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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study, Chikireddy et al. perform a series of experiments in which they compare the efficiency fo cofilin-mediated severing and actin filament disassembly on individual filaments versus bundles of different sizes from by the actin-bundling protein fascin. The key outcome, quite distinct from previously published conclusions by the authors themselves and other authors, is that fascin bundling actually reduces cofilin-mediated severing mostly because of much slower "nucleation" of cofilin clusters on fascin-bound filament bundles. Cofilin cluster formation is followed by local fascin removal, and the nucleation of a cofilin cluster on an adjacent bundle in the absence of fascin is strongly enhanced. The reason for the latter surprising observation is not entirely clear, but proposed to arise from cofilin-mediated changes in filament helicity of neighboring filaments. To my understanding, the main reason why fascin protects from cofilin severing here rather than enhancing it (as reported previously) is due to the lack of constraining of the induced, cofilin-mediated twist, because if this twist is constrained e.g. by anchoring of the bundles to the surface chamber, then severing by cofilin is accelerated.

Major comments:

I think the study is very well done, most experiments are super-elegant and controlled; I really don't have any objections against the conclusions drawn, as most of what I have seen is totally justified and reasonable. So from a scientific point of view, I can easily agree with all the major conclusions drawn, and so in my view, this should be published fast.

Minor comments:

There are two minor points that could be addressed:

1. I am not entirely convinced by the conclusions drawn from the EM images shown in Figure 6A, and in particular by the filaments in two-filament bundles locally twisting around each other (without breaking) at spatial sites lacking fascin and decorated by cofilin. This is hard to imagine for me, and the evidence for something like this happening is not very strong, as in the EM, only larger bundles could be observed. In addition, I am not sure that the braiding of filaments seen in the presence of cofilin is really occurring just locally on cofilin-decorated bundle segments and thus indeed coincides with loss of fascin as proposed in the scheme in Fig. 6B. Can the authors exclude that the braiding is not caused by some experimental artefact, as induced perhaps by sample preparation for negative staining? Did the authors quantify the occurrence of such braided bundle segments with and without cofilin? How large are these braided segments on average when you quantify them? Would you also see them if you prepared the bundles for an alternative EM-technique, such as Cryo-EM, for instance? This may admittedly all be experimentally challenging, but would it be possible to combine the negative staining of filaments with staining for cofilin and/or fascin using immunogold technology, to prove that the braided segments do indeed correlate with high cofilin and low fascin concentrations? In the absence of such data, and in particular in the absence of a clear quantification, the proposal is too strong in my view. Finally, it would be nice (albeit not essential I guess) to also look at two-filament bundles. The authors stated these can not be easily generated due to the tendency of fascin to promote the formation of larger bundles, but can this not be titrated/tuned somehow by lowering fascin concentrations, to come closer in reality to what is proposed to occur in the scheme in Figure 6B? In any case, the way the data are presented right now appears to constitute a pretty large gap between experimental evidence and theoretical model.
2. I think that the proposal of cofilin-decorated filaments to "transfer" the resulting cofilin-induced changes in filament helicity onto neighboring filaments in the bundle, which is proposed to occur locally and in the absence of fascin is a bit vague, and difficult to understand mechanistically. Can the authors speculate, at least, how they think this would occur? Are there no alternative possibilities for explaining obtained results? Maybe I am missing something here, but with considering cofilin to be monomeric and only harboring one actin-binding site, this proposal of helicity transfer onto neighboring filaments seems inconclusive.

Significance

General assessment:

The strength of this study is that owing, at least in part, to the microfluidics devices employed and the careful biochemistry, the experimental setups are super-controlled and clean, and they are used in a highly innovative and elegant fashion. The simulations are also nice! A limitation is that it is not entirely clear how precisely the main observations can be translated to what's happening in vivo. The results are largely dependent on the bundles not being constrained I understand, so to what extent would bundles be unconstrained in vivo? Perhaps this is not so important, because the experimental setup allows the authors to dissect specific biochemical behaviors and inter-dependencies between distinct actin binding proteins, but the latter view (if correct) could be stated more clearly!

Advance:

As stated above, the results are opposite to the proposed synergistic activities of fascin and cofilin observed for bundles previously, perhaps because they were not constrained. So although touched in part and in a very polite fashion in the discussion, the authors could specify more clearly what the differences between the studies are, and which of the distinct activities observed either here or in previous literature will be dominant or more relevant to consider in the future? This will be hard to discern as is now, in particular for non-experts.

Audience:

This manuscript will be most influential for a specialized audience interested in the complexities of biochemical activities of specific actin binding proteins when looking at them in combination. Although specialized, this is still a quite relevant audience though, since prominent actin binding proteins like cofilin are highly important in virtually any cell type and various actin structures, hence of broad relevance again in this respect.

Expertise:

I am a cell biologist and geneticist interested in actin dynamics and actin-based, motile processes.

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Referee #1

Evidence, reproducibility and clarity

In this study, it is shown that cofilin severs actin filaments slowly when fascin is present. Authors show that this is due to slower cluster nucleation of cofilin on fascin-induced actin bundles. Interestingly, the authors show that cofilin binding promotes helicity in actin filament bundles which in turn promotes facin exclusion and more cofilin clustering in adjacent filament bundles; thus, inducing local transmission of structural changes.

The authors use an elegant approach, and the data is nicely presented. Overall, I consider that this manuscript is in good shape to be published. It might benefit from language editing, though.

Significance

According to me the significance of this manuscript is that elegantly shows the molecular details of the cofilin severing effect of fascin-induced actin filament bundles. The authors show that cofilin binding promotes helicity in actin filament bundles which in turn promotes facin exclusion and more cofilin clustering in adjacent filament bundles; thus, inducing local transmission of structural changes.

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Reply to the reviewers

ReviewCommons Reviews Point-by-Point

Manuscript number: RC-2023-02131

Corresponding author(s): Holger, Gerhardt

Reviewer #1

Evidence, reproducibility and clarity

Summary: Giese et al. use genetic lineage tracing techniques and novel computational analysis methods to quantify and predict how the spatial distribution of ECs changes over time in the developing mouse retina from P5 to P9. They also develop mathematical models to describe and predict the response of ECs to the hypothesized dual force-field formed by the chemoattractant VEGFA, and the flow-induced shear stress.

Given that the mouse retina cannot be live imaged, these new methods are essential to infer cell dynamics from static images. With these methods the authors confirm previous findings that arteries are formed by endothelial cells derived from veins, or tip cells, or capillaries. They then combine their genetic system with Cdc42 and Rac1 floxed alleles to understand the function of these genes in EC mobilization. They find that Cdc42 has a very strong role in EC mobilization to arteries, not so much to the sprouting front, whereas the loss of Rac1 has relatively minor effects in vivo. Loss of Rac1 slows the cells but they maintain their directionality towards arteries. The discussion section and integration of these paper findings with previous work in the field is excellent.

Overall, this work provides a much higher level of quantitative analysis of endothelial cell dynamics in the developing vasculature of the mouse retina. It also provides mathematical models that can be useful to explain and predict the impact of other genetic mutations or pharmacological interventions during vascular development.

Reviewer #1, Major comment 1: This work provides one of the finest examples of quantitative biology in the vascular biology field. The conclusion on cell dynamics is however largely based on static images measurements and pre-defined mathematical models given also previous work and the proposed model of a dual-force field. The authors conclude that sprouting front cells mainly migrate away towards VEGF, whereas remodelling plexus cells migrate towards arteries. However, this is based on the entire EC population measurements/displacement and averaging, and does not account for the possibility of a few ECs having a different behaviour from most of their neighbours. This comment is related with the fact that arteries are formed mainly by tip-derived ECs, the cells closest to the VEGF source and further away from the flow/shear stress force. It seems the authors model presented here would not allow this to happen. According to the model presented, it seems that an EC close to the VEGF source, and subjected to low flow (shear stress), would always migrate to the front and never turn back towards arteries. Can a more complex model enable the consideration of the stochastic loss of VEGF signalling (or gain of shear stress sensing) by some ECs at the sprouting front ? And their subsequent formation of arteries ?

Response: We would like to thank the reviewer for these insightful views and for raising these questions. The aim of the computational model is to provide the simplest possible model that can be used to obtain estimates of EC migration patterns. This computational model can be used to introduce other aspects of endothelial cell behaviour, including proliferation and subpopulations with different migration sensitivities. However, the stochastic loss of VEGF signalling or gain of shear stress sensing is modelled by a stochastic term. For example, the coupling strength for control is 0.36, meaning that 0.36 is explained by directed migration along the force field, while the remaining 0.64 of the movement is stochastic. We agree that this could also be modelled differently to disentangle this stochastic term if more data on subpopulations were given. This will certainly be a fruitful direction for future research. As we do not have explicit proliferation data or data on subpopulations, direct inclusion of these extensions is difficult to validate and justify, or must be based on further assumptions or speculation.

We agree with the reviewer that there are likely distinct subpopulations, given also that ECs can compensate for higher sensitivity to shear stress or VEGF-A with higher migration speed (see Figure 2 F). Currently, the shear stress cue is overwritten by the VEGF-A cue in the sprouting front. Furthermore, both cues cancel each other out in the transition region from remodelling plexus to sprouting front, this was also suggested in (Barbacena et al., 2022) though this behaviour can be explained by heterogeneity or ECs being randomly polarised due to conflicting cues, which is not directly resolved by the data.

Nevertheless, random migration is a very inefficient strategy as shown in our theoretical investigation. Therefore, at the system level, it seems to be a much more efficient strategy to have EC subpopulations, since in this case ECs would migrate directly along one of the cues, rather than behaving randomly due to conflicting cues. We will add these considerations to the discussion of the mathematical model.

*Reviewer #1, Major comment 2: Previous work by Laviña et al showed that Cdc42 is required for the migration of ECs to the sprouting front. The authors' data suggest that Cdc42 is not necessary for this process. *

__Response: __We thank the reviewer for highlighting these points. We report a significant phenotype for Cdc42 depleted cells in the sprouting front: There is a significant shift of labelled cells from arterial to venous direction from P5 to P9 and in particular from P8 to P9. Therefore, the region of the sprouting front above the artery lacks Cdc42-depleted ECs, which can be clearly seen in the KDE plots in Figure 3.

A very important difference in our study is the definition of the sprouting front. In our study, the sprouting front is a whole region that extends to the tip of the vein, see Figure 2 and explanation on page 7: “Additionally, each retina was divided into a remodelled region containing mature veins and arteries (in the following called remodelling plexus) and a region lacking mature vessels (called sprouting front)”. However, in Lavina et al., as well as in some other studies, for example Barbacena et al., the sprouting front is the very end of the retinal vasculature. In Barbacena et al. the sprouting front is VEGFA dependent on the 100-200 μm from the very edge of the vasculature, whereas our region of interest extends much further for about 500 μm and we may lose definition for a tip cell related Cdc42 phenotype in our analysis. Our KDE plots extending from 0 (optic nerve) to 2000 μm (end of the vasculature) show a clear sprouting front Cdc42 phenotype, indicating that there is an accumulation of Cdc42 KO ECs at the end of the veins. However, these plots lose definition in the region analysed in Lavina et al. and Barbacena et al. Therefore, we will extend our analysis and explicitly report cell number proportions in the sprouting front that are compatible with (Lavina et al., 2018) and (Barbacena et al., 2022).

We will add a quantification of EC proportions in the sprouting front to make our study more comparable.

*Reviewer #1, Major comment 2 (continued): Could the difference between previous and the authors results be technical and related with the different stage of induction/analysis or the extent of Cdc42 deletion ? Did the authors tried inducing at P1 and collecting at P6/P7 ? *

Response: Lavina et al. used earlier induction time points at P0, P1 and P2. We do not know whether a retina at P5 requires less Cdc42 for sprouting front development. At this time point (P5), there is a distinct vasculature of veins, arteries forming a vascular plexus, and a sprouting front in contrast to P1, which is mainly a small vascular plexus. We will add these important points to the discussion of our manuscript.

In order to understand the role Cdc42 and Rac1 play in sprouting angiogenesis and migration to the sprouting front that is not influenced by different Cre lines and induction regimen, we will co-culture control and Cdc42/Rac1-deficient HUVECs in 3D microfluidic devices and analyse their sprouting over a number of days . With this assay we will be able to quantify the proportion of siCdc42/siRAC1 cells in tip and stalk positions compared to control, as well as do junctional and cytoskeletal analysis via immunofluorescent staining. See preliminary data in Additional Fig. 1 .

Reviewer #1, Major comment 2 (continued): The reporters used were also different and they may have different sensitivities to tamoxifen (and hence report Cdc42 deletion differently).

__Response: __This is correct as different Cre reporters have been shown to exhibit different sensitivities to recombine, including some with tamoxifen independent activity. The mTmG reporter we used however has been shown to reliably report tamoxifen induced recombination. Nevertheless, given that the reporter allele and the floxed gene alleles can recombine independent from each other, we cannot exclude the possibility that some GFP expressing cells still express Cdc42 or Rac1, or that some cells that have lost expression of Cdc42 or Rac1 due to recombination remain GFP negative. Statistically, these will however be rare events. The fact that we track all GFP positive cells allows us to draw conclusions on population behaviour, but not necessarily on the validity of any specific cell. The power of our analysis lies in the ability to draw conclusions on many randomly labelled populations across multiple time points without the necessity to validate each individual cell. The fact that the GFP population that carries floxed alleles for Cdc42 or Rac1 behave differently from those that do not provides strong evidence for successful loss of function for most of the cells. Importantly, unlike conventional full KO, this altered population behaviour occurs in the absence of an overt overall tissue phenotype, as we only lose gene function in a subpopulation of endothelial cells. The fact that we observe distinct deficiencies for migration towards the artery but not towards the sprouting front is therefore likely a true reflection of distinct functional importance and not evidence for a technical problem. Orthogonal evidence for such a selective role stems further from our in vitro cell culture experiments.

In the revised manuscript, we will include new mosaic flow-migration microfluidic studies as well as the mosaic vessel-on-chip assays mentioned above to independently verify the selective role for Cdc42 in flow-migration coupling versus sprouting (Additional Fig. 1).

Reviewer #1, Major comment 3: In the last section, some of the junctional/polarity/actin markers and analysis done in vitro could be also done in vivo.

Response: We agree with the reviewer that these experiments could be very informative to investigate junctional, polarity and actin markers. However, we believe that without a specific question these experiments would be rather explorative, do not add significant information to the current message of the study and can therefore not justify further animal experiments. This should in our opinion be the subject of future work.

We will however, quantify junctional markers in a sprouting 3D assay, see response to Reviewer #1, Major comment 2.

Reviewer #1, Major comment 4: The extent of Rac1 deletion in the mosaic experiments (done with suboptimal doses of

tamoxifen) could be analysed. This is especially relevant since minor effects for Rac1 were observed in these in vivo experiments.

Response: Lavina et al. used earlier induction time points at P0, P1 and P2. We do not know whether a retina at P5 requires less Cdc42 for sprouting front development. At this time point (P5), there is a distinct vasculature of veins, arteries forming a vascular plexus, and a sprouting front in contrast to P1, which is mainly a small vascular plexus. We will add these important points to the discussion of our manuscript.

In order to understand the role Cdc42 and Rac1 play in sprouting angiogenesis and migration to the sprouting front that is not influenced by different Cre lines and induction regimen, we will co-culture control and Cdc42/Rac1-deficient HUVECs in 3D microfluidic devices and analyse their sprouting over a number of days . With this assay we will be able to quantify the proportion of siCdc42/siRAC1 cells in tip and stalk positions compared to control, as well as do junctional and cytoskeletal analysis via immunofluorescent staining. See preliminary data in Additional Fig. 1 .

Reviewer #1, Minor comment 1: Lee et al., 2022 is a review. Better cite the original papers if possible: Some examples: Xu et al., 2014, Pitulescu et al 2017 and Lee et al., 2021.

Response: We would like to thank the reviewer for this suggestion and have added the citations to original publications where appropriate (see page 2 in the “Introduction” section).

Reviewer #1, Minor comment 2: Figure 1A: Stage of induction with tamoxifen is missing. Likely P5.

Response: We added this information to the caption of Figure 1A, Figure 3A and Figure 4A.

Reviewer #1, Minor comment 3: Figure 3 and 4 data would be easier to compare/understand by readers if part of the Wt data in Figure 1 was also plotted here. Or at least a Wt trend/average line on top of the mutant data, for us to see how much Cdc42 or Rac1 deletion changes the behaviour of the mutant cells versus the Wt cells.

Response: We agree with this suggestion and will add the wild type data for comparison in Figure 3 and 4.

Reviewer #1, Minor comment 4: Overall, for all dot plots and heatmaps, would be better to indicate the total number of cells analysed/plotted since the power of the analysis is related with cell number rather than number of retinas.

Response: We would like to thank the reviewer for this comment and agree that indicating the number of cells analysed allows the reader to contextualise the results more easily. We will therefore add estimated numbers of cells analysed to the respective figures. However, it is important to note that we used labelled pixels (GFP and ERG positive) as a proxy for the EC distribution, but did not segment out single cells. We always used the same number of 10,000 randomly selected pixels by bootstrapping to quantify the endothelial cell distributions. The heat map plots summarise the single cell behaviour pooled together for all retina samples. Therefore, each retina contributed equally to the analysis. This way, we could provide statistics on independent biological replicated samples for a thorough analysis.

Significance

General assessment: This paper is very strong on the quantitative analysis and mathematical modelling. Methods used and the model proposed may be of broad relevance for the field of vascular biology. It is however based on certain author-defined parameters and assumptions. EC dynamics in vivo can be much more complex than what can be modelled by equations. For example, heterogenous single cell genetics and signalling inputs can induce changes in cells that override the normal/average behaviour of the cells that are modelled. Despite the high level of quantitative analysis and modelling, the main findings here presented are not entirely novel, given previous work. For example, it was previously known that arteries are formed by vein/tip/capillary cells. It was also known that Cdc42 was required for proper EC migration away from veins (Laviña et al., 2018). However, the better quantitative analysis here presented does provide a higher level of detail and reliability.

The mosaic genetics used to delete Cdc42 is in general clear since few reporter positive cells can make arteries, suggesting efficient deletion of this gene. The data also goes in line with previous work. However for Rac1, given that a much weaker phenotype was observed, is not possible to be sure that all GFP+ ECs had deletion of Rac1. This is especially important in mosaic genetic experiments, using a suboptimal dose of tamoxifen. The extent of Rac1 deletion in GFP+ cells was not analysed. Which leaves the open question if Rac1 is really dispensable for EC migration and arterialization. Embryos lacking Rac1 in endothelial cells die early during development. Therefore ECs fully lacking Rac1 may have stronger defects than the ones shown here. All this data was obtained in the postnatal retina angiogenesis system. Other organ vessels may develop differently. Future work will tell if the models proposed can explain the dynamics of ECs during the growth of other vascular beds.

*Audience: Vascular/Cell biology researchers and bioinformaticians developing tools for image analysis and/or cell migration/dynamics modelling. *

Expertise of Reviewer: Vascular Biology. I do not have sufficient expertise to evaluate the mathematical modelling part of this paper.

Reviewer #2

Evidence, reproducibility and clarity

Summary: Giese et al., develop a computational model to track the migration of tip and venous endothelial cells (ECs) into developing arteries in the mouse retina. They validate prior studies which have identified important roles of shear stress and VEGFA gradient in driving EC migration and argue through their model that these dual forces shift in their relative influence along the vein-artery axis. Through in vivo lineage tracing in combination with Cre-inducible mouse knockout models, Giese et al., explore the role of Cdc42 and Rac1 in flow-migration coupling. They conclude that Cdc42, and not Rac1, is the primary driver of polarized flow-migration, further confirming this result with in vitro flow experiments involving siRNA depletion of Cdc42. Finally, the authors show that Cdc42 also plays a role in EC migration independent of flow, highlighting that its role in migration is universal and directly related to both actin regulation and cell junction dynamics.

Reviewer #2, Major comment 1: In Figure 1 the authors show retinas from a Vegfr3CreERT2 mouse model and make the claim that Vegfr3 is expressed in ECs in developing veins and tip cells, but not in arteries. Ralf Adam's group has previously shown that while Vegfr3 is more abundant in veins and capillaries than in arteries, expression is not exclusive to these EC subtypes (Ehling 2013). They, along with studies from Christer Betsholtz and Kari Alitalo's groups, show that Vegfr3 is observed in postnatal arteries (Tammela 2008, Ehling 2013). Indeed, from the panels in figure 1 (specifically P6 and P7) and supplemental figure 1, it appears that there may also be low levels of Vegfr3 expression in the arterial branches of postnatal Vegfr3CreERT2 mouse retinas. The authors should consider revising their statement that "ECs in arteries, however, do not express Vegfr3" and provide quantification of the number of GFP-labeled cells in arteries, veins and capillaries for each postnatal time point. Additional lineage tracing from later stages when migration into arteries is halted would be a good control for demonstrating that Vegfr3CreERT2 is not expressed in arteries, further support the authors' argument and conclusions.

Response: We would like to thank the reviewer for this comment. The percentage of labelled ECs in arteries of retinas for mice injected at P5 and collection at P6 is close to zero in all conditions (0.38 % +- 0.08 % (SEM) for control, 0.35 % +- 0.05 % (SEM) for Cdc42 depleted and 0.36 % +- 0.07% (SEM) for Rac1 depleted ECs). The same is true for mice injected at P8 and collected at P9 (0.22 % +- 0.06 % (SEM) for control, 0.11 % +- 0.03 % (SEM) for Cdc42 depleted and 0.11 % +- 0.01 % (SEM) for Rac1 depleted ECs).

As suggested by the reviewer, we will therefore revise the statement "ECs in arteries, however, do not express Vegfr3" and instead present the exact numbers in the revised manuscript, as this claim cannot be rejected or supported by our data. We will also add a discussion with references to (Tammela et al. 2008, Ehling et al. 2013) in our revised manuscript.

