reviewer that using orthogonal approaches is always desirable, it is not clear what other experimental platform can address the dynamic events with single cell resolution that underlie our observations here; indeed, this was the motivation behind designing this new approach. However, we will provide additional, detailed context to support our findings in the revised manuscript that highlights how orthogonal experimental strategies (e.g. DSB repair outcome assays) already in the literature (e.g. Hope et al., PNAS, 2006) are consistent with our findings. Importantly, however, there is no other population-based system we are aware of that could demonstrate, for example, that Rqh1 shows two different behaviors in individual cells (repair failure and more rapid repair). See more in response to comment 7, below.

\*Major comment:**

1) In Figure 1C, and also Figure 2D, the RAD52 focus observed does not appear in the same location as the LacO cassette. I assume this is because of the way the images are cropped. It would be nice if the authors are saying that the RAD52 focus co-localizes with the inducible DSB location for this to be more readily apparent in the representative images. *

Co-localization events, indicated with the yellow circles, are assessed within raw 3D data that is then flattened for representation in 2D in the figures. For Figure 1C, the two events in the example cell indeed overlap in 3D space. However, in Figure 2D (cells lacking Rad51) we do not observe any colocalization events in the example (and there are no time points annotated with yellow circles).

2) In Figure 3A, the authors claim that the mean time to repair an endonuclease induced DSB is 50 min +/- 20 min. It is unclear whether or not this experiment is done in a diploid strain.

We apologize if we were not clear. All experiments presented in the manuscript are carried out in diploid cells. What varies is whether there is a lac operator integrated at one copy of Chr II (all experiments except Fig. 2A) or on both copies (only Fig. 2A). This will be clarified in the revised text.

3) In Figure 3, whether or not this experiment represents asynchronous cells can greatly influence the timing of DSB repair, as the cell cycle is a huge contributor to HDR repair.

We agree with the Reviewer - the cell cycle has a critical influence on DSB repair mechanism. The diploid fission yeast in which we induced and observed DSBs are indeed asynchronous. However, in fission yeast, which spend over 80% of their cell in G2, we can assess cell cycle by morphology; cytokinesis coincides with the beginning of G2, which then persists until mitotic entry (which is also very obvious from the nuclear shape as visualized by Rad52-mCherry). Moreover, we previously found that HO endonuclease only induces DSBs during S phase (Leland et al., eLife, 2018). Given this, for individual cells we observe site-specific DSBs beginning in late S and early G2 phases and all of our analysis is done at this phase of the cell cycle. These observations are further validated by the observation that an HO-induced DSB undergoes very high rates of gene conversion in fission yeast (Prudden et al, EMBO J., 2003).

4) In Figure 3D, since a major finding of the paper is that there are multiple invasion events, it would be nice to show some representative images of a few cells where multiple pairings occur.

In Supplementary Figure 2A, we provided an example of a cell with multiple encounters between the DSB and donor. This will be more clearly highlighted in the revised text.

5) It is known from Eric Greene's work that RAD51 mediated homology search can do multiple samplings of 8-9 nucleotide segments. Have the authors considered the area around the DSB site and how many potential pairing sites there might be in this region? Is it possible that having a LAC array with repeated segments might be influencing this the pairing since there would be multiple templates?

We acknowledge that the homology of the region surrounding the DSB is important for faithful recognition of a homologous donor and that there could be many pairing sites surrounding our induced DSB after end resection. Such local sampling, however, would not be discernible due to the resolution of the light microscope (>0.2µm). We will address this noteworthy point during our discussion in the revision. Importantly, we placed the lacO array over 3 kb away from the locus where the HO recognition site is integrated on the homologous chromosome to attempt to avoid exactly the Reviewer’s concern.

6) It would aid the reader if there were some picture schematics of what the authors think is occurring throughout the paper in the Figures. Since this is a results/discussion, this approach would be appropriate in lieu of a model figure at the end (which would also be very nice).

We agree that diagrams would aid in communication of our hypotheses and interpretations, and these will be included in the revision.

7) Since the multiple strand invasion events is a major finding of the paper, it is important to test the hypothesis that multiple strand invasion events are occurring a different way. A few ideas would be to examine Lorraine Symington's work on BIR where she observes multiple template switching events (Smith, CE, Llorente, B, Symington, LS (2007) Nature, 447(7140): 102-105) or something analogous to Wolf Heyer's recent study in Cell on template switching that the authors already cited. Another idea is to try a RAD51 mutant. For example, Doug Bishop's group has created a RAD51 mutant that uncouples the homology search from strand exchange, Rad51-II3A mutant (Cloud, V et al (2012) Science, 337(6099): 1222). Perhaps a mutant like this might be able to further support the key finding here.

While our findings share parallels with the works raised by the Reviewer, we would argue that there is a fundamental difference between BIR-type assays and the one we present here, namely that we are visualizing multiple strand invasion events at the homologous chromosome in a normal, high fidelity repair event rather than multiple strand invasion events during BIR, which frequently result in translocations. Moreover, as the two chromosomes are perfectly homologous in our assay, we cannot leverage sequencing to reveal past strand invasion events that took place during HDR. We also cannot, unfortunately, access multiple simultaneous strand invasion events due to the diffraction limit of the light microscope. We concede that it would be informative to further dissect strand invasion using tools such as the Rad51-II3A mutant described in budding yeast in work referenced above by Reviewer #1 and developed in fission yeast by Sarah Lambert’s group (Ait Saada et al., Mol. Cell, 2017). However, with the present limitations on our laboratory access and the timeline necessary to carry out this experiment, we feel this is currently beyond the scope of this work.

8) It is surprising that Rqh1 doesn't have a role in DNA end resection since this is a conserved function from budding yeast to man. Would similar results to what is observed in Figure 4 be observed in a Dna2 or Exo1 mutant?

We acknowledge that Rqh1 orthologs in other organisms (BLM/Sgs1/etc.) have been shown to contribute to DSB end resection. However, previous work from our group indicates that Rqh1 is entirely dispensable for long-range resection in fission yeast (Leland et al., eLife, 2018). Interestingly, in this work we also demonstrated that it is only upon loss of either the 53BP1/Rad9 orthologue Crb2 or Rev7 that Rqh1 is able to compensate for loss of Exo1. It remains unclear whether this is a peculiarity of fission yeast (perhaps because they rely heavily on HR due to extensive time in G2) or if it is a direct consequence of the long G2 itself. Regardless, we demonstrated that cells lacking Exo1 cannot generate sufficient ssDNA tracts to load visualizable Rad52-mCherry (Leland et al., eLife, 2018). Given this, we cannot address this genetic background in this assay. The essential role for Dna2 in replication has also precluded its analysis.