We would like to point out that this does not change the results of our study, since for us the Cre line is primarily a tool to label ECs of venous and microvascular origin to follow the change in EC distributions over time, and any pan endothelial Cre line would be suitable for our analysis. This was demonstrated for example in (Jin et al. 2022), where ECs with Cdh5Cre-induced expression of iSureCre+ MbTomato were used.

In addition, we will provide percentages as well as total cell numbers for labelled ECs in veins, arteries and capillaries in the revision of our manuscript for all time points and conditions.

Reviewer #2, Major comment 2: In their computational simulations, the authors investigate three models: random walking of ECs (M1), VEGFA gradient driven migration (M2), and integrated VEGFA /shear-stress driven migration (M3). The reader naturally wonders why a model considering only shear-stress driven migration is not presented as a control simulation. The absence of this model reduces the strength of the claims that only the M3 model captures observed EC movement rates, the mean population shift in vein-artery distance, and the arterial proportion of ECs.

__Response: __We agree with the reviewer and will certainly add a simulation of a shear stress only model and introduce it as model M4 in the revised manuscript.

Reviewer #2, Major comment 3: Much of the terminology in this study needs more detailed explanation and carefully usage. It would be more friendly to readers if they were consolidated into a box figure or table. (For example, how is coupling strength related or different from coupling rate?) The reported numbers of these factors are noted separately in text here and there. It would be helpful to put them together to highlight the difference between different models and mutant strains, as this is one of the novel findings for this study.

Response: Thank you for pointing this out. The word 'coupling rate' was incorrectly used in the introduction on page 3. It has been replaced by 'coupling strength', which is used throughout the text. We will add a table with quantitative information and explanations of parameters.

Reviewer #2, Major comment 4: The lack of labelled cells in the P9 retinas of Cdc42iECKO mice is striking (Figure 3), and strong evidence for the importance of Cdc42 in the migration of ECs towards arteries. The authors cite Lavina et al, 2018 when they note that Cdc42 depleted ECs proliferate at normal rates, but independent verification of this observation through EdU quantification would allow the authors to distinguish between the two possibilities outlined on page 15 of the manuscript: local proliferation vs enhanced migration of non-recombined ECs. These experiments and analyses are expected to be quick (depending on the availability of mice) and low cost. An independent EC proliferation analysis would also give the authors insight into the degree to which localized proliferation likely impacts vein-artery migration, a parameter which is currently unaccounted for in their computational model. The authors recognize that the lack of EC proliferation parameters is a limitation of their current model and speculate that this makes their estimates of vein to artery migration slightly too low. Independent EC proliferation analysis would thus be informative and may allow the authors to remove this speculation from their discussion.

__Response: __We do not see any reduction in the labelled Cdc42 population (Supplementary Figure 2) at P9. for all conditions we observe an increase of the labelled population from earlier to later stages (P6, P7, P8, P9). Our analysis is robust with respect to EC number, meaning that changes in EC number does not change the distribution. Our computational model would only slightly be affected by the difference in proliferation between arterial and venous beds, but not by the total number of proliferation events.

It is known from the literature that endothelial activation by shear stress is associated with inhibition of EC proliferation (Dejana et al. 2004; Bogorad et al. 2015). We used immunostaining to label phospho-histone H3 (pHH3) in perfused monolayers after 12 hours of flow exposure to uncover the effects that downregulation of Rho GTPases might have on the proliferation of ECs after exposure to flow. The biomarker pHH3 is a well-established standard for detecting the late G2 phase of mitosis. As shown in Additional Fig. 5, and in agreement with the literature, proliferation of ECs under flow conditions decreased by 27.38% compared to control static conditions. Following Rho GTPase depletion, siCdc42 cells further decreased their proliferation by 22.48% compared to control flow conditions, respectively. No significant difference was observed in siRac1 cells. It has been shown that the absence of Cdc42 increases EC apoptosis both in vivo and in vitro (Barry et al. 2015; Jin et al., 2013), but the role of Cdc42 in endothelial proliferation remains unclear in the literature. The data presented here suggest that Cdc42 has a modest effect on endothelial proliferation under flow in vitro. As shown in Additional Fig. 5, none of the loss-of-function conditions appeared to drastically alter the effect of flow on reducing proliferation in confluent monolayers. This suggests that RhoGTPases may not play a major role in the regulation of proliferation under the influence of flow.

We do not expect any further insight from EdU staining since also with EdU staining we could only quantify ECs entering the S phase in static images and how this translates into proliferation would still introduce further speculation. We therefore addressed this question in our discussion, as a quantification of proliferation would go beyond the scope of this study.

Of note, any requests for additional in vivo experiments would require new animal licence application and therefore a considerable time delay which we would only suggest to accept if substantial additional insight was to be expected. As it stands, all our claims are supported by several independent observations and can where necessary and as detailed in our revision plan, be addressed by orthogonal means.

Reviewer #2, Major comment 5: In the legends of Figure 1B & C, no information about the x or y-axis were mentioned. Even though the authors explained it elsewhere in the text or other figures, it is the first time that these parameters show up in the paper, which would be a proper place to note the details of these KDE plots.

Response: We added this information in the caption of Figure 1B,C, Figure 3B,C, and Figure 4B,C.

Reviewer #2, Major comment 6: In the legends of Figure 2B & C, it mentioned the results of coupling strength and fraction of shear stress, which was not obvious by just looking at the figures provided. It is also not mentioned whether the numbers are calculated by collected or predicted data.

__Response: __We agree with the reviewer that this information should be more prominent in the figure and will add it accordingly. These are predicted data, where we systematically tested different values of key parameters. We will therefore also change the caption of the figure from “Simulation of EC migration in the retinal vasculature” to “Prediction of EC distributions from computational model simulations” to make this clear.

Reviewer #2, Major comment 7: Please direct the reader to the supplemental figure containing the tamoxifen injection strategy when the Vegfr3CreERT2 mouse model is introduced in the text and when Cdc42 and Rac1 EC knockout is discussed in the methods.

__Response: __We also moved Supplementary Figure 1 and 2 to the beginning of the supplement as they are now referenced first in the main text and hope this will erase the confusion.

Reviewer #2, Major comment 8: There appears to be a significant degree of variance in the KDE plots from Figures 1, 3, and 4. It would therefore be helpful if the authors could include plots of the remodeling plexus and sprouting front that show the median for each dataset (similar to Figure 1 D and E), since this is less likely to be skewed by extrema. Additionally, for clarity and ease to read, it would be nice if author can consolidate the results of the mean from WT, Cdc42 and Rac 1 iECKO side by side. The images of the retina are striking, but the quantification is not as well-communicated.

Response: We plotted the median (including 10th and 90th percentile) already in Figure 1 Supplement 1, Figure 3 Supplement 1 and Figure 4 Supplement 1 and found significant

Reviewer #2, Major comment 8 (continued): If the argument is that Cdc42 only disrupts the migration, but not the differentiation, of artery EC, the authors should see a significant difference between WT and Cdc42 iECKO only in P9, but not early stages.

Response: We are not sure that we have fully understood the reviewer's reasoning, but our data confirm the reviewer's prediction of disrupted Cdc42 KO EC migration: The timeline for the percentage of labelled arterial ECs relative to the total labelled EC population is shown in Additional Fig. 2. Here, a significant increase was observed for both control and Rac1 iECKO ECs between time points P8 and P9, but not at earlier stages. For Cdc42 iECKO no significant increase was found at all stages. A direct comparison of all conditions is shown in Additional Fig. 3. Similarly, the proportion of Cdc42 iECKO compared to control is significantly different at P9 for mice injected at P5, but not at earlier stages.

Reviewer #2, Minor comment 1: For KDE plots in Figure 1B and Figure 3B, the authors labeled the x-axis differently (r vs dr). No description about the x-axis is noted in the legends. Please consider keeping the label consistent so the readers can relate and compare them.

Response: Thank you for spotting this mislabelling. We changed the axis annotation to d_r in Figure 1 as it is used in Figure 3,4 and throughout the text. We added furthermore information on the x and y axis in the caption of Figure 1B,C, Figure 3B,C, and Figure 4B,C. See also major comment 5.

Reviewer #2, Minor comment 2: For the in vitro study, the cell line used is not mentioned in the results, even though there is a method section about HUVEC. Authors should note this information in the main text.

Response: We agree with the reviewer and have added the following information in the main text on page 18 in the section “Cdc42, but not Rac1, drives polarised flow-migration in vitro” stating:

“To assess EC migration under coupling to shear forces in vitro, siScrambled (siScr) control, siCdc42 and siRac1 treated human umbilical venous endothelial cell (HUVEC) monolayers were exposed to 20 dynes/cm2 of flow using the Ibidi perfusion system and observed for up to 17 hours using a non-toxic fluorescent DNA dye for nuclear tracking.”

*Reviewer #2, Minor comment 3: Please note the flow direction in Figure 5B. *

__Response: __We have added an additional indication of flow direction for Figure 5B to improve the clarity of the figure. Note that the direction of flow is already indicated in Figure 5A and is the same throughout the figure.

Reviewer #2, Minor comment 4: The naming of supplemental figures requires revisiting. Currently there are two figures labeled with variations of supplementary Figure 1, which makes identifying the correct data challenging.

Response: We regret that the reviewer found the labelling of supplementary figures ambiguous and thank the reviewer for spotting this mislabelling. We corrected the label Figure S1 to Supplementary Figure 1. Furthermore, we also moved Supplementary Figure 1 and 2 to the beginning of the supplement as they are now referenced first in the main text and hope this will erase the confusion (also see Reviewer #2, major comment 7).

Reviewer #2, Minor comment 5: There appears to be a small typo on page 16 in second paragraph in the sentence that currently reads "Nevertheless, only few cells reached the arteries by P9"

Response: We changed this sentence: “Nevertheless, the accumulation of Rac1-deficient ECs in the artery was less pronounced compared to control.” Also we provide actual numbers, see Additional Fig. 2 and Additional Fig. 3 and our response to Reviewer #1, Major comment 4.

Reviewer #2, Minor comment 6: The axis labels for the plots in Figure 5, Figure 2 Supplement 1, and Supplementary Figure 2 are currently very tiny and difficult to read.

Response: We agree with this suggestion and will increase the size of the axis labels.

Reviewer #2, Minor comment 7: Additional information is required to describe the trajectory plots in Figure 2 Supplement 1, Figure 3 Supplement 3 and Figure 4 Supplement 3. I assume that blue trajectories move in the positive x direction while orange trajectories move in the negative x direction, but this is currently not specified in any of the legends.

Response: We added a specification in the figure legend.

Significance

Giese et al advance current understanding of the molecular mechanisms that guide vein to artery migration by convincingly demonstrating (both in-vivo and in-vitro) that Cdc42 is essential for this process. In addition, they present a computational model that captures the dual force field of VEGFA and shear stress gradients to simulate and quantify this migratory process in the mouse retina: a tool which will likely be useful for future mechanistic studies of vascular remodeling and EC migration. As far as I am aware, no standard coordinate system exists in the field for the quantification and modeling of this migratory process, so the introduction of this method alone serves as a useful innovation for the field of vascular biology.

It should be noted by authors and the editors that the mathematical details of the computational model and its statistical accuracies are not evaluated in this review, which instead focuses on the study's findings as they relate to EC biology and vascular development.

This study complements previous work that has identified populations of ECs that appear to be primed for incorporation into arteries, termed "pre-arteries" (Su et al 2018, Phansalkar 2021, Luo 2021). The authors' observation of heterogeneous EC movements during migration supports the intriguing suggestion that actin regulation through Cdc42 may be related to the establishment or phenotype of this pre-artery identity, though further mechanistic work will be required to validate this hypothesis, as noted by Giese et al in their thoughtful discussion.

Reviewer #3

Evidence, reproducibility and clarity

Summary: this study uses VEGFR3cre as a lineage tracking system to track venous endothelial cells within the maturing retina postpartum in order to investigate the cues related to sprouting and remodeling of the vascular network. They use complex computation modeling to predict outcome and come with in vivo/vitro observations.

They identify that venous EC move towards the arterial bed with flow and oxygen tensions as critical parameter. It is an impressive study that in principle confirms earlier studies on the role of EC population in sprouting and vascular remodeling however utilizes an interesting cell population based computational approach. Since these finding are pretty new, confirmation with different technologies and approaches is important.

However for more "traditional" vascular biologist it is very difficult to understand and follow particular if not familiar with the data presentation and mathematical modeling. This is a major shortcoming of this manuscript because I feel that if the authors would put more effort to better communicate their findings to a broader community not only enhance the value of their findings but also disseminate their computational approaches to a broader vascular scientist community.

__Response: __We thank the reviewer for this valuable critique, we will add a table where all parameters are described. Furthermore, we will add an additional subpanel in Figure 2 to explain the computational model.

I do have a couple of model related comments. The authors are using different models without adequate description.

The VEGFR3 is a lymphatic EC tracking model that potential can be used to track venous tip cells in the retina. But this model is not characterized within the retina in the study the author cite. I believe it would be necessary to characterize this model in traditional way before it can be used as described.

__Response: __We appreciate this comment and generally agree with the wish to see Cre lines well characterised. This is particularly relevant in studies where researchers delete a gene of interest using a Cre line and then make claims about the role of the gene in certain tissues with assumed recombination specificity. In our study however, we are not using the Cre line as a lymphatic or venous specific line to make such claims. Instead we use it in combination with the mTmG reporter, to quantify population distributions. Therefore every sample is its own “characterization”.

We could cite literature that support our claim of lack of arterial expression (Ehling et al., 2013, Tammela et al., 2008) of Vegfr3 in postnatal retina, but these studies did not use this Cre-line. For the purpose of our study, and in line with previous comments by referee 2, we feel it is best to moderate the claim, as very rarely single arterial cells can be found to have recombined 24 h after tamoxifen injection, see Additional Fig. 2 and Additional Fig. 3. The revised manuscript therefore has the claim toned down to better reflect this. Nevertheless, the utility of the Cre-line is not dependent on whether or not single arterial cells can be labelled, as the coordinate system and population quantification shows the population shift. This would even be valid using Cre-lines with random endothelial recombination in all vascular segments (Jin et al., 2022).

If deemed necessary, we have reporter expression from various stages of recombination in the postnatal retina, as well as in the developing brain, as well as comparison with arterial Cre-lines such a BMX cre. A rather complete characterization could be provided in supplements. However, we would argue that this is not relevant for the present study.

Distance to artery /veins is one parameter the authors are using in their modeling. I'm not sure I understand how they determine it since ECs can original form any place with the venous network, then again they might not.

__Response: __In the computational model we assume an initial distribution that is derived from the distribution at P6, which is shown in Figure 2A (middle panel). In summary, we do not hypothesise any origin of the ECs but start with the experimentally observed distribution at P6. From this starting distribution and for the following time steps we can then compute the exact distances to the closest vein and artery.

SiRNA experiment do not show knock down efficiency, which is probably also heterogenous. I'm not sure if this affects the modeling. In the last set they use HUVECs which is a very specialized "venous" ECs which I would not use for their modelsystem.

__Response: __The knockdown efficiency is shown in the supplementary data, see Figure 5 Supplementary data 2: qPCR knockdown validation. We do not use the in vitro data for the computational modelling, only the distribution in the in vivo data. Vegfr3 is expressed in endothelial tip cells and ECs in the developing vein, as well as in scattered ECs throughout the primitive vascular plexus. Therefore, despite the general limitations of in vitro systems, HUVECs are very similar to the in vivo situation shown in our study. HUVECs, despite being of venous origin, are a very versatile tool for endothelial studies. They express both venous and arterial genes, including dll4 and many components of the notch signalling cascade. Importantly, they are heterogenous, but adapt to media and flow conditions. The medium we use stimulates a microvascular growth pattern, and exposing HUVECs to flow results in transcriptional and proteomic changes that fit well with microvascular responses. Using fully differentiated arterial endothelial cells would not be useful as we are modelling endothelial responses that set in venous and microvascular regions of the vascular plexus in vivo, and stimulate a response that leads to movement towards arteries. We have therefore purposefully chosen and validated this model system.

Significance

I already commented in the above paragraph on this topics

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Referee #3

Evidence, reproducibility and clarity

Summary:

this study uses VEGFR3cre as a lineage tracking system to track venous endothelial cells within the maturing retina postpartum in order to investigate the cues related to sprouting and remodeling of the vascular network. They use complex computation modeling to predict outcome and come with in vivo/vitro observations.

They identify that venous EC move towards the arterial bed with flow and oxygen tensions as critical parameter. It is an impressive study that in principle confirms earlier studies on the role of EC population in sprouting and vascular remodeling however utilizes an interesting cell population based computational approach. Since these finding are pretty new, confirmation with different technologies and approaches is important.

However for more "traditional" vascular biologist it is very difficult to understand and follow particular if not familiar with the data presentation and mathematical modeling. This is a major shortcoming of this manuscript because I feel that if the authors would put more effort to better communicate their findings to a broader community not only enhance the value of their findings but also disseminate their computational approaches to a broader vascular scientist community. I do have a couple of model related comments. The authors are using different models without adequate description. The VEGFR3 is a lymphatic EC tracking model that potential can be used to track venous tip cells in the retina. But this model is not characterized within the retina in the study the author cite. I believe it would be necessary to characterize this model in traditional way before it can be used as described. Distance to artery /veins is one parameter the authors are using in their modeling. I'm not sure I understand how they determine it since ECs can original form any place with the venous network, then again they might not. SiRNA experiment do not show knock down efficiency, which is probably also heterogenous. I'm not sure if this affects the modeling. In the last set they use HUVECs which is a very specialized "venous" ECs which I would not use for their modelsystem

Significance

The VEGFR3 is a lymphatic EC tracking model that potential can be used to track venous tip cells in the retina. But this model is not characterized within the retina in the study the author cite. I believe it would be necessary to characterize this model in traditional way before it can be used as described.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Giese et al., develop a computational model to track the migration of tip and venous endothelial cells (ECs) into developing arteries in the mouse retina. They validate prior studies which have identified important roles of shear stress and VEGFA gradient in driving EC migration and argue through their model that these dual forces shift in their relative influence along the vein-artery axis. Through in vivo lineage tracing in combination with Cre-inducible mouse knockout models, Giese et al., explore the role of Cdc42 and Rac1 in flow-migration coupling. They conclude that Cdc42, and not Rac1, is the primary driver of polarized flow-migration, further confirming this result with in vitro flow experiments involving siRNA depletion of Cdc42. Finally, the authors show that Cdc42 also plays a role in EC migration independent of flow, highlighting that its role in migration is universal and directly related to both actin regulation and cell junction dynamics.

Major Comments:

1. In Figure 1 the authors show retinas from a Vegfr3CreERT2 mouse model and make the claim that Vegfr3 is expressed in ECs in developing veins and tip cells, but not in arteries. Ralf Adam's group has previously shown that while Vegfr3 is more abundant in veins and capillaries than in arteries, expression is not exclusive to these EC subtypes (Ehling 2013). They, along with studies from Christer Betsholtz and Kari Alitalo's groups, show that Vegfr3 is observed in postnatal arteries (Tammela 2008, Ehling 2013). Indeed, from the panels in figure 1 (specifically P6 and P7) and supplemental figure 1, it appears that there may also be low levels of Vegfr3 expression in the arterial branches of postnatal Vegfr3CreERT2 mouse retinas. The authors should consider revising their statement that "ECs in arteries, however, do not express Vegfr3" and provide quantification of the number of GFP-labeled cells in arteries, veins and capillaries for each postnatal time point. Additional lineage tracing from later stages when migration into arteries is halted would be a good control for demonstrating that Vegfr3CreERT2 is not expressed in arteries, further support the authors' argument and conclusions.

2. In their computational simulations, the authors investigate three models: random walking of ECs (M1), VEGFA gradient driven migration (M2), and integrated VEGFA /shear-stress driven migration (M3). The reader naturally wonders why a model considering only shear-stress driven migration is not presented as a control simulation. The absence of this model reduces the strength of the claims that only the M3 model captures observed EC movement rates, the mean population shift in vein-artery distance, and the arterial proportion of ECs.

3. Much of the terminology in this study needs more detailed explanation and carefully usage. It would be more friendly to readers if they were consolidated into a box figure or table. (For example, how is coupling strength related or different from coupling rate?) The reported numbers of these factors are noted separately in text here and there. It would be helpful to put them together to highlight the difference between different models and mutant strains, as this is one of the novel findings for this study.

4. The lack of labelled cells in the P9 retinas of Cdc42iECKO mice is striking (Figure 3), and strong evidence for the importance of Cdc42 in the migration of ECs towards arteries. The authors cite Lavina et al, 2018 when they note that Cdc42 depleted ECs proliferate at normal rates, but independent verification of this observation through EdU quantification would allow the authors to distinguish between the two possibilities outlined on page 15 of the manuscript: local proliferation vs enhanced migration of non-recombined ECs. These experiments and analyses are expected to be quick (depending on the availability of mice) and low cost. An independent EC proliferation analysis would also give the authors insight into the degree to which localized proliferation likely impacts vein-artery migration, a parameter which is currently unaccounted for in their computational model. The authors recognize that the lack of EC proliferation parameters is a limitation of their current model and speculate that this makes their estimates of vein to artery migration slightly too low. Independent EC proliferation analysis would thus be informative and may allow the authors to remove this speculation from their discussion.

5. In the legends of Figure 1B & C, no information about the x or y-axis were mentioned. Even though the authors explained it elsewhere in the text or other figures, it is the first time that these parameters show up in the paper, which would be a proper place to note the details of these KDE plots.

6. In the legends of Figure 2B & C, it mentioned the results of coupling strength and fraction of shear stress, which was not obvious by just looking at the figures provided. It is also not mentioned whether the numbers are calculated by collected or predicted data.

7. Please direct the reader to the supplemental figure containing the tamoxifen injection strategy when the Vegfr3CreERT2 mouse model is introduced in the text and when Cdc42 and Rac1 EC knockout is discussed in the methods.

8. There appears to be a significant degree of variance in the KDE plots from Figures 1, 3, and 4. It would therefore be helpful if the authors could include plots of the remodeling plexus and sprouting front that show the median for each dataset (similar to Figure 1 D and E), since this is less likely to be skewed by extrema. Additionally, for clarity and ease to read, it would be nice if author can consolidate the results of the mean from WT, Cdc42 and Rac 1 iECKO side by side. The images of the retina are striking, but the quantification is not as well-communicated. If the argument is that Cdc42 only disrupts the migration, but not the differentiation, of artery EC, the authors should see a significant difference between WT and Cdc42 iECKO only in P9, but not early stages.

Minor Comments:

1. For KDE plots in Figure 1B and Figure 3B, the authors labeled the x-axis differently (r vs dr). No description about the x-axis is noted in the legends. Please consider keeping the label consistent so the readers can relate and compare them.

2. For the in vitro study, the cell line used is not mentioned in the results, even though there is a method section about HUVEC. Authors should note this information in the main text.

3. Please note the flow direction in Figure 5B.

4. The naming of supplemental figures requires revisiting. Currently there are two figures labeled with variations of supplementary Figure 1, which makes identifying the correct data challenging.

5. There appears to be a small typo on page 16 in second paragraph in the sentence that currently reads "Nevertheless, only few cells reached the arteries by P9"

6. The axis labels for the plots in Figure 5, Figure 2 Supplement 1, and Supplementary Figure 2 are currently very tiny and difficult to read.

7. Additional information is required to describe the trajectory plots in Figure 2 Supplement 1, Figure 3 Supplement 3 and Figure 4 Supplement 3. I assume that blue trajectories move in the positive x direction while orange trajectories move in the negative x direction, but this is currently not specified in any of the legends.

Significance

Giese et al advance current understanding of the molecular mechanisms that guide vein to artery migration by convincingly demonstrating (both in-vivo and in-vitro) that Cdc42 is essential for this process. In addition, they present a computational model that captures the dual force field of VEGFA and shear stress gradients to simulate and quantify this migratory process in the mouse retina: a tool which will likely be useful for future mechanistic studies of vascular remodeling and EC migration. As far as I am aware, no standard coordinate system exists in the field for the quantification and modeling of this migratory process, so the introduction of this method alone serves as a useful innovation for the field of vascular biology.

• It should be noted by authors and the editors that the mathematical details of the computational model and its statistical accuracies are not evaluated in this review, which instead focuses on the study's findings as they relate to EC biology and vascular development.

• This study complements previous work that has identified populations of ECs that appear to be primed for incorporation into arteries, termed "pre-arteries" (Su et al 2018, Phansalkar 2021, Luo 2021). The authors' observation of heterogeneous EC movements during migration supports the intriguing suggestion that actin regulation through Cdc42 may be related to the establishment or phenotype of this pre-artery identity, though further mechanistic work will be required to validate this hypothesis, as noted by Giese et al in their thoughtful discussion.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Giese et al. use genetic lineage tracing techniques and novel computational analysis methods to quantify and predict how the spatial distribution of ECs changes over time in the developing mouse retina from P5 to P9. They also develop mathematical models to describe and predict the response of ECs to the hypothesized dual force-field formed by the chemoattractant VEGFA, and the flow-induced shear stress. Given that the mouse retina cannot be live imaged, these new methods are essential to infer cell dynamics from static images. With these methods the authors confirm previous findings that arteries are formed by endothelial cells derived from veins, or tip cells, or capillaries. They then combine their genetic system with Cdc42 and Rac1 floxed alleles to understand the function of these genes in EC mobilization. They find that Cdc42 has a very strong role in EC mobilization to arteries, not so much to the sprouting front, whereas the loss of Rac1 has relatively minor effects in vivo. Loss of Rac1 slows the cells but they maintain their directionality towards arteries. The discussion section and integration of these paper findings with previous work in the field is excellent. Overall, this work provides a much higher level of quantitative analysis of endothelial cell dynamics in the developing vasculature of the mouse retina. It also provides mathematical models that can be useful to explain and predict the impact of other genetic mutations or pharmacological interventions during vascular development.

Major comments:

1 - This work provides one of the finest examples of quantitative biology in the vascular biology field. The conclusion on cell dynamics is however largely based on static images measurements and pre-defined mathematical models given also previous work and the proposed model of a dual-force field. The authors conclude that sprouting front cells mainly migrate away towards VEGF, whereas remodelling plexus cells migrate towards arteries. However, this is based on the entire EC population measurements/displacement and averaging, and does not account for the possibility of a few ECs having a different behaviour from most of their neighbours. This comment is related with the fact that arteries are formed mainly by tip-derived ECs, the cells closest to the VEGF source and further away from the flow/shear stress force. It seems the authors model presented here would not allow this to happen. According to the model presented, it seems that an EC close to the VEGF source, and subjected to low flow (shear stress), would always migrate to the front and never turn back towards arteries. Can a more complex model enable the consideration of the stochastic loss of VEGF signalling (or gain of shear stress sensing) by some ECs at the sprouting front ? And their subsequent formation of arteries ?

2 - Previous work by Laviña et al showed that Cdc42 is required for the migration of ECs to the sprouting front. The authors data suggest that Cdc42 is not necessary for this process. Could the difference between previous and the authors results be technical and related with the different stage of induction/analysis or the extent of Cdc42 deletion ? Did the authors tried inducing at P1 and collecting at P6/P7 ? The reporters used were also different and they may have different sensitivities to tamoxifen (and hence report Cdc42 deletion differently).

3 - In the last section, some of the junctional/polarity/actin markers and analysis done in vitro could be also done in vivo.

4 - The extent of Rac1 deletion in the mosaic experiments (done with suboptimal doses of tamoxifen) could be analysed. This is especially relevant since minor effects for Rac1 were observed in these in vivo experiments.

Minor comments:

1 - Lee et al., 2022 is a review. Better cite the original papers if possible: Some examples: Xu et al., 2014, Pitulescu et al 2017 and Lee et al., 2021.

2 - Figure 1A: Stage of induction with tamoxifen is missing. Likely P5.

3 - Figure 3 and 4 data would be easier to compare/understand by readers if part of the Wt data in Figure 1 was also plotted here. Or at least a Wt trend/average line on top of the mutant data, for us to see how much Cdc42 or Rac1 deletion changes the behaviour of the mutant cells versus the Wt cells.

4 - Overall, for all dot plots and heatmaps, would be better to indicate the total number of cells analysed/plotted since the power of the analysis is related with cell number rather than number of retinas.

Significance

Significance

General assessment: This paper is very strong on the quantitative analysis and mathematical modelling. Methods used and the model proposed may be of broad relevance for the field of vascular biology. It is however based on certain author-defined parameters and assumptions. EC dynamics in vivo can be much more complex than what can be modelled by equations. For example, heterogenous single cell genetics and signalling inputs can induce changes in cells that override the normal/average behaviour of the cells that are modelled. Despite the high level of quantitative analysis and modelling, the main findings here presented are not entirely novel, given previous work. For example, it was previously known that arteries are formed by vein/tip/capillary cells. It was also known that Cdc42 was required for proper EC migration away from veins (Laviña et al., 2018). However, the better quantitative analysis here presented does provide a higher level of detail and reliability. The mosaic genetics used to delete Cdc42 is in general clear since few reporter positive cells can make arteries, suggesting efficient deletion of this gene. The data also goes in line with previous work. However for Rac1, given that a much weaker phenotype was observed, is not possible to be sure that all GFP+ ECs had deletion of Rac1. This is especially important in mosaic genetic experiments, using a suboptimal dose of tamoxifen. The extent of Rac1 deletion in GFP+ cells was not analysed. Which leaves the open question if Rac1 is really dispensable for EC migration and arterialization. Embryos lacking Rac1 in endothelial cells die early during development. Therefore ECs fully lacking Rac1 may have stronger defects than the ones shown here. All this data was obtained in the postnatal retina angiogenesis system. Other organ vessels may develop differently. Future work will tell if the models proposed can explain the dynamics of ECs during the growth of other vascular beds.

Audience: Vascular/Cell biology researchers and bioinformaticians developing tools for image analysis and/or cell migration/dynamics modelling.

Expertise of Reviewer: Vascular Biology. I do not have sufficient expertise to evaluate the mathematical modelling part of this paper.

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Reply to the reviewers

Planned Revisions based on comments from Reviewer #1

• The introductory material and the title of the paper emphasize the ring canal scaling question. This problem is somewhat obscured in the text by the side problem of nuclear scaling, which comes up frequently even though the results are not as thoroughly explored. Could the authors think about moving these data into a different, single figure for the sake of coherence? This is not a required revision. Just a thought.
• *We have moved the nuclear scaling data from Fig. 5 into Fig. S3, and once we have analyzed the data from the planned experiments (over-expressing either HtsRC or the active form of myosin), then we will have a better idea of whether we should move the rest of the nuclear scaling data out of the main part of the paper, consolidate it into a single figure (as Reviewer #1 suggests), or keep some of it in the main figures. *

Planned Revisions based on comments from Reviewer #3

• I cannot see differences in RC size in the panel A images. More importantly, this method altering ring canal size is limited. A more direct way is overexpression of HtsRC (https://doi.org/10.1534/genetics.120.303629).
• We have requested and just recently received the line to over-express HtsRC in the germline. We plan to cross this UAS line to the mataTub-GAL4 which expresses GAL4 beginning around stage 3 of oogenesis. Because crossing this UAS line with this GAL4 line produced egg chambers with larger ring canals in the original study2*, we do not anticipate any technical issues with this experiment. We will incorporate the results from analysis of these egg chambers in the revised manuscript. *

• To further explore the effect of ring canal size on scaling, we will also be testing a condition that we hope will have the opposite effect on ring canal size; expression of a phosphomimetic version of the non-muscle myosin II regulatory light chain, encoded by spaghetti squash (Sqh)(UAS-sqhE20E21). We plan to cross this UAS line to two different GAL4 drivers (nos-GAL4, which expresses GAL4 in a pulse during early oogenesis and then in another pulse in mid-oogenesis and the mataTub-GAL4 which expresses GAL4 beginning around stage 3 of oogenesis). We know that expression of sqhE20E21will reduce the size of the ring canals that connect the nurse cells to each other, but it is possible that the posterior ring canals will not show a strong phenotype. In a study that looked at egg chambers homozygous for a mutation in the myosin binding subunit of the myosin phosphatase, DMYPT, which should also increase sqh phosphorylation, it was shown that the posterior ring canals were larger than those connecting nurse cells 1*. Therefore, it is possible that this condition may not allow us to consistently reduce the size of all ring canal types; however, if we do see a significant reduction in posterior ring canal size in these egg chambers, we will include these data in the revised manuscript. *

• In panel 2E, it would be helpful to plot the y-intercepts separately, too.

• Based on the analysis of the data from the proposed experiments, we will consider plotting the y-intercepts separately for the various conditions.

1. Description of the revisions that have already been incorporated in the transferred manuscript

Revisions made based on comments from Reviewer #1

• One way to think about the dhc-64C experiments presented in Figure 2 is that they are meant to test the hypothesis that ring canal size impacts scaling in such a way that transport across the four ring canals tends towards equilibrium over time. One possibility would therefore be that ring canals aren't programmed to grow to a particular final size but rather they grow at different rates until their diameters are the same. This seems to me an important distinction. It might be made by analysis of the arpC2-RNAi cells, since those ring canals are meant to be initially larger. Unfortunately, I can't see the answer.
• *Reviewer #3 suggested determining the ratio of the diameter of the M1 ring canal to the M4 ring canal. If ring canals grow toward equilibrium (to achieve a similar final size), then we would expect to see this ratio approach 1; when we performed this analysis, we saw that the ratio did decrease as the egg chambers increased in volume, but it never quite reaches a ratio of 1. We have added a supplemental figure (Fig. S1) showing these data and incorporated this idea into the text within the results and discussion sections. *
• *Although it would be informative to determine whether ring canals that all started with a similar diameter would grow at the same rate, we have not found a condition that would provide the opportunity to test this hypothesis. We hope that the planned experiments will provide us with a way to test this hypothesis; we will determine the M1/M4 ratio in egg chambers over-expressing either HtsRC or sqhE20E21 and see whether this ratio still decreases as egg chamber volume increases. *

• *Once we perform the planned experiments to either increase or decrease ring canal size, then we can determine whether we need to further modify Fig. 3 to highlight these size differences between ring canals in the arpC2-RNAi egg chambers or whether we will instead focus more on the results of the planned experiments. *

• The authors write that arpC2-RNAi "ring canals tended to be larger than those in similarly-sized control egg chambers," but that conclusion isn't obvious to me from the data in Figure 3B. The only difference I can see is that the M4 ring canals look to be consistently smaller in the experimental versus control egg chambers, especially at the final timepoint.

• *To further clarify the difference in ring canal size between the control and the arpC2-RNAi egg chambers, we have added additional explanation to the results section to highlight that the y-intercepts of the lines of best fit are significantly higher in the arpC2-RNAi egg chambers at each stage. This demonstrates that given an egg chamber volume, the ring canals will be larger in egg chambers depleted of ArpC2 than in the controls. *

• The authors write that "there was a consistent, but not significant decrease in the scaling exponents for the arpC2-RNAi egg chambers compared to controls," but I don't see this in the M1 (identical) or M2 (almost the same) ring canals. The scaling decrease is most pronounced at M4. All the other ring canals seem to reach a final size that's equivalent to controls. What does this tell us about scaling? Is the M4 more sensitive to the effect of arpC2-RNAi? I note and appreciate that the data for M4 show a wide distribution and might have been impacted by outliers, which could be discussed.

• *We have separated the arpC2-RNAI ring canal scaling data by lineage (Fig. S2), and we have color-coded the data in Fig. 3B (as suggested by Reviewer #3). *

• We have expanded the discussion of these results and their implications, and we have added a line in the results section to address this wide distribution of the M4 ring canal sizes.

• The possibility that ring canal scaling "could generate eggs of different sizes" could use some elaboration (at least) as it does not seem to be especially well supported:

• Only one of the small egg lines had lower scaling exponents than the big egg lines, and it's a struggle for me to understand the extent of that difference based on the data shown. (Is it significant?).

• *We have restructured this section of the results and modified Fig. 5 to highlight similarities and differences between the four lines. In the results section (and in the figure legend), we have stated that when we compared the slopes of the regression lines for all four lines, there was a significant difference for M1, M2, and M4 (Fig. 5C, D, and F). We have also modified the results section to highlight that although the slopes for line 9.31.4 was not different from the two big egg lines, the intercepts were significantly different for M1, M2, M3, and M4 ring canals. We moved the nuclear scaling data to Fig. S3 to simplify the figure. *

• The authors conclude that "the effect of lineage on ring canal scaling is conserved, and it suggests that at least in one line, reducing posterior ring canal scaling could provide a mechanism to produce a smaller mature egg." The first part of this sentence is confusing for me since I don't know what is meant here by "conserved." The second part of the sentence is technically correct but disguises what I would consider the more meaningful and exciting finding. The 9.31.4 line produces the smallest eggs but does not demonstrate scaling differences in comparison to the big egg lines examined (1.40.1 and 3.34.1). The authors have therefore avoided/solved a "chicken and egg" ("fruit fly and egg"?) problem by showing that scaling and egg size can be decoupled!

• We have modified the first part of the sentence to clarify our point. We appreciate this suggestion and have modified the text in the results section to further elaborate on the results.

• This point is not made very clearly in the discussion, which concludes with the suggestion that scaling could help explain why some insects produce much larger or much smaller eggs that fruit flies. I can only understand this to be the case if - as the authors point out - scaling "affect the directed transfer of materials into the oocyte." That argument seems predicated on the possibility that these insects make the same amount of initial material then regulate how much is transferred. Seems like a costly way to go about it.

• *We have modified this section of the discussion. *

• I really had to look very closely to distinguish the little blue boxes from the little blue circles in panels 2C and especially 2D. I suggest using a different color instead of a different shape, or maybe splitting the graphs up.

• *We have made the shapes larger in Fig. 2C (nuclear sizes), and we have split the ring canal size data into Fig. 2D, E and made the shapes larger. The legend has been modified to reflect this change. *

• "Depletion of the linker protein, Short stop (Shot), or dynein heavy chain (Dhc64C), significantly reduced the biased transport at the posterior, which reduced oocyte size (Lu et al., 2021)." I suggest this sentence might be clearer if it was rewritten as "Depletion of either dynein heavy chain (Dhc64C) or the linker protein Short stop (Shot) significantly reduces biased transport at the posterior, in turn reducing oocyte size (Lu et al., 2021).

• We have made this change.

• "Because nuclear growth has been shown to be tightly coupled to cell growth (Diegmiller et al., 2021), we can use nuclear size as a proxy for nurse cell size." I think it would help the reader to know that the Diegmiller study was performed using germline cysts in the Drosophila ovary; I paused when I got to this sentence because I initially read it as overly broad. I suggest "Recent work in demonstrates that nuclear growth is tightly coupled to cell growth in this system (Diegmiller et al., 2021), and we can therefore use nuclear size as a proxy for nurse cell size" or similar. This is certainly not a required revision, just a suggestion.

• We have made this change.

Planned Revisions based on comments from Reviewer #3

• Reviewer #3 asked: Does the ratio of the diameter of M1 to M4 stay the same?

• *We have performed this analysis in the control egg chambers (from Fig. 1), and we found that the ratio does not stay the same, but that it tends to decrease as the egg chamber increases in volume. We plotted the log of egg chamber volume versus this ratio, and the equation for the regression line was y = -0.166x + 2.32, which was significantly different from a slope of 0 (included in Fig. S1). *

• It would be helpful to explain that the log-log plots were used to derive a line equation (y=mx + b) and why that is useful in this context. In the case of a log-log plot, what does the y-intercept mean biologically? Is it simply a way to compare two things or does it indicate real measurements such as volume or ring canal size? Also, the slope of the line is being used as a scaling value. Be careful to define the terms "scaling" and "scaling exponent".

• We have added additional explanation in the results section.

• Are four significant digits called for in calculating slope? The figure has 4 significant digits, the text has three.

• *We have modified all figures and text to include only 3 significant digits. *

• Why is isometric scaling 0.66 - is that microns squared over microns cubed? Please explain.

• We have added additional explanation to the results section.

• Were all four posterior nuclei measured? The figure indicates just M1 and M4.

• We apologize that it was not clear that all four posterior nuclei were measured in Fig. 1. For the sake of space, we only showed images of the M1, M4, and Anterior ring canals and nuclei (in Fig. 1A), but all four nuclear measurements were included in the graph in Fig. 1B. We have added M1-M4 to the legend to clarify and revised the text of the legend.

• It is hard to explain why all four posterior nuclei are bigger than anterior when one of the four is the same age as the anterior nucleus.

• The posterior nuclei are larger than the anterior nuclei due to their proximity to the oocyte. Multiple recent studies have described this hierarchical nurse cell size relationship in which the nurse cells closest to the oocyte are larger than those separated from the oocyte by additional intercellular bridges 3–5*. *

• In panel D, a conclusion is, "Further, the scaling exponent [slope] for the anterior ring canals, which are also formed during the fourth mitotic division, was not significantly different from that of the posterior M4 ring canals". Anterior is 0.23, M4 is 0.25. These seem different to me. How is significance determined? Were any of the scaling exponents in M1, M2, M3, M4 or Anterior significantly different?

• *Significance was determined within the Prism software using a method equivalent to an ANCOVA. If the slopes are compared, M1 is significantly different from M2, M3, and M4, and M2 is significantly different from M4. M4 is not significantly different from the slope for the anterior ring canals, which supports the correlation between scaling and lineage. *

• References are needed for the statements about biased transport to the oocyte.

• *There was a reference to the Lu (2021) paper in that paragraph, but we have added an additional reference to that paper to this part of the results section. *

• In panel 2C, why are the scaling exponents (slopes) of the controls bigger than in Figure 1B? The controls look hyper allometric in Fig. 2.

• *This experiment was done with a different GAL4 driver, so it is possible that there are some differences in scaling based on genetic background. *

• In panel 2D it is impossible to pick out the control posterior vs anterior lines - use different colors as in Figure 1. Why do the control lines for posterior and anterior merge?

• *We have split the ring canal scaling data from Fig. 2D into different separate panels (Fig. 2D,E), as suggested by Reviewer #1. *

• These lines likely approach each other because the slope of the line for the anterior ring canals (M4 type) is always larger than the slope for the combined posterior ring canals.

• Re: Fig. 3: Scaling of what? RC size?

• *We assume that this comment is related to the heading for this section of the results, so we have added “ring canal to the end of this title, so that it now reads: “Increasing initial ring canal size does not dramatically alter ring canal scaling” *

• Since there was no effect, "dramatically" should be deleted from the section title.

• This change has been made.

• Clarify this sentence: If ring canal size inversely correlates with scaling, then increasing initial ring canal diameter should reduce the scaling exponent.

• We have made this change in the text.

• How does panel B show that RCs are larger in arpC2 KD? Fig. S1A has smaller y-intercept for control. Again, it is impossible to see which lines go with which M and which genotype.

• *As mentioned above, we have modified Fig. 3 to highlight these differences and added additional explanation to the results section. *

• Panels 4D & 4G are clear - should include significance indications.

• *We have added asterisks to indicate significant differences. *

• The conclusion from panels 5B and 5C that reducing RC scaling could lead to smaller mature eggs is a stretch. Without looking at the rest of the lines these data are preliminary and detract from the rest of the paper.

• *As suggested by Reviewer #1, we have modified the results and discussion sections, and we have added a statement about the need for analysis of additional lines. *

2. Description of analyses that authors prefer not to carry out

Comment from Reviewer #2

• I am surprised that the author has not considered controlling the impact of cell cycle regulation on this scaling process, especially as the work of Dorherty et al. has shown that this type of regulation is essential for regulating the size of nurse cell nuclei. The authors should test the impact of at least dacapo and cyclin E in this process.
• We have attempted to deplete Dacapo from the germline by crossing two different RNAi lines to multiple germline drivers; however, we have been unable to see a consistent effect on nurse cell nuclear size, which suggests that these RNAi lines may not effectively reduce Dacapo protein in the germline. Although we agree with the reviewer that this is an obvious mechanism that should be explored, we believe that it is not necessary for it to be included in this manuscript, because altering Dacapo levels in the germline would not provide a mechanism to explain our model that ring canal lineage impacts ring canal scaling. Dacapo has been shown to contribute to the hierarchical pattern of nurse cell size observed in the germline. Dacapo mRNA produced in the nurse cells is transported into the oocyte, where it is translated. Then, the Dacapo protein diffuses back into the nurse cells, producing a posterior to anterior gradient 4. Doherty (2021) showed that reducing the levels of the Dacapo protein using the deGradFP system eliminated the nurse cell size hierarchy. If our data had supported a model in which proximity to the oocyte was a strong predictor of ring canal size and scaling (as shown for the nurse cells and their nuclei3,5*), then this would have been an excellent way to dig further into the mechanism. Instead, our data supported a role for ring canal lineage in predicting ring canal growth, since the M4 ring canals at the posterior and anterior showed similar scaling with egg chamber volume. *
• We believe that performing the proposed experiments (over-expressing HtsRC to increase ring canal size or expressing the phosphomimetic form of the myosin regulatory light chain, sqhE20,E21 to reduce ring canal size) will allow us to determine how ring canal size affects scaling, which will provide additional mechanistic insight into this scaling behavior.*

*

Comment from Reviewer #3

• Panel 3E is interesting and would fit better in Figure 1.
• *This panel is from a different genetic background than the data in Fig. 1. Therefore, we do not think it would be appropriate to move it to Fig. 1. *

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Referee #3

Evidence, reproducibility and clarity

Coordinating subcellular size of organelles is important for normal cell function. This research investigates how the size of intercellular bridges called ring canals in Drosophila egg chambers is regulated. The work builds on previous research in Change Tan's lab that reported ring canal size varies by lineage - the ring canal from the first germ cell mitotic division (M1) is larger than those resulting in subsequent divisions during egg chamber formation. Shaikh et al. probe this linkage between lineage and ring canal size during egg chamber development by testing the relationship with flow through the ring canals, initial ring canal size, and number of mitotic divisions. They also investigate whether ring canal size per se affects egg size. The quantification is carefully done.

The results strongly reinforce the overall conclusion that lineage is the main driver of ring canal size. They report that growth of younger ring canals is slightly faster than old ones, suggesting a "catch-up" mechanism. However, neither the flow through ring canals nor their initial size has an apparent effect on the relationship with lineage.

General comments:

The authors derive scaling relationships between nurse cell or ring canal size and egg chamber volume to address their hypotheses. The most interesting observation is the relatively accelerated growth of young versus old ring canals attaching the oocyte to nurse cells, each from a different mitosis. Another perhaps simpler way to do this is to determine the ratios of the diameters of M1 to M4 ring canals as egg chambers develop. Does the ratio stay the same?

Specific comments:

Fig. 1:

1. For those who forgot their algebra, it would be helpful to explain that the log-log plots were used to derive a line equation (y=mx + b) and why that is useful in this context. In the case of a log-log plot, what does the y-intercept mean biologically? Is it simply a way to compare two things or does it indicate real measurements such as volume or ring canal size? Also, the slope of the line is being used as a scaling value. Be careful to define the terms "scaling" and "scaling exponent".
2. Are four significant digits called for in calculating slope? The figure has 4 significant digits, the text has three.
3. Why is isometric scaling 0.66 - is that microns squared over microns cubed? Please explain.
4. Were all four posterior nuclei measured? The figure indicates just M1 and M4. It is hard to explain why all four posterior nuclei are bigger than anterior when one of the four is the same age as the anterior nucleus.
5. In panel D, a conclusion is, "Further, the scaling exponent [slope] for the anterior ring canals, which are also formed during the fourth mitotic division, was not significantly different from that of the posterior M4 ring canals". Anterior is 0.23, M4 is 0.25. These seem different to me. How is significance determined? Were any of the scaling exponents in M1, M2, M3, M4 or Anterior significantly different? Fig. 2: Less flow through M4 drives faster RC growth? No.
6. References are needed for the statements about biased transport to the oocyte.
7. In panel C, why are the scaling exponents (slopes) of the controls bigger than in Figure 1B? The controls look hyper allometric in Fig. 2.
8. In panel D it is impossible to pick out the control posterior vs anterior lines - use different colors as in Figure 1. Why do the control lines for posterior and anterior merge?
9. In pane E, it would be helpful to plot the y-intercepts separately, too. Fig. 3: increasing initial RC size does not dramatically alter scaling.
10. Scaling of what? RC size?
11. Since there was no effect, "dramatically" should be deleted from the section title.
12. Clarify this sentence: If ring canal size inversely correlates with scaling, then increasing initial ring canal diameter should reduce the scaling exponent.
13. I cannot see differences in RC size in the panel A images. More importantly, this method altering ring canal size is limited. A more direct way is overexpression of HtsRC (https://doi.org/10.1534/genetics.120.303629).
14. How does panel B show that RCs are larger in arpC2 KD? Fig. S1A has smaller y-intercept for control. Again, it is impossible to see which lines go with which M and which genotype.
15. Panel E is interesting and would fit better in Figure 1.

Fig. 4: Additional mitotic division doesn't affect RC or nuclear scaling. 16. Panels D & G are clear - should include significance indications.

Fig. 5: small and big lines 17. The conclusion from panels B and C that reducing RC scaling could lead to smaller mature eggs is a stretch. Without looking at the rest of the lines these data are preliminary and detract from the rest of the paper.

Significance

Overall, this work is an extension and reinforcement of information previously available rather than providing significant new insight. Researchers in Drosophila oogenesis will be interested.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Umayr Shaikh and colleagues study the evolution of the size of subcellular structures during tissue growth. To do this, the authors use the Drosophila egg chamber as a model system, studying the growth rate of the intercellular bridges, also known as ring canals, connecting the oocyte to the nurse cells and the growth rate of the nurse cell nuclei during the development of the egg chamber. In particular, they focused their study on the ring canals and the nuclei of the 4 nurse cells, both of which are in direct contact with the oocyte but have a different lineage history. They show that first born ring canal ring grow more slowly than smaller ring canal that are the result of subsequent mitotic divisions. This scaling process is maintained when polarised transport between the nurse cells and the oocyte is reduced by decreasing the level of dynein. They demonstrate that manipulation of the size of the ring canals by arpC2 RNAi does not radically alter scaling. Furthermore, by inactivating an uncharacterised gene CG34200, they show that additional mitotic division does not affect the scaling of the annular canal and nucleus.

Significance

Major comment

These results are based on new and original observations. The results are clear and well documented. However, this work is very descriptive in its current state and in the absence of a mechanism for this lineage-based scaling process.

I am surprised that the author has not considered controlling the impact of cell cycle regulation on this scaling process, especially as the work of Dorherty et al. has shown that this type of regulation is essential for regulating the size of nurse cell nuclei. The authors should test the impact of at least dacapo and cyclin E in this process.

Without a mechanism for the scaling process, this manuscript is more suitable for a specialize journal

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Referee #1

Evidence, reproducibility and clarity

The relationship between nuclear size and cell size has received a lot of attention. Less well-recognized is the problem of how other structures within the cell scale with size. This is a good question and the authors have a nice system - Drosophila female germline cysts - in which to study it. Here the authors show that lineage impacts ring canal scaling. This is an interesting finding that makes for neat biology; a simple way to think about it is that older ring canals have more time to mature (grow) than younger ones. The manuscript is beautifully and carefully written! It was fun to read. The experiments are straightforward, performed to a high standard, and generally well-presented.

Comments:

One way to think about the dhc-64C experiments presented in Figure 2 is that they are meant to test the hypothesis that ring canal size impacts scaling in such a way that transport across the four ring canals tends towards equilibrium over time. One possibility would therefore be that ring canals aren't programmed to grow to a particular final size but rather they grow at different rates until their diameters are the same. This seems to me an important distinction. It might be made by analysis of the arpC2-RNAi cells, since those ring canals are meant to be initially larger. Unfortunately I can't see the answer. The authors write that arpC2-RNAi "ring canals tended to be larger than those in similarly-sized control egg chambers," but that conclusion isn't obvious to me from the data in Figure 3B. The only difference I can see is that the M4 ring canals look to be consistently smaller in the experimental versus control egg chambers, especially at the final timepoint. Related to this concern, the authors write that "there was a consistent, but not significant decrease in the scaling exponents for the arpC2-RNAi egg chambers compared to controls," but I don't see this in the M1 (identical) or M2 (almost the same) ring canals. The scaling decrease is most pronounced at M4. All of the other ring canals seem to reach a final size that's equivalent to controls. What does this tell us about scaling? Is the M4 more sensitive to the effect of arpC2-RNAi? I note and appreciate that the data for M4 show a wide distribution and might have been impacted by outliers, which could be discussed.

The possibility that ring canal scaling "could generate eggs of different sizes" could use some elaboration (at least) as it does not seem to be especially well supported:

• Only one of the small egg lines had lower scaling exponents than the big egg lines, and it's a struggle for me to understand the extent of that difference based on the data shown. (Is it significant?).
• The authors conclude that "the effect of lineage on ring canal scaling is conserved, and it suggests that at least in one line, reducing posterior ring canal scaling could provide a mechanism to produce a smaller mature egg." The first part of this sentence is confusing for me since I don't know what is meant here by "conserved." The second part of the sentence is technically correct but disguises what I would consider the more meaningful and exciting finding. The 9.31.4 line produces the smallest eggs but does not demonstrate scaling differences in comparison to the big egg lines examined (91.40.1 and 3.34.1). The authors have therefore avoided/solved a "chicken and egg" ("fruit fly and egg"?) problem by showing that scaling and egg size can be decoupled!
• This point is not made very clearly in the discussion, which concludes with the suggestion that scaling could help explain why some insects produce much larger or much smaller eggs that fruit flies. I can only understand this to be the case if - as the authors point out - scaling "affect[s] the directed transfer of materials into the oocyte." That argument seems predicated on the possibility that these insects make the same amount of initial material then regulate how much is transferred. Seems like a costly way to go about it.

Minor comments:

I really had to look very closely to distinguish the little blue boxes from the little blue circles in panels 2C and especially 2D. I suggest using a different color instead of a different shape, or maybe splitting the graphs up.

The introductory material and the title of the paper emphasize the ring canal scaling question. This problem is somewhat obscured in the text by the side problem of nuclear scaling, which comes up frequently even though the results are not as thoroughly explored. Could the authors think about moving these data into a different, single figure for the sake of coherence? This is not a required revision. Just a thought.

I have two trivial comments regarding sentence structure in the text: "Depletion of the linker protein, Short stop (Shot), or dynein heavy chain (Dhc64C), significantly reduced the biased transport at the posterior, which reduced oocyte size (Lu et al., 2021)." I suggest this sentence might be clearer if it was rewritten as "Depletion of either dynein heavy chain (Dhc64C) or the linker protein Short stop (Shot) significantly reduces biased transport at the posterior, in turn reducing oocyte size (Lu et al., 2021).

"Because nuclear growth has been shown to be tightly coupled to cell growth (Diegmiller et al., 2021), we can use nuclear size as a proxy for nurse cell size." I think it would help the reader to know that the Diegmiller study was performed using germline cysts in the Drosophila ovary; I paused when I got to this sentence because I initially read it as overly broad. I suggest "Recent work in demonstrates that nuclear growth is tightly coupled to cell growth in this system (Diegmiller et al., 2021), and we can therefore use nuclear size as a proxy for nurse cell size" or similar. This is certainly not a required revision, just a suggestion.

Significance

The manuscript is beautifully and carefully written! It was fun to read. The experiments are straightforward, performed to a high standard, and generally well-presented. The problem it addresses is an important/useful complement to other studies on the relationship between nuclear size and cell size. The paper identifies and characterizes differential scaling of ring canals, raising exciting mechanistic questions that can be addressed in future studies. I think it will be of interest to an audience cell and developmental biologists.

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Reply to the reviewers

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

*

*Major comments: 1. Mirc56_2 and 4 showed lower integration rates, and the authors suggest that this could be due to sgRNA pool imbalance. The authors should validate this by performing sequencing of the input sgRNA and cassettes. *

→Thank you very much for your comment, and we agree with your suggestion.

We are going to confirm sgRNA pool imbalance in donor vector library by amplicon short-read NGS.

In addition, to confirm another possibility that we raised, we re-sequenced sgRNA donor vector for Mirc56_2 and 4, and will add the following sentences:

“We firstly doubted that their low integration frequencies were caused by any mutations on PB transposon of sgRNA donor vector, on especially ITR or ID that are important for integration efficiency [PMID: 15663772]. Therefore, we sequenced PB transposons for Mirc56_2 and 4 again. However, we could not find any mutations on their PB transposon.” following to “…efficiency or cell growth.” in the Discussion (page14, line 346)

*2. Clonal analysis in Figure 5c is unclear a. Figure 5c indicates that all changes were homozygous (e.g. both alleles were deleted). Was this the case in all clones? Or were some mutations heterozygous? *

→Thank you very much for your comment.

We apologize for the misleading context.

We targeted mono allele on X chromosome in male mES cells so that all mutations should be hemizygous as mentioned in the Result (page11, line 259-260)

To enhance our study is monoallelic assessment, we will add the following sentence:

“This study targeted mono allele on X chromosome in male mES cells so that all genotype on Mirc56 should be hemizygous and these mutations induced might be cis-mutation.” following to“…owing to six tandem repeats [37]” in the Result (page12, line 302)

*b. Many clones in Figure 5c show that the entire region was deleted (all black dots). Could this be due to some experimental error or misinterpretation of the sequencing data, or could it be validated using some orthogonal method? This is especially surprising for clones in which the final guide (Mirc56_13) was not detected yet the final site (Mirc56_13) was reported as "Regional deletion". *

→Thank you very much for your comment.

We apologize for the misleading context.

Firstly, we just confirmed and sequenced the mature-miRNA genomic regions by amplifying approximately 200 bp around the target sites. Therefore, we defined unamplified regions as “miRNA deletion”. In addition, to make the Figure 5C easy to understand, we added “predicted regional deletion” and each name of clones as attached.

In fact, only 4 clones harbored entire Mirc56_X deletions on all analysed Mirc56_X genomic region (Mirc56_1 to 13). Besides, these clones could be PCR-amplified by sgRNA cassettes and Sry on Y chromosome so that these results suggested we could successfully obtain their genomic DNA and at least mature-miRNA genomic regions were deleted.

Moreover, Mirc56_13 deletions without target sites on Mirc56_13 are always within predicted regional deletions that are induced from upstream and downstream of sgRNA target sites. Therefore, it could be estimated that these deletions were induced from the target sites on Mirc56_14, 15, 16, or 17 and upstream of Mirc56_13.

To clarify them, we will add the following sentences:

• “Four clones (#2_066, #1_021, #1_029 and #1_046) harboured entire Mirc56_X deletions on all analysed Mirc56_X genomic region. In addition to these clones, only 3 pairs (#2_019 and #2_084, #2_038 and #1_023, #1_016 and #1_027) harboured same combination of mutations.” following to “…combinations of mutations (Figure 5C).” in the Result (page16, line 378-380)
• “Meanwhile, focusing on relationship between mutations and target sites that targeted by sgRNA cassettes in each clone, all Mirc56_X genomic regions harbouring Indel mutations were target Micr56_X In addition, if sequential Mirc56_Xs on the genome were deleted, the most upstream and downstream of Mirc56_Xs deleted were always on the target Mirc56_X sites except for #2_025 and #1_41.” following to “…combinations of mutations (Figure 5C).” in the Result (page12, line 304)
• “Genotyping PCR amplified approximately 200 bp around the mature-miRNA genomic region. Unamplified region is defined as miRNA deletion (Black circle) and amplified region was determined as Indel mutation (Gray circle) or Intact by short-NGS. If sequential Mirc56_Xs on the genome were deleted, black translucent square indicates predicted regional deletion assumed that the genomic region flanked by miRNA deletions was also deleted. Besides, if miRNA deletion was induced in Mirc56_13 and the clone have target Mirc56_X on Mirc56_14, 15, 16, or 17” following to “…in each PB mES clone.” in the Figure legend (page23, line 575) Moreover, because we defined “miRNA deletion”, we will change ”regional deletion” to “miRNA deletion” where I mean “deletion of the mature-miRNA genomic regions” in the Result (page13, line 312) and the Discussion (page14, line 363)

*3. Next-generation targeted sequencing of clones should be made publicly accessible. *

→Thank you very much for your comment. We apologize for the inconvenience.

We already informed Review commons that we made publicly available.

We already described BioProject ID PRJNA996747 in the Data Availability (page16, line 383-384)

4. OPTIONAL - Cassette integration number is understudied. One important aspect of tiling mutagenesis is the control over how many guides are present in each cell. The authors report an average of 4.7 cassettes/cell. This could be modulated by the amount of donor vector added, and indeed the authors performed titration experiments, but only with a fluorescent reporter readout. It would be very useful to know how the concentration of donor vector corresponds to the number of cassettes/cell - perhaps genotyping of clones from one or two additional experiments would be sufficient.

→ Thank you very much for your suggestion.

We agree that cassette integration number is one important aspect of tiling mutagenesis.

To investigate how many copies our concentration of donor vector could integrate, we are going to check actual copy numbers in several clones by qPCR.

We think that it is other research to confirm “how the concentration of donor vector corresponds to the number of cassettes/cell”. The correlation might not be liner due to transposase overproduction inhibition (OPI) so that it would require huge amounts of experiments to confirm it. Our research is how CTRL-Mutations induce diverse mutations but not how property PB system have.

Minor comments: 1. The background fails to acknowledge the work of CRISPR-Cas tiling screens (e.g. https://doi.org/10.1038/nbt.3450) or CRISPR-Cas in creating mutagenesis in cell lines (e.g. https://doi.org/10.1007/978-1-0716-0247-8_29*) *

→ Thank you very much for your suggestion, and we agree with your suggestion.

We will add to acknowledge previous studies for CRISPR-Cas tilling screens.

• “Recently, targeted mutagenesis combined forward genetics and reverse genetics has been developed such as saturating mutagenesis and tiling mutagenesis that induce random mutation within target gene(s) [PMID: 25141179, 31586052, 27260157, 28118392]. This targeted mutagenesis can construct a mutant library harbouring subtly different mutations within a target gene(s) so that comparative analysis through the mutant library can screen out critical mutation(s) for biological processes. These random mutagenesises have also revealed the function of numerous coding genes” following to “…list of coding genes [6–8].” in the Introduction (page3, line 55-56)
• “In addition, the saturating mutagenesis are limited in the length of target region due to an approach basing homology-directed repair although it could introduce random mutations on donor template library harbouring any combination and variety of mutations [PMID: 25141179]. On the other hand, the tiling mutagenesis could expand target length in principle because the length depends on multiplex guide RNA (gRNA) designed to target genomic region. Therefore, tiling mutagenesis has been employed to identify critical regions embedded in cis-elements [PMID: 26375006, 30612741, 26751173, 27708057, 28416141, 31784727]. Tiling mutagenesis requires editor such as Cas9 or epigenetic modifier fused to catalytically dead Cas9 (e.g. KRAB-dCas9), and a library containing multiplex gRNA tiling across target genomic region. In general, random single guide RNA (sgRNA) expression cassette are integrated into chromosomes of host cells by retrotransposon system.” following to “…within a narrow region.” in the Introduction (page4, line 82) However, we do not agree that we have to acknowledge previous report about KI or KO by single or double cut in cell lines (as you suggested that https://doi.org/10.1007/978-1-0716-0247-8_29) because it is obvious knowledge. Therefore, we will not add this paper.

2. Figure 1 left 'ROI random mutant PB mES cell' should be horizontally aligned so Mir_1, Mir_2 and MirX align with the upper figure.

→ Thank you very much for your kind comment, and we agree with your suggestion.

Therefore, we changed it in the Figure 1.

*3. It is interesting and unexpected that some guides never induce indels, even in the absence of a regional deletion (e.g. Mirc56_3, Mirc56_7). Why might this be? Was there perhaps an error in the assignment of these guides to these cells? *

→ Thank you very much for your comment.

As you mentioned, Mirc56_3, 4 and 7 had no indel. We appreciate that we can correct our mistakes by your suggestion. We corrected Figure 5D as attached. In addition, we will correct average Mirc56_X site as 22.6 from 22.7.

These sgRNA also induced miRNA deletion with low frequency (Mirc56_3: 38.9%, Mirc56_4: 25.0% and Mirc56_7: 68.0%, Figure 5D). Moreover, every deleted Mirc56_3, 4 and 7 was within predicted regional deletion except for target Mirc56_3 of PB mES clone #2_080 (revised Figure 5C).

Therefore, we raised why some guides never induce indels even in the absence of a regional deletion, as “In addition to low frequencies, Indel mutation might disappear due to regional deletion if these sgRNAs could induce Indel mutation”.

To clarify them, we will add the following sentences:

• “In particularly, middle target sites such as Mirc56_3, 4 and 7 were induced only miRNA deletion or Intact (Figure 5D)” following to “…in our mutant library (Figure 5C, D).” in the Discussion (page14, line 364)
• “In fact, every deleted Mirc56_3, 4 and 7 was within predicted regional deletion except for target Mirc56_3 of PB mES clone #2_080 (Figure 5C). In addition, these sgRNA induced mutation with low frequency (Mirc56_3: 38.9%, Mirc56_4: 25.0% and Mirc56_7: 68.0%, Figure S6). Therefore, we suspected that regional deletion and their low mutation introduction rate facilitated to disappear Indel mutation.” following to “…induced at target sites.” in the Discussion (page14, line 366)

  *4. Regarding Mirc56_2 and 4 integration, on line 34 the authors suggest that "We suspect this was caused by a technical error, such as an unequal amount of sgRNA donor vector or the sequence in sgRNA cassettes affecting integration efficiency or cell growth." sgRNA library imbalance would be a technical error, but integration affecting cell growth is not a technical error. This sentence should be reworded. *

→ Thank you very much for your comment.

We apologize for the misleading sentence even though this paper was already English-reviewed by English language editor.

We will reword that “We suspect this was caused by the sequence in sgRNA cassettes affecting integration efficiency or cell growth, or a technical error such as an unequal amount of sgRNA donor vector.” following to “…PB mES clones via FACS..” in the Discussion (page14, line 344)

*5. Line 540 "ration" is the incorrect word - perhaps "ratio"? *

→ Thank you very much for your kind comment, and we are sorry for the typo.

We will correct it in the Figure legend (page22, line 540).

6. Plot 5b should be shown as a histogram rather than a swarm plot to show how many clones were in each category.

→ Thank you very much for your suggestion.

In Figure 5B, we aimed to indicate the number of sgRNA cassette varieties in each clone but not distribution of the number of integrated sgRNA cassettes. Distribution of the number of integrated sgRNA cassettes in clone library matched with the frequency of target sites in Figure 5D.

We already described the distribution data as “In addition, an average of 22.7 Mirc56_X sites … the same frequency except for the Mirc56_2- and 4-targeting cassettes.” in the Result (page13, line 312-315)

*Reviewer #1 (Significance (Required)):

1. General assessment: The authors are successful in creating clonal cell lines bearing a variety of mutations. Unfortunately, the cell lines also have transposase-mediated insertion events of the sgRNA cassettes at unknown positions in the genome, which will hamper the interpretability of any experiment using these cell lines. The authors fail to justify the use of the transposase and integration of the sgRNA, especially compared to lentiviral transfection or RNPs which would produce edits at the region of interest. Alternately, integrated sgRNA cassettes could have been excised with Flp recombinase as in https://doi.org/10.1007/978-1-0716-0247-8_29. *

→ Thank you very much for your suggestion.

We agree that we did not mention why we choose PiggyBac system compared to lentiviral delivery.

Therefore, we will add the following sentences:

• “In general, random single guide RNA (sgRNA) expression cassette are integrated into chromosomes of host cells by retrotransposon system. To identify combinations of critical region embedded in target regions, it would require diverse combinations of mutations or inactivation sites. To induce multiple mutations or inactivated sites, it requires multiple sgRNA cassettes integration. However, multiple integration of sgRNA cassettes have higher risk of non-targeted endogenous gene disruptions and may impair functional analysis [PMID: 23435812].” in the Introduction.
• “Here, we proposed that DNA transposon system rather than retrotransposon system is more suitable to remove sgRNA cassettes from a mutant library. Transposons are genetic elements that can relocate between genomic sites and there are two types of transposons: (1) DNA transposon is transferred by a "cut and paste" mechanism in which the transposon sequence is cut directly from the genome, and (2) retrotransposon is transferred by a "copy and paste" mechanism in which the transposon sequence is transcribed into RNA and then integrated by reverse transcribed [PMID: 21958341]. Therefore, retrotransposon is never removed from the genome. DNA transposon such as PiggyBac, Sleeping Beauty and Tol2 systems are also used as gene transfer tools in vertebrates [PMID: 26481584]. Especially, PiggyBac leaves no footprint on integrated sites after transposons relocated while other DNA transposon system leaves small insertion on integrated sites [PMID: 34064900]. In addition, excision-only-PiggyBac transposase that can remove transposons but not integrate them, is developed [PMID: 27929521]. Only PiggyBac system can remove transposons carrying sgRNA cassettes from mutant library with no footprint. Therefore, we aimed to validate PiggyBac system for CRISPRko tilling mutagenesis.” in the Introduction. However, we are not going to mention comparison to RNPs because it is obvious that random sgRNA expressions is important key for random mutagenesis and design of random sgRNA treatments by RNP is difficult. The reason is that the target region might be cleaved by almost all sgRNA incorporated into cells. On the other hand, it is easier to design the number of sgRNA expression variety using the delivery system via integration into the chromosome because only integrate sgRNA are expressed.

In addition, we could not agree that “integrated sgRNA cassettes could have been excised with Flp recombinase as in https://doi.org/10.1007/978-1-0716-0247-8_29.”

This paper reports the concept that one EM7>neoR expression cassette flanked by Frt within KI allele could select intended-KI clone and then the cassette could remove by Flp recombinase. However, this approach is not suitable for our method because it causes structural mutation by recombination of multi Frt cassettes that are integrated into nearby genomic regions. Therefore, we will not mention it.

*2. Additionally, the genotyping analysis is unclear, and seems to indicate that each clone bears homozygous mutations, with several clones showing deletions of the entire region. *

→ Thank you very much for your suggestion.

We will revise them in Reviewer #1 Major comment 2a and b.

3. Advance: The authors are motivated to create clones using tiling mutagenesis. Tiling mutagenesis has already been performed without transposases (e.g. https://doi.org/10.1038/nbt.3450, https://doi.org/10.1371/journal.pone.0170445, https://doi.org/10.1038/s41467-019-12489-8*) in the context of a screen, and clones have already been created using CRISPR/Cas9 mutagenesis so the advance presented in this manuscript over previous published work is unclear. *

→Thank you very much for your suggestion, and we agree with your suggestion.

We will add to acknowledge previous studies for CRISPR-Cas tilling screens.

We will add the following sentences:

• “Recently, targeted mutagenesis combined forward genetics and reverse genetics has been developed such as saturating mutagenesis and tiling mutagenesis that induce random mutation within target gene(s) [PMID: 25141179, 31586052, 27260157, 28118392]. This targeted mutagenesis can construct a mutant library harbouring subtly different mutations within a target gene(s) so that comparative analysis through the mutant library can screen out critical mutation(s) for biological processes. These random mutagenesises have also revealed the function of numerous coding genes” following to “…list of coding genes [6–8].” in the Introduction (page3, line 55-56)
• “In addition, the saturating mutagenesis are limited in the length of target region due to an approach basing homology-directed repair although it could introduce random mutations on donor template library harbouring any combination and variety of mutations [PMID: 25141179]. On the other hand, the tiling mutagenesis could expand target length in principle because the length depends on multiplex guide RNA (gRNA) designed to target genomic region. Therefore, tiling mutagenesis has been employed to identify critical regions embedded in cis-elements [PMID: 26375006, 30612741, 26751173, 27708057, 28416141, 31784727]. Tiling mutagenesis requires editor such as Cas9 or epigenetic modifier fused to catalytically dead Cas9 (e.g. KRAB-dCas9), and a library containing multiplex gRNA tiling across target genomic region. In general, random single guide RNA (sgRNA) expression cassette are integrated into chromosomes of host cells by retrotransposon system.” following to “…within a narrow region.” in the Introduction (page4, line 82) The paper you raised as DOI: https://doi.org/10.1038/nbt.3450 applied CRISPRko tiling mutagenesis to find out critical region embedded 2 kb of p53 binding enhancer region by lentiviral delivery of sgRNA cassettes. Our method employs PiggyBac system that can remove the sgRNA cassettes from the chromosome with no footprint. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions. In addition, we expand the length of target region to more than 50 kb. This is one of the advances.

The paper you raised as DOI: https://doi.org/10.1371/journal.pone.0170445 applied CRISPRko tiling mutagenesis to find out critical mutation on MAP2K1 and BRAF protein coding sequence by lentiviral delivery of sgRNA cassettes. Our method employs PiggyBac system that can remove the sgRNA cassettes from the chromosome with no footprint. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions.

The paper you raised as DOI: https://doi.org/10.1038/s41467-019-12489-8 applied CRISPRko tiling mutagenesis for to find out critical domain from protein coding sequence by lentiviral delivery of sgRNA cassettes. Our method employs PiggyBac system that can remove the sgRNA cassettes from the chromosome with no footprint. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions.

To clarify the advantages, we will add the following sentences:

• “Here, we proposed that DNA transposon system rather than retrotransposon system is more suitable to remove sgRNA cassettes from a mutant library. Transposons are genetic elements that can relocate between genomic sites and there are two types of transposons: (1) DNA transposon is transferred by a "cut and paste" mechanism in which the transposon sequence is cut directly from the genome, and (2) retrotransposon is transferred by a "copy and paste" mechanism in which the transposon sequence is transcribed into RNA and then integrated by reverse transcribed [PMID: 21958341]. Therefore, retrotransposon is never removed from the genome. DNA transposon such as PiggyBac, Sleeping Beauty and Tol2 systems are also used as gene transfer tools in vertebrates [PMID: 26481584]. Especially, PiggyBac leaves no footprint on integrated sites after transposons relocated while other DNA transposon system leaves small insertion on integrated sites [PMID: 34064900]. In addition, excision-only-PiggyBac transposase that can remove transposons but not integrate them, is developed [PMID: 27929521]. Only PiggyBac system can remove transposons carrying sgRNA cassettes from mutant library with no footprint. Therefore, we aimed to validate PiggyBac system for CRISPRko tilling mutagenesis.” in the Introduction.
• “CRISPRko tiling mutagenesis is conducted for less than 15 kb target genomic region so far [PMID: 26375006, 30612741], while CRISPRi tiling mutagenesis can target more than 70 kb [PMID: 27708057], it is reported that. Hence, it remains unknown unclear how length CRISPRko tiling mutagenesis could expand” in the Introduction. In addition, we are going to conduct transposon removal by exicision-only-PBase treatment with several PB mES clones, for the proof of concept that CTRL-Mutagenesis can generate mutant library with no sgRNA cassettes.

*4. Audience: The manuscript is written for the basic research audience, and the method could be applied to the study of regions of interest in many diseases. However, the unexcised use of transposases make the method less desirable than other methods. *

→ Thank you very much for your suggestion.

We do not agree that the PiggyBac make the method less desirable than other methods.

As mentioned in our response for reviewer #1 Significance 3, only PiggyBac system can remove transposons carrying sgRNA cassettes from mutant library with no footprint. Multiple integration of sgRNA cassettes have higher risk of non-targeted endogenous gene disruptions and may impair functional analysis. However, sgRNA cassettes by lentiviral delivery is never removed from the genome. In addition, other approaches such as Flp recombinase that reviewer #1 proposed in Significance 1 is not better than PiggyBac because Flp recombinase causes stratal mutation by recombination of multi Frt cassettes that are integrated into nearby genomic regions.

To clarify them, we will add the following sentences:

• “However, multiple integration of single guide RNA (sgRNA) cassettes has higher risk of non-targeted endogenous gene disruptions and may impair functional analysis.” in the Abstract.
• “However, multiple integration of sgRNA cassettes have higher risk of non-targeted endogenous gene disruptions and may impair functional analysis [PMID: 23435812]. To eliminate the risk that integrated sgRNA cassettes disrupt non-targeted endogenous genes, it is best way to remove the sgRNA cassettes from the chromosome.” in the Introduction.
• “Here, we proposed that DNA transposon system rather than retrotransposon system is more suitable to remove sgRNA cassettes from a mutant library. Transposons are genetic elements that can relocate between genomic sites and there are two types of transposons: (1) DNA transposon is transferred by a "cut and paste" mechanism in which the transposon sequence is cut directly from the genome, and (2) retrotransposon is transferred by a "copy and paste" mechanism in which the transposon sequence is transcribed into RNA and then integrated by reverse transcribed [PMID: 21958341]. Therefore, retrotransposon is never removed from the genome. DNA transposon such as PiggyBac, Sleeping Beauty and Tol2 systems are also used as gene transfer tools in vertebrates [PMID: 26481584]. Especially, PiggyBac leaves no footprint on integrated sites after transposons relocated while other DNA transposon system leaves small insertion on integrated sites [PMID: 34064900]. In addition, excision-only-PiggyBac transposase that can remove transposons but not integrate them, is developed [PMID: 27929521]. Only PiggyBac system can remove transposons carrying sgRNA cassettes from mutant library with no footprint. Therefore, we aimed to validate PiggyBac system for CRISPRko tilling mutagenesis.” in the Introduction. In addition, we are going to conduct transposon removal by exicision-only-PBase treatment with several PB mES clones, for the proof of concept that CTRL-Mutagenesis can generate mutant library with no sgRNA cassettes.

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

Major concerns:

1) Concern about the Novelty of Functional Analysis Platforms: The authors claim that there are no established platforms for the study of cis-elements or microRNA clusters. This assertion seems inaccurate, as previous studies have utilized Cas9 tiling screens to investigate cis-regulatory elements (CREs) and large-scale screens to probe microRNA functions, as exemplified by the works of Canver et al. in Nature 2015, Gasperini et al. in Cell 2019, and others. *

→ Thank you very much for your suggestion, and we agree with your suggestion.

We apologize our false claim so that we will delete the following sentences:

• “In contrast, no functional analysis platforms have been established for the study of cis-elements or microRNA cluster regions consisting of multiple microRNAs with functional overlap” in the Abstract (page2, line 28-30)
• “While loss-of-function analysis has been conducted for numerous coding genes, very limited progress has been made on non-coding genes and cis-elements.” in the Introduction (page3, line 47-49) The paper you raised as DOI: https://doi.org/10.1038/nature15521 (Canver et al. in Nature 2015) applied CRISPRko tiling mutagenesis to find out critical region embedded 12 kb of BCL11A enhancer region by lentiviral delivery of sgRNA cassettes. Our method employs PiggyBac system that can remove the sgRNA cassettes from the chromosome with no footprint. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions. In addition, we expand the length of target region to more than 50 kb. This is one of the advances.

The paper you raised as DOI: https://doi.org/10.1016/j.cell.2018.11.029 (Gasperini et al. in Cell 2019) applied CRISPRko tiling mutagenesis to find out critical region embedded maximum 12 kb enhancer candidates, in addition to CRISPRi tilling candidate screening through one sgRNA by one candidate enhancer, by lentiviral delivery of sgRNA cassettes. Our method employs PiggyBac system that can remove the sgRNA cassettes from the chromosome with no footprint. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions. In addition, we expand the length of target region to more than 50 kb. This is one of the advances. Additionally, to identify combinations of critical region embedded in target regions, it would require diverse combinations of mutations or inactivation sites. To induce multiple mutations or inactivated sites, it requires multiple sgRNA cassettes integration. However, multiple integration of sgRNA cassettes have higher risk of non-targeted endogenous gene disruptions and may impair functional analysis. To eliminate the risk that integrated sgRNA cassettes disrupt non-targeted endogenous genes, it is best way to remove the sgRNA cassettes from the chromosome. Thus, to identify combinations of critical region embedded in target regions with no artifact owing to no footprint by removal of sgRNA cassettes, CRISPRko tiling mutagenesis rather than CRISPRi is better method because CRISPRi requires integrated cassettes that stably expressed sgRNA and epigenetic modifier fused to dCas9. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions to find out combinations of critical region embedded in target regions.

Therefore, to add to acknowledge previous studies and clarify the advantages, we will add the following sentences:

• “In addition, the saturating mutagenesis are limited in the length of target region due to an approach basing homology-directed repair although it could introduce random mutations on donor template library harbouring any combination and variety of mutations [PMID: 25141179]. On the other hand, the tiling mutagenesis could expand target length in principle because the length depends on multiplex guide RNA (gRNA) designed to target genomic region. Therefore, tiling mutagenesis has been employed to identify critical regions embedded in cis-elements [PMID: 26375006, 30612741, 26751173, 27708057, 28416141, 31784727]. Tiling mutagenesis requires editor such as Cas9 or epigenetic modifier fused to catalytically dead Cas9 (e.g. KRAB-dCas9), and a library containing multiplex gRNA tiling across target genomic region. In general, random single guide RNA (sgRNA) expression cassette are integrated into chromosomes of host cells by retrotransposon system.” following to “…within a narrow region.” in the Introduction (page4, line 82)
• “To identify combinations of critical region embedded in target regions, it would require diverse combinations of mutations or inactivation sites. To induce multiple mutations or inactivated sites, it requires multiple sgRNA cassettes integration. However, multiple integration of sgRNA cassettes have higher risk of non-targeted endogenous gene disruptions and may impair functional analysis [PMID: 23435812]. To eliminate the risk that integrated sgRNA cassettes disrupt non-targeted endogenous genes, it is best way to remove the sgRNA cassettes from the chromosome. Thus, to identify combinations of critical region embedded in target regions with no artifact owing to no footprint by removal of sgRNA cassettes, CRISPRko tiling mutagenesis rather than CRISPRi is better method because CRISPRi requires integrated cassettes that stably expressed sgRNA and epigenetic modifier fused to dCas9.” in the Introduction.
• “Here, we proposed that DNA transposon system rather than retrotransposon system is more suitable to remove sgRNA cassettes from a mutant library. Transposons are genetic elements that can relocate between genomic sites and there are two types of transposons: (1) DNA transposon is transferred by a "cut and paste" mechanism in which the transposon sequence is cut directly from the genome, and (2) retrotransposon is transferred by a "copy and paste" mechanism in which the transposon sequence is transcribed into RNA and then integrated by reverse transcribed [PMID: 21958341]. Therefore, retrotransposon is never removed from the genome. DNA transposon such as PiggyBac, Sleeping Beauty and Tol2 systems are also used as gene transfer tools in vertebrates [PMID: 26481584]. Especially, PiggyBac leaves no footprint on integrated sites after transposons relocated while other DNA transposon system leaves small insertion on integrated sites [PMID: 34064900]. In addition, excision-only-PiggyBac transposase that can remove transposons but not integrate them, is developed [PMID: 27929521]. Only PiggyBac system can remove transposons carrying sgRNA cassettes from mutant library with no footprint. Therefore, we aimed to validate PiggyBac system for CRISPRko tilling mutagenesis.” in the Introduction.
• “CRISPRko tiling mutagenesis is conducted for less than 15 kb target genomic region so far [PMID: 26375006, 30612741], while CRISPRi tiling mutagenesis can target more than 70 kb [PMID: 27708057], it is reported that. Hence, it remains unknown unclear how length CRISPRko tiling mutagenesis could expand” in the Introduction. On the other hand, we could not find previous studies employing Cas9 tiling mutagenesis to investigate miRNA functions. The application for miRNA cluster is also one of the advances.

2) Advantages of PiggyBack System Over Lentiviral Integration: The paper does not clearly articulate the advantages of their proposed PiggyBack-based system for sgRNA integration over traditional lentiviral integration. Both methods facilitate the random integration of multiple gRNAs, but the paper lacks a comparative analysis or justification for choosing the PiggyBack system.

→ Thank you very much for your suggestion, and we agree with your suggestion.

We agree that we did not mention why we choose PiggyBac system compared to lentiviral delivery.

Therefore, we will add the following sentences:

• “In general, random single guide RNA (sgRNA) expression cassette are integrated into chromosomes of host cells by retrotransposon system. To identify combinations of critical region embedded in target regions, it would require diverse combinations of mutations or inactivation sites. To induce multiple mutations or inactivated sites, it requires multiple sgRNA cassettes integration. However, multiple integration of sgRNA cassettes have higher risk of non-targeted endogenous gene disruptions and may impair functional analysis [PMID: 23435812].” in the Introduction.
• “Here, we proposed that DNA transposon system rather than retrotransposon system is more suitable to remove sgRNA cassettes from a mutant library. Transposons are genetic elements that can relocate between genomic sites and there are two types of transposons: (1) DNA transposon is transferred by a "cut and paste" mechanism in which the transposon sequence is cut directly from the genome, and (2) retrotransposon is transferred by a "copy and paste" mechanism in which the transposon sequence is transcribed into RNA and then integrated by reverse transcribed [PMID: 21958341]. Therefore, retrotransposon is never removed from the genome. DNA transposon such as PiggyBac, Sleeping Beauty and Tol2 systems are also used as gene transfer tools in vertebrates [PMID: 26481584]. Especially, PiggyBac leaves no footprint on integrated sites after transposons relocated while other DNA transposon system leaves small insertion on integrated sites [PMID: 34064900]. In addition, excision-only-PiggyBac transposase that can remove transposons but not integrate them, is developed [PMID: 27929521]. Only PiggyBac system can remove transposons carrying sgRNA cassettes from mutant library with no footprint. Therefore, we aimed to validate PiggyBac system for CRISPRko tilling mutagenesis.” in the Introduction.

  *3) Lack of Comparative Analysis with Alternative Methods: The authors did not provide a comparison of CTRL-Mutagenesis with other existing screening methods. Such a comparison is crucial for understanding the effectiveness and efficiency of the new method in relation to established techniques. *

→ Thank you very much for your suggestion.

We agree with the comparison is one of important experiments.

However, our main claim is validation of tiling mutagenesis using PiggyBac that is only integration system with no footprint. Therefore, we propose our novelty without the comparison and not argue higher / lower efficiency of CTRL-Mutagenesis compared to exiting methods.

*4) Limitations in Library Resolution: The paper acknowledges the limited resolution of their proposed library. The authors might have explored the use of base editors for enhanced resolution in such screens, as base editing could potentially offer more precise and controlled mutagenesis as briefly mentioned in the discussion. *

→ Thank you very much for your suggestion.

We agree with your suggestion.

Base editing is occurred within only editing window. In addition, a major limitation of prime editing is low efficiency (https://doi.org/10.1016/j.tibtech.2023.03.004). Therefore, design of sgRNA for base editor or pegRNA and its editing efficiency requires huge amounts of experiments.

Our study is proof of concept to validate PiggyBac system for CRISPRko tilling mutagenesis and expanded the length of target regions. Thus, we just discussed limited resolution of our mutant library and proposed the use of base editors for enhanced resolution in the Discussion (page14, line 366-370).

5) Absence of Functional Data Post-Mutagenesis: A significant limitation of the study is the absence of functional data following the creation of cells with different mutations. While the authors speculate about using differentiation systems or organoids for practical applications, they do not provide empirical data to demonstrate the utility of the CTRL-Mutagenesis approach. This lack of functional validation raises questions about the practical applicability of the method.

→ Thank you very much for your suggestion.

We agree with your suggestion.

We would make functional analysis future research.

In this paper, we just validated PiggyBac system for CRISPRko tilling mutagenesis and expanded the length of target regions.

To change our tone that claiming usability of our method for functional analysis, we will change the following sentences:

• Change “to identify functionally important elements in non-coding regions” to “to induce diverse combination and variety of mutations within more than 50 kb non-coding region” in the Title.
• Add “However, not much loss-of-function screens of non-coding regulatory elements has been conducted due to ambiguous annotations compared with protein-coding genes. Tiling mutagenesis has been employed to identify critical regions embedded in non-coding regulatory elements by comparative analysis through a mutant library harbouring subtly different regions mutated within less than 15 kb region. Conventional tiling mutagenesis construct a mutant library integrated multiple sgRNA cassettes by retroviral delivery. However, multiple integration of single guide RNA (sgRNA) cassettes has higher risk of non-targeted endogenous gene disruptions and may impair functional analysis. Herein, combining tiling mutagenesis and PiggyBac transposon that can be removed with no footprint on integrated sites, we established an expanded tilling mutagenesis method named CRISPR- & Transposase-based RegionaL Mutagenesis (CTRL-Mutagenesis). We demonstrated that PiggyBac system could integrated diverse combinations and varieties of sgRNA cassettes.and then CTRL-Mutagenesis randomly induces diverse combination and variety of mutations within more than 50 kb non-coding region in murine embryonic stem cells. CTRL-Mutagenesis would apply for wider non-coding regulatory elements with no risk of non-targeted endogenous gene disruptions.” in the Abstract.
• Delete “Comparative analysis of mutants harbouring subtly different mutations within the same region would facilitate the further study of cis-element and microRNA clusters.” in the Abstract (page2, line 38-40).
• Change “The generated random mutant mES clone library could facilitate further functional analyses of non-coding regulatory elements within the genome.” to “The generated random mutant mES clone library could develop to investigate critical regions of non-coding regulatory elements within the genome.” In the Introduction (page4, line 88-90)

  *Reviewer #2 (Significance (Required)):

  1. In summary, while the idea to integrate sgRNA in the genome by the PiggyBack system is interesting the claim of novelty is questionable due to existing methods in the field. The advantages of their system over existing technologies are not clearly articulated, and a lack of comparative analysis with other methods leaves the efficiency of CTRL-Mutagenesis uncertain. *

→ Thank you very much for your suggestion.

Previous studies about CRISPRko and CRISPRi tiling mutagenesis employ lentiviral delivery of sgRNA cassettes into the genome. However, multi sgRNA cassette integrations have higher risk to disrupt non-targeted endogenous functions. To eliminate the risk that integrated sgRNA cassettes disrupt non-targeted endogenous genes, it is best way to remove the sgRNA cassettes from the chromosome. Nevertheless, lentiviral transposon, one of retrotransposon, cannot be removed from the chromosome. On the other hand, only PiggyBac transposon can be removed with no footprint. Therefore, we aimed to validate PiggyBac system for tiling mutagenesis. Moreover, there is no report that CRISPRko tiling mutagenesis apply for more than 15 kb genomic region. Therefore, we aimed to expand the length of target region.

Therefore, we will change our claim that our method could expand CRISPRko tiling mutagenesis to more than 50 kb with no risk of non-targeted endogenous gene disruption.

We will add the novelty and advantage of our method.

• “Here, we proposed that DNA transposon system rather than retrotransposon system is more suitable to remove sgRNA cassettes from a mutant library. Transposons are genetic elements that can relocate between genomic sites and there are two types of transposons: (1) DNA transposon is transferred by a "cut and paste" mechanism in which the transposon sequence is cut directly from the genome, and (2) retrotransposon is transferred by a "copy and paste" mechanism in which the transposon sequence is transcribed into RNA and then integrated by reverse transcribed [PMID: 21958341]. Therefore, retrotransposon is never removed from the genome. DNA transposon such as PiggyBac, Sleeping Beauty and Tol2 systems are also used as gene transfer tools in vertebrates [PMID: 26481584]. Especially, PiggyBac leaves no footprint on integrated sites after transposons relocated while other DNA transposon system leaves small insertion on integrated sites [PMID: 34064900]. In addition, excision-only-PiggyBac transposase that can remove transposons but not integrate them, is developed [PMID: 27929521]. Only PiggyBac system can remove transposons carrying sgRNA cassettes from mutant library with no footprint. Therefore, we aimed to validate PiggyBac system for CRISPRko tilling mutagenesis.” in the Introduction.
• “CRISPRko tiling mutagenesis is conducted for less than 15 kb target genomic region so far [PMID: 26375006, 30612741], while CRISPRi tiling mutagenesis can target more than 70 kb [PMID: 27708057], it is reported that. Hence, it remains unknown unclear how length CRISPRko tiling mutagenesis could expand” in the Introduction. However, our main claim is validation of tiling mutagenesis using PiggyBac that is only integration system with no footprint. Therefore, we will propose our novelty without the comparison and not argue higher / lower efficiency of CTRL-Mutagenesis compared to exiting methods.

In addition, we are going to conduct transposon removal by exicision-only-PBase treatment with several PB mES clones, for the proof of concept that CTRL-Mutagenesis can generate mutant library with no sgRNA cassettes.

2. Moreover, the limited resolution of their library and the absence of functional data post-mutagenesis are significant drawbacks that need to be addressed in future research to ascertain the method's practical utility.

→ Thank you very much for your suggestion.

We agree with your suggestion.

We would make functional analysis future research.

Base editing is occurred within only editing window. In addition, a major limitation of prime editing is low efficiency (https://doi.org/10.1016/j.tibtech.2023.03.004). Therefore, design of sgRNA for base editor or pegRNA and its editing efficiency requires huge amounts of experiments.

Our study is proof of concept to validate PiggyBac system for CRISPRko tilling mutagenesis and expanded the length of target regions. Thus, we just discussed limited resolution of our mutant library and proposed the use of base editors for enhanced resolution in the Discussion (page14, line 366-370).

Therefore, we just claimed that we validated PiggyBac system for CRISPRko tilling mutagenesis and expanded the length of target regions.

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

Major comments: 1. Authors claim that "CTRL-mutagenesis randomly induces diverse mutations only within the targeted regions in murine embryonic stem (mES) cells.", however, the outcome of mutations is not entirely random since most of the mutations are regional deletions. For example, despite the random distribution of gRNAs per cell, the inner regions like Mirc56_5 or Mirc56_8 are mutated with >80% efficiency.*

→ Thank you very much for your comment.

We agree that middle regions are tending to be deleted and mutation type induced is not entirely random. However, we do not agree that “the outcome of mutations is not entirely random since most of the mutations are regional deletions.” Focusing on the combinations of mutations as mentioned in the Result (page12, line 302-304), CTRL-Mutagenesis could induce diverse mutation combinations randomly at a moderate degree. In fact, 79.2% of clones harboring multiple mutations were induced different combinations of mutations. In addition, to confirm how mutations occurred within Mirc56 by CTRL-Mutagenesis, we constructed only 87 mutant clones though single cloning. Therefore, it is not completely understanded due to fewer clones compared with conventional CRISPRko tiling mutant library. Of course, we should improve the randomness of mutation combinations, but we already discussed it and proposed solutions in the Discussion (page14, line 366-370).

Certainly, CTRL-Mutagenesis would be difficult to identify necessary and sufficient genomic region due to incomplete randomness. Nevertheless, there is no report to induce diverse combination and variety of mutations within more than 50 kb genomic region. Hence, CTRL-Mutagenesis should be worth screening out critical regions within more than 50 kb regions.

To clarify them, will add the following sentences:

• “CRISPRko tiling mutagenesis is conducted for less than 15 kb target genomic region so far [PMID: 26375006, 30612741], while CRISPRi tiling mutagenesis can target more than 70 kb [PMID: 27708057], it is reported that. Hence, it remains unknown unclear how length CRISPRko tiling mutagenesis could expand” in the Introduction.
• “Four clones (#2_066, #1_021, #1_029 and #1_046) harboured entire Mirc56_X deletions on all analysed Mirc56_X genomic region. In addition to these clones, only 3 pairs (#2_019 and #2_084, #2_038 and #1_023, #1_016 and #1_027) were induced same combination of mutations. Besides, 26 clones had only one mutation from Mirc56_1 to Mirc56_13. On the other hand, there was no mutation on Mirc56_1 to 13 in 11 clones including 5 clones (#2_012, #2_015, #2_054, #2_092 and #2_102) carried no sgRNA cassette for Mirc56 _1 to 13 and 6 clones (#2_017, #2_053, #2_098, #1_003, #1_012 and #1_044) even carried any one of sgRNA cassettes for Mirc56 _1 to 13. Among 48 clones carrying multiple mutations except for clones carrying only one mutation or Intact, 38 clones (79.2%) harboured different combinations of mutations. These results suggested that CTRL-Mutagenesis could induce diverse combinations of mutations.” following to “…different combinations of mutations (Figure 5C).” in the Result (page12, line 304)
• “Note that CTRL-Mutagenesis would be difficult to identify necessary and sufficient genomic region due to incomplete randomness. Nevertheless, CTRL-Mutagenesis should be worth screening out critical regions within more than 50 kb regions” following to “…to induce regional deletions.” in the Discussion (page15, line 378)
• Change “diverse mutations” to “diverse combination and variety of mutations” in the Title, Abstract (page2, line 37), Introduction (page4, line 87), Result (page13, line 318), Discussion (page13, line 325), (page14, line 363) Additionally, we do not agree with your suggestions that “the inner regions like Mirc56_5 or Mirc56_8 are mutated with >80% efficiency”. We apologize for the misleading context. These high mutation rates were calculated on only the target sites. Actually, maximum mutation rate on all MIrc56_X genomic regions are 44.8% on Mirc56_10, minimum is 14.9% on Mirc56_2 and an average is 30.9% (attached Figure).

We appreciate that we can recognize our misleading context by your suggestion. It is more important that the analysis focusing all Mirc56_X genomic regions rather than target Mirc56_X. Therefore, we newly made figure about event occurrence in Mirc56_X genomic regions (attached Figure) as Figure 5D and replaced previous Figure 5D about event occurrence in target Mirc56_X to Supplemental Figure S6.

To clarify them, we will add the following sentences:

• “As for event occurrences on each Mirc56_X genomic region, miRNA deletions were dominant and an average of 26.7 Mirc56_X genomic region were induced mutations in 87 clones (Figure 5D). Maximum mutation rate on all MIrc56_X genomic regions was 44.8% (39/87) on Mirc56_10, minimum was 14.9% (13/87) on Mirc56_2” following to “…on the same strand” in the Result (page12, line 309)
• “__D, __Mutations in 87 Mirc56 random mutant clones. The target sites do not include Mirc56_14, 15, 16, and The vertical axis and bar graphs show event occurrence on each Mirc56 genomic region in 87 Mirc56 random mutant clones. The bar colour indicates each event (Black: Regional deletion, Gray: Indel mutation, White: Intact).” in the Figure legend.

  2. Also, although the authors discuss that the lower mutation frequency observed for Mirc56_2 and 4 may be due to a technical error, confirming this by repeating the experiment would be important to prove the usability of this method.

→Thank you very much for your comment, and we agree with your suggestion.

We had already constructed bulk PB mES cells twice and showed Figure 4B combined these experimental replicates.

To clarify that we constructed bulk PB mES cells twice, we changed Figure 4B as attached and will add the following sentences:

• “Even though these bulk PB mES cells were constructed twice, it seemed that sgRNA cassettes for Mirc56_2 and 4 were difficult to integrate into the genome.” following to “…were rarely detected” in the Result (page11, line 273)
• “In addition, we suspected technical errors so that we constructed bulk PB mES cells twice. Unfortunately, their low integration frequencies were not improved.” following to “…efficiency or cell growth.” in the Discussion (page14, line 346)
• “Bulk1 and Bulk2 indicate the experimental replicate.” following to “…next-generation sequencing (NGS).”in the Figure legend (page22 line 563) In addition, we re-sequenced sgRNA donor vector for Mirc56_2 and 4, and will add the following sentences:

“We firstly doubted that their low integration frequencies were caused by any mutations on PB transposon of sgRNA donor vector, on especially ITR or ID that are important for integration efficiency [PMID: 15663772]. Therefore, we sequenced PB transposons for Mirc56_2 and 4 again. However, we could not find any mutations on their PB transposon.” following to “…efficiency or cell growth.” in the Discussion (page14, line 346)

Moreover, to confirm the technical error, we are going to confirm sgRNA pool imbalance in donor vector library by amplicon short-read NGS.

*3. Additionally, the experiments were performed on the haploid X chromosome of a male cell line. It is questionable whether this method can be generalized to other regions located in the other chromosomes. Clarifying These points would be essential especially because the focus of this manuscript is to describe the efficiency of this novel methodology. *

→Thank you very much for your comment.

We expect that CTRL-Mutagenesis could be valid on other biallelic locus.

Therefore, we raised predicted issue such as complex genotyping and proposed one solution.

When we target other biallelic locus, we must determine whether the combination of mutations induced are cis- or trans-mutations. Haplotype phasing, combined long-read sequencing with SNP markers within ROI on maternal/paternal chromosome, assembles each allele via SNP markers on each read [PMID: 35710642]. Therefore, combining CTRL-Mutagenesis on heterozygotic alleles of cells derived from such as human or murine hybrid with haplotype phasing might simplify genotyping.

We will add the following sentences:

“In this study, CTRL-Mutagenesis was validated by genotyping on mono allele in male mES cells to avoid investigating whether the combination of mutations induced are cis- or trans-mutations. All genotypes on Mirc56 should be hemizygous and these mutations induced might be cis-mutations so that we determined the genotypes by amplifying approximately 200 bp around the target sites. However, we did not confirm large mutations such as deletion of the genomic region between target sites and inversion. Long-read sequencing might capture their large mutations. Besides, we also expect that CTRL-Mutagenesis could be valid for ROI on biallelic autosome and X chromosome in female. Therefore, it is required to determine whether the combination of mutations induced are cis- or trans-mutation. Haplotype phasing, combined long-read sequencing with SNP markers within ROI on maternal/paternal chromosome, assembles each allele via SNP markers on each read [PMID: 35710642]. Therefore, combining CTRL-Mutagenesis on heterozygotic alleles of cells derived from such as human or murine hybrid with haplotype phasing might simplify genotyping.” in the Discussion.

*4. The limitations of the methods seem not to be fully described in the manuscript and must be clarified. Compared to the previous studies (see "significance" section for details), this method is inferior in that (1) it is time-consuming because it requires clonal expansion of single cells and (2) it has low throughput because it requires genome sequencing due to the occurrence of deletions. These points should be described for the potential users of this methodology. For example, it may be useful to detail the time consumption in each experimental step in Fig. 4A. *

→Thank you very much for your comment.

We do not agree that (1) it is time-consuming because it requires clonal expansion of single cells.

To confirm the mutations that CTRL-Mutagenesis induced, we did not conduct phenotyping screening such as dropout screening in this study. For further high-throughput screening, CTRL-Mutagenesis could apply bulk mutant mES cells, that is treated with Cas9 and EGFP-positive, for phenotyping screening.

Additionally, we do not agree that (2) it has low throughput because it requires genome sequencing due to the occurrence of deletions. In this study, to prove our concept that CTRL-Mutagenesis could induce diverse combinations and varieties of mutations such as Indel and regional deletion, we conducted genotyping in all random mutant clones. On the other hand, there are alternative comparative method to improve throughput without genotyping. Combination of phenotyping screening and gene expression assay for target miRNAs or transcript regulated by target cis-element help us obtain clones harboring mutations on functionally critical regions within target region. Finally, we should conduct genotyping to identify critical regions embedded in non-coding regulatory elements.

Even so, we will add the time consumption in Figure 4A as attached because the information may be useful for potential users as you mentioned.

*Minor comments: 1. Data and methods are well-presented for reproducibility. The EGFP-positive ratio may be added to Fig. 4C for clarity. *

→Thank you very much for your kind comment.

We added the EGFP-positive ratio to Figure 4C and will add the following sentence:

“The percentage above the box indicates the EGFP-positive ratio.” following to “…the gates of the EGFP filter.” in the Figure legends (page23, line 567)

2. Enhance referencing accuracy, rectify DOI format in ref 21, and ensure consistency in citation formatting, e.g., ref 32.

→Thank you very much for your kind comment.

Along with the transfer, we will modify the style of references and have already confirmed the referencing accuracy in the Reference.

3. It seems that the experimental condition (e.g. The amount of vectors used for transfection) should be re-considered every time the researcher wants to set up an experiment changing target genomic regions, cell types etc. If so, this also should be described in the text for potential users of this method.

→Thank you very much for your comment, and we agree with your suggestion.

We will add the following sentences:

“This study just validated CTRL-Mutagenesis for 17 target sites in mES cells. Therefore, it might be better to adjust the number of integrated sgRNA cassettes according to the number of target sites and cell types.” following to “…sgRNA cassettes to be integrated.” in the Discussion (page14, line 355)

*Reviewer #3 (Significance (Required)):

There were various methods described in the late 2010's which aimed to screen for the functional non-coding regions using approaches such as KO-based, HDR-based, and epigenetic silencing using dCas9 (for example, PMID: 25141179, 26751173, 27708057, 28416141, 31784727). The authors should summarize what would be the strength of their method compared to these previously described methodologies. The strength of this methodology seems to be moderate complexity and cost-effectiveness compared to these previous techniques. It may be difficult for this methodology to become a state-of-the-art method to evaluate cis-element combinations, but it can be beneficial to researchers wanting to set up a low-cost system that can produce moderately complex cell libraries.*

→Thank you very much for your suggestion.

We will add to acknowledge previous studies for CRISPR-Cas tilling screens.

• “Recently, targeted mutagenesis combined forward genetics and reverse genetics has been developed such as saturating mutagenesis and tiling mutagenesis that induce random mutation within target gene(s) [PMID: 25141179, 31586052, 27260157, 28118392]. This targeted mutagenesis can construct a mutant library harbouring subtly different mutations within a target gene(s) so that comparative analysis through the mutant library can screen out critical mutation(s) for biological processes. These random mutagenesises have also revealed the function of numerous coding genes” following to “…list of coding genes [6–8].” in the Introduction (page3, line 55-56)
• “In addition, the saturating mutagenesis are limited in the length of target region due to an approach basing homology-directed repair although it could introduce random mutations on donor template library harbouring any combination and variety of mutations [PMID: 25141179]. On the other hand, the tiling mutagenesis could expand target length in principle because the length depends on multiplex guide RNA (gRNA) designed to target genomic region. Therefore, tiling mutagenesis has been employed to identify critical regions embedded in cis-elements [PMID: 26375006, 30612741, 26751173, 27708057, 28416141, 31784727]. Tiling mutagenesis requires editor such as Cas9 or epigenetic modifier fused to catalytically dead Cas9 (e.g. KRAB-dCas9), and a library containing multiplex gRNA tiling across target genomic region. In general, random single guide RNA (sgRNA) expression cassette are integrated into chromosomes of host cells by retrotransposon system.” following to “…within a narrow region.” in the Introduction (page4, line 82) The paper you raised as DOI: https://doi.org/10.1038/nature13695 (PMID: 25141179) applied saturation mutagenesis to find out critical mutation on BRCA1 and DBR1 protein coding sequence by HDR-based strategy using donor template library. This method based homologous recombination repair, so that the length of target region is limited. Our method employs tiling mutagenesis whose target length depends on sgRNA designed. We expand the length of target region to more than 50 kb from less than 15 kb previously reported. This is our strength compared with this report.

The paper you raised as DOI: https://doi.org/10.1038/nbt.3450 (PMID: 25141179) applied CRISPRko tiling mutagenesis to find out critical region from 2 kb of p53 binding enhancer region by lentiviral delivery of sgRNA cassettes. Our method employs PiggyBac system that can remove the sgRNA cassettes from the chromosome with no footprint. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions. In addition, we expand the length of target region to more than 50 kb. This is one of the advances.

The paper you raised as DOI: https://doi.org/10.1126/science.aag2445 (PMID: 27708057) applied CRISPRi tiling mutagenesis to find out critical region from 74 kb genomic region around GATA1 and MYC by lentiviral delivery of sgRNA cassettes. Our method employs CRISPRko and PiggyBac system that can remove the sgRNA cassettes from the chromosome with no footprint. To identify combinations of critical region embedded in target regions, it would require diverse combinations of mutations or inactivation sites. To induce multiple mutations or inactivated sites, it requires multiple sgRNA cassettes integration. However, multiple integration of sgRNA cassettes have higher risk of non-targeted endogenous gene disruptions and may impair functional analysis. To eliminate the risk that integrated sgRNA cassettes disrupt non-targeted endogenous genes, it is best way to remove the sgRNA cassettes from the chromosome. Thus, to identify combinations of critical region embedded in target regions with no artifact owing to no footprint by removal of sgRNA cassettes, CRISPRko tiling mutagenesis rather than CRISPRi is better method because CRISPRi requires integrated cassettes that stably expressed sgRNA and epigenetic modifier fused to dCas9. PiggyBac system can remove the sgRNA cassettes from the chromosome with no footprint. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions to find out combinations of critical region embedded in target regions.

The paper you raised as DOI: https://doi.org/10.1016/j.molcel.2017.03.007 (PMID: 28416141) reported applied CRISPRi tiling mutagenesis to find out critical region from TAD scale (about 200 kb) with low magnification by lentiviral delivery of sgRNA cassettes. Our method employs PiggyBac system that can remove the sgRNA cassettes from the chromosome with no footprint. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions.

The paper you raised as DOI: https://doi.org/10.1038/s41588-019-0538-0 (PMID: 31784727) reported applied CRISPRi tiling mutagenesis to develop method that can find out novel regulatory element around protein coding by lentiviral delivery of sgRNA cassettes. Our method employs PiggyBac system that can remove the sgRNA cassettes from the chromosome with no footprint. Therefore, our method should be novel method that generates mutant library with no risk of non-targeted endogenous gene disruptions.

To clarify the advantages, we will add the following sentences:

• “To identify combinations of critical region embedded in target regions, it would require diverse combinations of mutations or inactivation sites. To induce multiple mutations or inactivated sites, it requires multiple sgRNA cassettes integration. However, multiple integration of sgRNA cassettes have higher risk of non-targeted endogenous gene disruptions and may impair functional analysis [PMID: 23435812]. To eliminate the risk that integrated sgRNA cassettes disrupt non-targeted endogenous genes, it is best way to remove the sgRNA cassettes from the chromosome. Thus, to identify combinations of critical region embedded in target regions with no artifact owing to no footprint by removal of sgRNA cassettes, CRISPRko tiling mutagenesis rather than CRISPRi is better method because CRISPRi requires integrated cassettes that stably expressed sgRNA and epigenetic modifier fused to dCas9.” in the Introduction.
• “Here, we proposed that DNA transposon system rather than retrotransposon system is more suitable to remove sgRNA cassettes from a mutant library. Transposons are genetic elements that can relocate between genomic sites and there are two types of transposons: (1) DNA transposon is transferred by a "cut and paste" mechanism in which the transposon sequence is cut directly from the genome, and (2) retrotransposon is transferred by a "copy and paste" mechanism in which the transposon sequence is transcribed into RNA and then integrated by reverse transcribed [PMID: 21958341]. Therefore, retrotransposon is never removed from the genome. DNA transposon such as PiggyBac, Sleeping Beauty and Tol2 systems are also used as gene transfer tools in vertebrates [PMID: 26481584]. Especially, PiggyBac leaves no footprint on integrated sites after transposons relocated while other DNA transposon system leaves small insertion on integrated sites [PMID: 34064900]. In addition, excision-only-PiggyBac transposase that can remove transposons but not integrate them, is developed [PMID: 27929521]. Only PiggyBac system can remove transposons carrying sgRNA cassettes from mutant library with no footprint. Therefore, we aimed to validate PiggyBac system for CRISPRko tilling mutagenesis.” in the Introduction.
• “CRISPRko tiling mutagenesis is conducted for less than 15 kb target genomic region so far [PMID: 26375006, 30612741], while CRISPRi tiling mutagenesis can target more than 70 kb [PMID: 27708057], it is reported that. Hence, it remains unknown unclear how length CRISPRko tiling mutagenesis could expand” in the Introduction. In addition, we are going to conduct transposon removal by exicision-only-PBase treatment with several PB mES clones, for the proof of concept that CTRL-Mutagenesis can generate mutant library with no sgRNA cassettes.

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

Major concerns, 1, Authors claim "to identify functionally important elements in non-coding regions in the title but there is no evidence of any functional analysis in the manuscript.*

→ Thank you very much for your suggestion, and we agree with your suggestion.

In this paper, we just validated PiggyBac system for CRISPRko tilling mutagenesis and expanded the length of target regions.

To change our tone that claiming usability of our method for functional analysis, we will change the following sentences:

• Change “to identify functionally important elements in non-coding regions” to “to induce diverse combination and variety of mutations within more than 50 kb non-coding region” in the Title.
• Add “However, not much loss-of-function screens of non-coding regulatory elements has been conducted due to ambiguous annotations compared with protein-coding genes. Tiling mutagenesis has been employed to identify critical regions embedded in non-coding regulatory elements by comparative analysis through a mutant library harbouring subtly different regions mutated within less than 15 kb region. Conventional tiling mutagenesis construct a mutant library integrated multiple sgRNA cassettes by retroviral delivery. However, multiple integration of single guide RNA (sgRNA) cassettes has higher risk of non-targeted endogenous gene disruptions and may impair functional analysis. Herein, combining tiling mutagenesis and PiggyBac transposon that can be removed with no footprint on integrated sites, we established an expanded tilling mutagenesis method named CRISPR- & Transposase-based RegionaL Mutagenesis (CTRL-Mutagenesis). We demonstrated that PiggyBac system could integrated diverse combinations and varieties of sgRNA cassettes.and then CTRL-Mutagenesis randomly induces diverse combination and variety of mutations within more than 50 kb non-coding region in murine embryonic stem cells. CTRL-Mutagenesis would apply for wider non-coding regulatory elements with no risk of non-targeted endogenous gene disruptions.” in the Abstract.
• Delete “Comparative analysis of mutants harbouring subtly different mutations within the same region would facilitate the further study of cis-element and microRNA clusters.” in the Abstract (page2, line 38-40).
• Change “The generated random mutant mES clone library could facilitate further functional analyses of non-coding regulatory elements within the genome.” to “The generated random mutant mES clone library could develop to investigate critical regions of non-coding regulatory elements within the genome.” In the Introduction (page4, line 88-90)

  2, Genotypes of mutant library, especially Mirc56, 14,15, 16, 17 were not determined due to six tandem repeats. Thus, analysis of the relationship between genotype and biological functions is not possible. Moreover, the authors did not show any phenotypic analysis.

→ Thank you very much for your suggestion.

The 6 tandem repeats consisted of each approximately 3.3 kb are hard to determine mutations and are uncommon.

Therefore, we skipped genotyping Mirc56_14, 15, 16, and 17

Certainly, it is drawback that we did not determine all mutations induced by CRTL-mutagenesis.

Even so, we could determine the properties of mutant library within 37 kb genomic region from Mirc56_1 to Mirc56_13.

Therefore, we could conclude that CTRL-mutagenesis could induce diverse combinations and variations of mutations into more than 50 kb.

3, Multiple gRNA may cause deletion and inversion to targeted loci. With local PCR based amplification, detection of large deletion and inversion can be very difficult. I think the authors should examine and address this possibility more carefully. The definition of indel in Fig 5C should be explained in more detail.

→ Thank you very much for your comment, and we agree with your suggestion.

We did not confirm inversion and large deletion.

To confirm whether inversions were happened, we are going to perform PCR walking in several clones and long-read sequencing.

4, Although the authors showed a variety of PB cassettes (Max is 17), more importantly would be to determine the actual copy number of PB cassettes. Difference between the highest and the lowest EGFP intensities in Fig 2C (Donor 300ng Effector 350ng) is approximately ~100 fold, thus ES clone bearing highest PB vector may contain ~100 copies of PB vector. PB transposon prefers insertion in active genes compared to other transposon system such as Sleeping Beauty and Tol2 transposon. (Yoshida J et al Sci Rep. 2017 Mar 2;7:43613. doi: 10.1038/srep43613.). Higher integration rates of PB vectors have a higher chance of endogenous gene disruptions and may impair functional analysis.

→ Thank you very much for your suggestion.

We agree that cassette integration number is one important aspect of tiling mutagenesis. To determine actual copy number of PB transposon is useful information when potential user consider optimizing our method for own target region. However, to confirm whether the relationship between mutations induced and sgRNA cassettes integrated, the number of integrated cassette variety is more important because the diversity of sgRNAs variety expressed is more related to the diversity of mutations induced. Therefore, we identified the number of integrated cassette variety.

To clarify this point, we will add we the following sentences:

“rather than the copy number of sgRNA cassettes because the diversity of sgRNAs variety expressed is more related to the diversity of mutations induced” following to “…the number of sgRNA cassette varieties.” in the Result (page12, line 297)

Certainly, we apologize that it is not accurate that “EGFP signal intensity correlated with the copy number of EGFP cassettes integrated into genomes[23]” in the Result (page11, line 249-250). EGFP expression levels are affected by cell cycle so that the paper reported that “Median EGFP intensities correlated with the copy number of EGFP cassettes integrated into genomes”.

Therefore, we will delete the following sentence:

“EGFP signal intensity correlated with the copy number of EGFP cassettes integrated into genomes[23]” in the Result (page11, line 249-250).

To investigate how many copies our concentration of donor vector could integrate, we are going to check actual copy numbers in several clones by qPCR.

Besides, we agree with your suggestion that “PB transposon prefers insertion in active genes compared to other transposon system such as Sleeping Beauty and Tol2 transposon. (Yoshida J et al Sci Rep. 2017 Mar 2;7:43613. doi: 10.1038/srep43613.)”

Therefore, we will change the following sentence:

“random TTAA sites across genomes [24]” to “random TTAA sites of transcribed region rather than intergenic region [PMID: 28252665]” in the Discussion (page14, line 357).

However, Sleeping Beauty and Tol2 transposon remain footprint at integration sites when these transposons move [PMID: 15133768, 23143102]. Especially, SB transposon leaves canonical 5 bp insertion at integration sites so that the canonical 5bp insertion into coding sequence could disrupt the function of endogenous protein frequently. On the other hand, PB transposon remains no footprint. Therefore, excision-only-PBase can remove the PB transposon from mutant library clearly. Thus, it is no worry about that PB transposon disrupt non-targeted endogenous gene impair functional analysis if PB mutant library is treated with excision-only-PBase.

In addition, we are going to conduct transposon removal by exicision-only-PBase treatment with several PB mES clones, for the proof of concept that CTRL-Mutagenesis can generate mutant library with no sgRNA cassettes.

5, Most non-coding regions are located at autosomes. Genotyping would be very difficult or even impossible by the current PCR based strategy.

→ Thank you very much for your comment, and we agree with your suggestion.

This is one of our issues.

We expect that CTRL-Mutagenesis could be valid on other biallelic locus.

Therefore, we raised predicted issue such as complex genotyping and proposed one solution.

When we target other biallelic locus, we must determine whether the combination of mutations induced are cis- or trans-mutations. Haplotype phasing, combined long-read sequencing with SNP markers within ROI on maternal/paternal chromosome, assembles each allele via SNP markers on each read [PMID: 35710642]. Therefore, combining CTRL-Mutagenesis on heterozygotic alleles of cells derived from such as human or murine hybrid with haplotype phasing might simplify genotyping.

We will add the following sentences:

“In this study, CTRL-Mutagenesis was validated by genotyping on mono allele in male mES cells to avoid investigating whether the combination of mutations induced are cis- or trans-mutations. All genotypes on Mirc56 should be hemizygous and these mutations induced might be cis-mutations so that we determined the genotypes by amplifying approximately 200 bp around the target sites. However, we did not confirm large mutations such as deletion of the genomic region between target sites and inversion. Long-read sequencing might capture their large mutations. Besides, we also expect that CTRL-Mutagenesis could be valid for ROI on biallelic autosome and X chromosome in female. Therefore, it is required to determine whether the combination of mutations induced are cis- or trans-mutation. Haplotype phasing, combined long-read sequencing with SNP markers within ROI on maternal/paternal chromosome, assembles each allele via SNP markers on each read [PMID: 35710642]. Therefore, combining CTRL-Mutagenesis on heterozygotic alleles of cells derived from such as human or murine hybrid with haplotype phasing might simplify genotyping.” in the Discussion.

Moreover, genome-wide NGS and nanopore Cas9-treated sequencing (nCATs) could also help us to read the mutations without PCR-amplification. However, both methods can obtain reads of target regions with low frequency. Therefore, it is difficult to perform multiplex samples for mutant library.

*6, Fig 4C, large amounts of Cas9 independent EGFP positive cells suggest the current system is not efficient. *

→ Thank you very much for your comment.

We cannot agree with your indication.

In fact, by the cutoff set in Cas9-untreated cells, the EGxxFP system successfully selected at least 76 mutant clones (87.4%) harboring mutations within Mirc56_1 to Mirc56_13. Moreover, we could seed 180 single-cells for single cloning by FACS once.

To enhance this point, we added the following sentences:

“Moreover, at least 76 out of 87 PB mES clones have mutations within all analysed Mirc56_Xs (Figure 5C). Therefore, the EGxxFP system could selected ROI mutant mES clones efficiently.” following to “…depended on integrated sgRNA cassettes.” in the Discussion (page13, line 355)

*Reviewer #4 (Significance (Required)):

The authors claim "Functional analysis" in the manuscript title but there is no evidence of functional analysis in the manuscript.*

→ Thank you very much for your suggestion, and we agree with your suggestion.

In this paper, we just validated PiggyBac system for CRISPRko tilling mutagenesis and expanded the length of target regions.

To change our tone that claiming usability of our method for functional analysis, we will change the following sentences:

• Change “to identify functionally important elements in non-coding regions” to “to induce diverse combination and variety of mutations within more than 50 kb non-coding region” in the Title.
• Add “However, not much loss-of-function screens of non-coding regulatory elements has been conducted due to ambiguous annotations compared with protein-coding genes. Tiling mutagenesis has been employed to identify critical regions embedded in non-coding regulatory elements by comparative analysis through a mutant library harbouring subtly different regions mutated within less than 15 kb region. Conventional tiling mutagenesis construct a mutant library integrated multiple sgRNA cassettes by retroviral delivery. However, multiple integration of single guide RNA (sgRNA) cassettes has higher risk of non-targeted endogenous gene disruptions and may impair functional analysis. Herein, combining tiling mutagenesis and PiggyBac transposon that can be removed with no footprint on integrated sites, we established an expanded tilling mutagenesis method named CRISPR- & Transposase-based RegionaL Mutagenesis (CTRL-Mutagenesis). We demonstrated that PiggyBac system could integrated diverse combinations and varieties of sgRNA cassettes.and then CTRL-Mutagenesis randomly induces diverse combination and variety of mutations within more than 50 kb non-coding region in murine embryonic stem cells. CTRL-Mutagenesis would apply for wider non-coding regulatory elements with no risk of non-targeted endogenous gene disruptions.” in the Abstract.
• Delete “Comparative analysis of mutants harbouring subtly different mutations within the same region would facilitate the further study of cis-element and microRNA clusters.” in the Abstract (page2, line 38-40).
• Change “The generated random mutant mES clone library could facilitate further functional analyses of non-coding regulatory elements within the genome.” to “The generated random mutant mES clone library could develop to investigate critical regions of non-coding regulatory elements within the genome.” In the Introduction (page4, line 88-90).

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

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Referee #4

Evidence, reproducibility and clarity

Morimoto et al. presented a regional random mutagenesis study using multiple sgRNAs in PiggyBac transposon vectors to analyze the relationship between genotype and biological functions. For proof of principle, authors chose the X-linked miRNA cluster Mirc56 and made its mutant library.

Major concerns

1. Authors claim "to identify functionally important elements in non-coding regions in the title but there is no evidence of any functional analysis in the manuscript.
2. Genotypes of mutant library, especially Mirc56, 14,15, 16, 17 were not determined due to six tandem repeats. Thus, analysis of the relationship between genotype and biological functions is not possible. Moreover, the authors did not show any phenotypic analysis.
3. Multiple gRNA may cause deletion and inversion to targeted loci. With local PCR based amplification, detection of large deletion and inversion can be very difficult. I think the authors should examine and address this possibility more carefully. The definition of indel in Fig 5C should be explained in more detail.
4. Although the authors showed a variety of PB cassettes (Max is 17), more importantly would be to determine the actual copy number of PB cassettes. Difference between the highest and the lowest EGFP intensities in Fig 2C (Donor 300ng Effector 350ng) is approximately ~100 fold, thus ES clone bearing highest PB vector may contain ~100 copies of PB vector. PB transposon prefers insertion in active genes compared to other transposon system such as Sleeping Beauty and Tol2 transposon. (Yoshida J et al Sci Rep. 2017 Mar 2;7:43613. doi: 10.1038/srep43613.). Higher integration rates of PB vectors have a higher chance of endogenous gene disruptions and may impair functional analysis.
5. Most non-coding regions are located at autosomes. Genotyping would be very difficult or even impossible by the current PCR based strategy.
6. Fig 4C, large amounts of Cas9 independent EGFP positive cells suggest the current system is not efficient.

Significance

The authors claim "Functional analysis" in the manuscript title but there is no evidence of functional analysis in the manuscript.

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

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

The study proposes a method utilizing EGxxFP, piggybac, and CRISPR-Cas9 systems to generate a random mutation library in non-coding genomic regions, such as cis-element regions or microRNA clusters. As a proof-of-concept of this method, a random mutation library of Mirc56 microRNA cluster was generated. The manuscript highlights the creation of regional mutations using mES cells.

Major comments:

Authors claim that "CTRL-mutagenesis randomly induces diverse mutations only within the targeted regions in murine embryonic stem (mES) cells.", however, the outcome of mutations is not entirely random since most of the mutations are regional deletions. For example, despite the random distribution of gRNAs per cell, the inner regions like Mirc56_5 or Mirc56_8 are mutated with >80% efficiency. Also, although the authors discuss that the lower mutation frequency observed for Mirc56_2 and 4 may be due to a technical error, confirming this by repeating the experiment would be important to prove the usability of this method. Additionally, the experiments were performed on the haploid X chromosome of a male cell line. It is questionable whether this method can be generalized to other regions located in the other chromosomes. Clarifying These points would be essential especially because the focus of this manuscript is to describe the efficiency of this novel methodology.

The limitations of the methods seem not to be fully described in the manuscript and must be clarified. Compared to the previous studies (see "significance" section for details), this method is inferior in that (1) it is time-consuming because it requires clonal expansion of single cells and (2) it has low throughput because it requires genome sequencing due to the occurrence of deletions. These points should be described for the potential users of this methodology. For example, it may be useful to detail the time consumption in each experimental step in Fig. 4A.

Minor comments:

Data and methods are well-presented for reproducibility. The EGFP-positive ratio may be added to Fig. 4C for clarity.

Enhance referencing accuracy, rectify DOI format in ref 21, and ensure consistency in citation formatting, e.g., ref 32.

It seems that the experimental condition (e.g. The amount of vectors used for transfection) should be re-considered every time the researcher wants to set up an experiment changing target genomic regions, cell types etc. If so, this also should be described in the text for potential users of this method.

Referees cross-commenting

Major concerns raised by the reviewers, including the non-random nature of mutations, challenges in library resolution, and unclear advantages over existing methodologies, all seem to be reasonable. These concerns should be addressed before publication, especially because this is a methodology paper that reports the usability of this novel methodology.

Significance

The method combines CRISPR screens with EGxxFP and PiggyBac systems for complex cell library generation, albeit with limitations in throughput and time consumption.

There were various methods described in the late 2010's which aimed to screen for the functional non-coding regions using approaches such as KO-based, HDR-based, and epigenetic silencing using dCas9 (for example, PMID: 25141179, 26751173, 27708057, 28416141, 31784727). The authors should summarize what would be the strength of their method compared to these previously described methodologies. The strength of this methodology seems to be moderate complexity and cost-effectiveness compared to these previous techniques. It may be difficult for this methodology to become a state-of-the-art method to evaluate cis-element combinations, but it can be beneficial to researchers wanting to set up a low-cost system that can produce moderately complex cell libraries.

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Referee #2

Evidence, reproducibility and clarity

In this paper, Morimoto et al. present CTRL-Mutagenesis, a method for region-specific random mutagenesis, aiming to identify functionally important elements in non-coding regions of the genome. While the idea to integrate sgRNA in the genome by the PiggyBack system is interesting there are several major concerns that limit the novelty and impact of this study as outlined below.

Major concerns:

1. Concern about the Novelty of Functional Analysis Platforms: The authors claim that there are no established platforms for the study of cis-elements or microRNA clusters. This assertion seems inaccurate, as previous studies have utilized Cas9 tiling screens to investigate cis-regulatory elements (CREs) and large-scale screens to probe microRNA functions, as exemplified by the works of Canver et al. in Nature 2015, Gasperini et al. in Cell 2019, and others.
2. Advantages of PiggyBack System Over Lentiviral Integration: The paper does not clearly articulate the advantages of their proposed PiggyBack-based system for sgRNA integration over traditional lentiviral integration. Both methods facilitate the random integration of multiple gRNAs, but the paper lacks a comparative analysis or justification for choosing the PiggyBack system.
3. Lack of Comparative Analysis with Alternative Methods: The authors did not provide a comparison of CTRL-Mutagenesis with other existing screening methods. Such a comparison is crucial for understanding the effectiveness and efficiency of the new method in relation to established techniques.
4. Limitations in Library Resolution: The paper acknowledges the limited resolution of their proposed library. The authors might have explored the use of base editors for enhanced resolution in such screens, as base editing could potentially offer more precise and controlled mutagenesis as briefly mentioned in the discussion.
5. Absence of Functional Data Post-Mutagenesis: A significant limitation of the study is the absence of functional data following the creation of cells with different mutations. While the authors speculate about using differentiation systems or organoids for practical applications, they do not provide empirical data to demonstrate the utility of the CTRL-Mutagenesis approach. This lack of functional validation raises questions about the practical applicability of the method.

Significance

In summary, while the idea to integrate sgRNA in the genome by the PiggyBack system is interesting the claim of novelty is questionable due to existing methods in the field. The advantages of their system over existing technologies are not clearly articulated, and a lack of comparative analysis with other methods leaves the efficiency of CTRL-Mutagenesis uncertain. Moreover, the limited resolution of their library and the absence of functional data post-mutagenesis are significant drawbacks that need to be addressed in future research to ascertain the method's practical utility.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In "Regional random mutagenesis driven by multiple sgRNAs and diverse on-target genome editing events to identify functionally important elements in non-coding regions", Morimoto et al. detail a method for generating clonal cell lines containing mutations tiled across a region of interest. Briefly, they create a pool of sgRNAs tiling a region of interest, then utilize the PiggyBac transposase to insert random sgRNAs from this pool into cellular DNA. Cas9 cleavage directed by cellular sgRNAs creates small indels and large deletions in cells that can be grown out into clonal cell lines. They apply their method to study the Mirc56 microRNA cluster to generate 87 clones, each clone being edited by an average of 4.7/17 sgRNAs. The authors suggest that these cell lines could be used to elucidate the functional importance of non-coding regions.

Major comments:

1. Mirc56_2 and 4 showed lower integration rates, and the authors suggest that this could be due to sgRNA pool imbalance. The authors should validate this by performing sequencing of the input sgRNA and cassettes.
2. Clonal analysis in Figure 5c is unclear
   • a. Figure 5c indicates that all changes were homozygous (e.g. both alleles were deleted). Was this the case in all clones? Or were some mutations heterozygous?
   • b. Many clones in Figure 5c show that the entire region was deleted (all black dots). Could this be due to some experimental error or misinterpretation of the sequencing data, or could it be validated using some orthogonal method? This is especially surprising for clones in which the final guide (Mirc56_13) was not detected yet the final site (Mirc56_13) was reported as "Regional deletion".
3. Next-generation targeted sequencing of clones should be made publicly accessible.
4. OPTIONAL - Cassette integration number is understudied. One important aspect of tiling mutagenesis is the control over how many guides are present in each cell. The authors report an average of 4.7 cassettes/cell. This could be modulated by the amount of donor vector added, and indeed the authors performed titration experiments, but only with a fluorescent reporter readout. It would be very useful to know how the concentration of donor vector corresponds to the number of cassettes/cell - perhaps genotyping of clones from one or two additional experiments would be sufficient.

Minor comments:

1. The background fails to acknowledge the work of CRISPR-Cas tiling screens (e.g. https://doi-org/10.1038/nbt.3450) or CRISPR-Cas in creating mutagenesis in cell lines (e.g. https://doi-org/10.1007/978-1-0716-0247-8_29)
2. Figure 1 left 'ROI random mutant PB mES cell' should be horizontally aligned so Mir_1, Mir_2 and MirX align with the upper figure.
3. It is interesting and unexpected that some guides never induce indels, even in the absence of a regional deletion (e.g. Mirc56_3, Mirc56_7). Why might this be? Was there perhaps an error in the assignment of these guides to these cells?
4. Regarding Mirc56_2 and 4 integration, on line 34 the authors suggest that "We suspect this was caused by a technical error, such as an unequal amount of sgRNA donor vector or the sequence in sgRNA cassettes affecting integration efficiency or cell growth." sgRNA library imbalance would be a technical error, but integration affecting cell growth is not a technical error. This sentence should be reworded.
5. Line 540 "ration" is the incorrect word - perhaps "ratio"?
6. Plot 5b should be shown as a histogram rather than a swarm plot to show how many clones were in each category.

Referees cross-commenting

All reviewers note previous functional non-coding screens and the lack of justification of the author's PiggyBac system. The authors should consider strengthening the justification and adding comparisons to existing methods if future revisions are considered.

Significance

General assessment: The authors are successful in creating clonal cell lines bearing a variety of mutations. Unfortunately, the cell lines also have transposase-mediated insertion events of the sgRNA cassettes at unknown positions in the genome, which will hamper the interpretability of any experiment using these cell lines. The authors fail to justify the use of the transposase and integration of the sgRNA, especially compared to lentiviral transfection or RNPs which would produce edits at the region of interest. Alternately, integrated sgRNA cassettes could have been excised with Flp recombinase as in https://doi-org/10.1007/978-1-0716-0247-8_29. Additionally, the genotyping analysis is unclear, and seems to indicate that each clone bears homozygous mutations, with several clones showing deletions of the entire region.

Advance: The authors are motivated to create clones using tiling mutagenesis. Tiling mutagenesis has already been performed without transposases (e.g. https://doi-org/10.1038/nbt.3450, https://doi.org/10.1371/journal.pone.0170445, https://doi.org/10.1038/s41467-019-12489-8) in the context of a screen, and clones have already been created using CRISPR/Cas9 mutagenesis so the advance presented in this manuscript over previous published work is unclear.

Audience: The manuscript is written for the basic research audience, and the method could be applied to the study of regions of interest in many diseases. However, the unexcised use of transposases make the method less desirable than other methods.

I am a computational biologist with experience in CRISPR tiling screens and CRISPR amplicon sequencing analysis.

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Reply to the reviewers

Review Commons - Revision Plan

Manuscript number: RC-2023-02228

Corresponding author(s): Gatfield, David

1. General Statements

We are grateful to the three Reviewers for their detailed assessment of our manuscript and are delighted about their very constructive and positive evaluations, highlighting the study’s novelty and rigor.

Briefly, the main points raised by Reviewers 1 and 3 do not involve additional experiments and are mostly about rethinking manuscript structure (e.g. moving data/analyses to the supplement or removing them altogether, as they distract from the main thrust of the story) and making the text overall less dense and more readable.

Reviewer 3 also raises a number of additional interesting points that we should discuss in our manuscript, which would allow us placing our findings more effectively into the context of the existing literature.

All these points are very well taken and will be implemented (see below, under 2).

Reviewer 2 is overall also rather positive – speaking of “a very careful and detailed study that addresses an important issue” and the study being “really rigorous and the logic […] very well explained”; moreover, this Reviewer also shares the view of both other Reviewers that parts of the manuscript (i.e., in particular its beginning) should be shortened.

Importantly, this Reviewer remarks in addition under “Significance”: “Without additional mechanistic insights suggesting that there is something particular different about the regulation of these mRNAs the manuscript is not of extremely high significance.” – an important point of criticism that we wish to address in our revision, as detailed below.

2. Description of the planned revisions

In the following, we detail how we plan to address the points raised by the Reviewers. The order in which we treat the points follows their – in our view – relative importance according to the Reviewers’ feedback. In particular the first item below, under (A), is the main point of criticism that we feel we should address carefully for the future revised version.

(A) Major point raised by Reviewer 2: “However, the study falls short on addressing the mechanism of this regulation and if it is different of other feeding regulated mRNA oscillations. This diminishes the significance of the study unless additional mechanistic details are provided.” , which is cross-commented both by Reviewer 1: “More importantly, clues to the mechanism (e.g. iron, heme) regulating the rhythmic translation of IRP1 and IRP2 IRE-mRNAs in liver would increase the significance of the work.” as well as by Reviewer 3: “Reading the comment from Reviewer #2 over the lack of a mechanism to explain why only four transcripts with IREs amongst a larger pool are subject to circadian regulation by IRPs somehow reduces the significance of the study, one has to agree that a discovery - likely another component in the system - is wanting. I remain of the view that the present work exposes this "weakness" of the entire field in a global as opposed to a partial manner and in doing so, makes a significant contribution, especially by further sub-classifying the IRE-containing transcripts according to their responsiveness in the diurnal occupancy of their IREs.”

Our response and revision plan: Indeed, in the original version of our manuscript we established the link to feeding, yet we did not pinpoint the precise molecular cue that could underlie the rhythmic regulation observed on certain IRE-containing mRNAs. We did discuss the molecular candidates quite extensively in the Discussion section of the manuscript (Fe2+; oxygen; reactive oxygen species), and it remains quite obviously the main question whether the observed diurnal control could be mediated directly by changes in intracellular iron availability.

Of note, the preprint by Bennett et al., for which we cite the initial biorXiv version in our manuscript, was updated very recently (https://doi.org/10.1101/2023.05.07.539729 – see version submitted December 18, 2023). It now includes new data that analyses around-the-clock iron levels also in liver. Briefly, the preprint shows, first, that serum iron is rhythmic with a peak during the dark phase at ZT16 (Figure 1D in Bennett et al.) yet loses rhythmicity when feeding is restricted to the light phase (Bennett et al., Figure 2E), indicating both feeding-dependence and circadian gating. Moreover, liver total non-heme iron – quantified using a method that measures both ferrous Fe(II) and ferric Fe(III) – shows low-amplitude diurnal variations which, however, do not meet the threshold for rhythmicity significance (Bennett et al., Figure 3G). Still, the difference between timepoints ZT4 (lower iron; light phase) and ZT16 (higher iron; dark phase) is reported as significant, with a fold-change that is not very pronounced (not compatible with the observed direction of regulation of Tfrc mRNA, whose higher abundance in the dark phase would rather be in line with lower *cytoplasmic iron levels, as pointed out by the authors.

Thus, at first sight the analyses by Bennett et al. would appear to answer part of the Reviewer’s question and point towards other mechanisms of regulation than iron levels themselves. However, it should be pointed out that the particular methodology for iron measurements used by the authors includes the use of reducing reagents and hence quantifies the sum of Fe2+ and Fe3+ iron. Large amounts of iron are stored in the liver in the form of ferritin-bound Fe3+, yet the bioactive, low-complexity iron that is considered relevant for IRP regulation is in the Fe2+ form. Therefore, the question whether bioactive ferrous iron levels follow a daily rhythm, compatible with the observed IRP/IRE rhythms described in our manuscript, still remains an open question and warrants a dedicated set of experiments that we are proposing to conduct in response to the Reviewers’ comments.

Briefly, for the revision we propose to use liver pieces from the two relevant timepoints of our study (i.e., ZT5 and ZT12) and apply a method that allows the separate quantification of Fe2+ and Fe3+ (Abcam iron assay ab83366; this assay can be adapted to liver iron measurements, see e.g. PMID31610175, Fig. 4A). This experiment will provide novel and decisive data on the molecular mechanism that may regulate the IRP/IRE system in a rhythmic fashion and therefore add to the significance of our findings, as requested by the reviewers.

Moreover, we believe that the outcome of the experiment would be very interesting either way, i.e. if we find rhythms in Fe2+ that are compatible with rhythmic IRP/IRE regulation, we would be able to provide excellent evidence in term of likely molecular mechanism and rhythmicity cue. If, by contrast, we find that Fe2+ is not rhythmic, it will point towards a mechanism that is distinct from simple Fe2+ concentrations.

In the latter case, collecting additional evidence on relevant alternative molecular cues would be beyond our capabilities for this particular manuscript, as it would require quite sophisticated methodological setup and preparation. For example, one could imagine that measuring around-the-clock liver oxygen levels in vivo – another candidate cue – would be highly interesting, yet we would not be able to conduct these experiments in a reasonable time frame (to start with, we would first need to request ethics authorisation from the Swiss veterinary authorities, which would in itself take ca. 4-6 months before we could even start an experiment). Thus, in the case of non-rhythmic iron levels, we would leave the question of other responsible cues open, but still think that with a balanced discussion of the resulting hypotheses we could provide significant added value to our work.

(B) Major comment raised by Reviewer 1: “Alas2 is expressed mainly in erythroid cells and not liver, whereas Alas1 is ubiquitously expressed. Therefore, it is possible that Alas2 in this study may originate from red cells/reticulocytes in the liver, and not from hepatocytes.”

Our response and revision plan: We would like to thank the Reviewer for the comment that is indeed pertinent. It is well established that Alas1 is the main transcript encoding delta-aminolevulinate synthase activity in hepatocytes, and Alas2 is about 10-fold less abundant in total liver RNA-seq data (quantified form own RNA-seq data, not shown).

We are nevertheless relatively sure that the Alas2 signal comes from low expression in hepatocytes; the best argument in support of this hypothesis is the analysis of single-cell RNA-seq data, as shown in the following Revision Plan Figure 1, which we would be happy to include in a revised version of the manuscript if the reviewers wish:

(C) Minor comment raised by Reviewer 1: “The paper is dense and not easy to read. For example, the section on Tfrc regulation and NMD regulation is lengthy and perhaps not necessary for the paper and the section on "Previous observations in IRE-IRP regulation...." could be included in the discussion rather in than in the Results section. Some figures could be included in a supplement.” continued in Referee cross-commenting “I agree with Reviewer 2 that the first sections in the manuscript are lengthy and not needed.”; moreover, Reviewer 2: “Also, the manuscript first sections (which mainly describe negative results) seem too long and descriptive.”

Our response and revision plan: We shall reorganize the paper accordingly, with the aim of making it an easier, shorter, clearer read. Many thanks for the input.

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(D) Minor comment raised by Reviewer 1: “A description of the new anti-IREB2 antibody is needed. What IRP2 sequence was used to generate antibodies?”

Our response and revision plan: The following information will be included in the manuscript: “Rat monoclonal antibodies against ACO1/IRP1 and IREB2/IRP2 were generated at the Antibodies Core Facility of the DKFZ. Briefly, full-length murine ACO1/IRP1 and IREB2/IRP2 proteins, fused to a poly-histidine tag, were expressed in E. coli and purified on Ni-NTA columns using standard protocols. Purified His-tagged proteins were used to immunize rats and generate hybridomas. Hybridoma supernatants were first screened by ELISA against His-tagged ACO1/IRP1 and His-tagged IREB2/IRP2. As an additional control, supernatants were tested against full-length His-tagged murine ACO2 (mitochondrial aconitase), which shares 27 and 26% identity with ACO1/IRP1 and IREB2/IRP2, respectively. Supernatants reacting specifically with ACO1 or IREB2 were validated by western blotting using extracts from wild-type versus ACO1- or IREB2-null mice.”

(E) Minor comment raised by Reviewer 1: “A model summarizing the data would be useful.”

• *Our response and revision plan: Thank you for the suggestion – this will be done.

(F) “Optional” idea raised by Reviewer 3: “One nuance in the field of circadian biology is that a rhythm is deemed to be genuinely "circadian" when it continues in the absence of zeitgebers. In this sense, although all experiments are valuable, the "collapse" of the rhythm in the paradigms where dietary rhythms have been disrupted makes the phenomenology a candidate "epiphenomenon" rather than being closer related to the biological clock(s). Likewise, in the manuscript we never learn how the liver IRE-binding activity behaves in constant darkness.”

Our response and revision plan: This is an important aspect that we can clarify more specifically in our manuscript. It is true that constant (darkness) conditions are used to call a phenomenon circadian. We would nevertheless argue that for a rhythmic feature that is specifically found in liver, the constant darkness definition to distinguish circadian from non-circadian is not fully valid because even in constant darkness, the liver clocks are not in a free-running state but continue to be entrained by the SCN clock (it is only the latter that is free-running under these conditions).

In our manuscript, we actually suggest that the observed rhythms are not a core output of the circadian machinery (Fig. 6 of our manuscript), but indirectly engendered through feeding rhythms, which are coupled to sleep-wake cycles and thus connect in an indirect way to the central circadian clock activity in the SCN.

In wild-type mice we would therefore expect that irrespective of constant darkness or light-dark entrainment (and assuming ad libitum feeding), the hepatic rhythms of the relevant IRE-containing transcripts would persist in a similar fashion.

(G) “Optional” idea raised by Reviewer 3: “Where the authors mention in a parenthesis "moreover, there are documented links between iron and the circadian timekeeping mechanism itself", I invite them to take a closer look to the paper Konstantinos Mandilaras and I coauthored in 2012 "Genes for iron metabolism influence circadian rhythms in Drosophila melanogaster". In that work, we showed that RNA interference of genes that are required for iron sulfur cluster formation (including on IRP1) in the central clock neurons of the fly result in loss of the circadian rhythm when flies were kept at constant darkness (not so when they were kept under light:dark oscillation). So this point should probably remain open..”

Our response and revision plan: We would like to thank the Reviewer for pointing out this interesting connection that would fit well into the context of our manuscript. It should be cited in the context of our current Figure 3, where we measure in vivo and in tissue explants whether IRP-deficiency affects the clock itself.

To follow Reviewer 3’s idea, we have gone a little further in our analyses of around-the-clock expression data to see if any of the components of the Fe-S assembly machinery is rhythmic itself, which could have the potential to add novel information.

Briefly, we have used for this purpose our around-the-clock RNA-seq and ribo-seq data from PMID 26486724. In summary, we find that the expression at RNA and/or footprint level is non-rhythmic for the vast majority of genes involved in FeS biogenesis, assembly or transport, with the exception of low-amplitude rhythms for Glrx5 and Iba57 (Revision Plan Figure 2).

By contrast, all of the following other genes are non-rhythmic throughout (list of Fe-S-relevant genes from PMID34660592): Cytoplasmic/nuclear, all non-rhythmic: Cfd1=Nubp2, Nbp35=Nubp1 , Ciapin1, Ndor1, Iop1=Ciao3=Narfl, Ciao1, Ciao2b=Fam96b, Mms19, Ciao2a=Fam96a; mitochondrial, all non-rhythmic: Iscu, Nfs1, Isd11=Lyrm4, Acpm=Ndufab1, Fdx1, Fdx2=Fdx1l, Fxn, Hspa9 Hsc20=Hscb, Abcb7, Alr=Gfer, Isca1, Isca2, Nfu1

As these are mainly “negative results”, and as we are also unable to propose a solid possible mechanistic connection between the Glrx5 and/or Iba57 rhythms and the rest of the story of our manuscript, we do not intend to include such data in our manuscript, but are only putting it for the record into this rebuttal.

3. Description of the revisions that have already been incorporated in the transferred manuscript

NONE

4. Description of analyses that authors prefer not to carry out

NONE – we think we can address all points as described above.

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Referee #3

Evidence, reproducibility and clarity

The present manuscript highlights the previously neglected component of diurnal rhythms into the study of iron regulation in the liver, a key organ in the systemic regulation of the metal. A major, well substantiated finding is that IRP1 takes over from IRP2 as a highly relevant regulator during a time of maximal use of the combined system. The presence of a "dietary signal" that sustains the cycling of cellular IRE binding activity in the liver, although undisputable, is perhaps a lesser claim until these or other investigators can confirm or refute the possibility that iron itself (i.e., the best-established factor affecting cellular IRE-binding) is such a signal. If iron does the job, then the interest lies in showing diurnal rhythmicity of its availability in the circulatory system, presumably linked to dietary iron absorption. There is plenty of clinical evidence of this in humans, but the present study along with the cited preprint by Bennett et al. appear to be the first demonstrations of this diurnal variation in mice.

The manuscript has other strengths not immediately evident from the above claims made in the abstract. It contains an elegant balance of reanalyzing and reassessing "big data" produced by the same laboratory in the past in light of new experimental findings that have appeared in the meantime in the literature together with important new additions of such data from combined RNAseq and ribo-seq collections using IRP1 and IRP2 knockout animals and, importantly, by making use of published material from other studies that have provided relevant comparators from other knockouts that studied aspects of liver circadian biology. The approach, besides providing robust testing of the ideas presented, opens the field to questions that remain unanswered but seem highly relevant (I come to these below). The authors write in a very open manner not only about the new findings but also about aspects we do not understand, and their systems biology approach is likely to generate new hypotheses to address incognita.

Let me therefore be clear upfront that the response that follows is written on the premise that I evaluate the work presented as ready for publication: The figures have been constructed with care summarizing a lot of careful investigations and the main conclusions derive seamlessly from the experimental data. Rather than taken as potential criticism to the authors, I would ask that the counterviews or limitations that may arise from my response to the paper are better taken as a celebration of the work - and views - presented. Such a discussion is only possible due to the open style of this communication mentioned above and is meant to provoke a dialogue or even drive further questioning of the datasets and the design of future experimental approaches. If the authors find any of these comments useful for their revision, they are welcome to take them onboard, but everything that follows should be read under the term "optional".

One nuance in the field of circadian biology is that a rhythm is deemed to be genuinely "circadian" when it continues in the absence of zeitgebers. In this sense, although all experiments are valuable, the "collapse" of the rhythm in the paradigms where dietary rhythms have been disrupted makes the phenomenology a candidate "epiphenomenon" rather than being closer related to the biological clock(s). Likewise, in the manuscript we never learn how the liver IRE-binding activity behaves in constant darkness. Where the authors mention in a parenthesis "moreover, there are documented links between iron and the circadian timekeeping mechanism itself", I invite them to take a closer look to the paper Konstantinos Mandilaras and I coauthored in 2012 "Genes for iron metabolism influence circadian rhythms in Drosophila melanogaster". In that work, we showed that RNA interference of genes that are required for iron sulfur cluster formation (including on IRP1) in the central clock neurons of the fly result in loss of the circadian rhythm when flies were kept at constant darkness (not so when they were kept under light:dark oscillation). So this point should probably remain open.

Given the phenotypes collected from RNAi in different cell types, we became sensitive to the notion that different cell types may work with different sets of what we might call collectively "iron metabolism genes". Thus, while reading the present differences between the relative contributions of IRP1 and IRP2 in mouse liver at different times during the day (and night), I kept wondering if both function in the hepatocytes or whether the macrophages or other cell types in the liver may have their own particular contributions.

Another issue raised by the authors early on relates to the differential effects of IRP1/2 "activation" on different IRE-containing transcripts. This is a fascinating problem, not answered by the six transcripts shown in figure 1G, but I consider that the present paper offers a great service to the field in figure 5I, where an even more comprehensive grouping of IRE-containing transcripts is provided in terms of their "regulation" by IRPs. Future research should attempt to discover features that correlate within the sets of transcripts, as grouped in here.

Thus, another point made repeatedly by the authors that despite four decades of work on the IRPs we still have open questions about how they "regulate" is well taken. In the same tone, their results in relation to IRP2 degradation show that the story of how the presence of iron leads to the degradation of IRP2 has not been fully elucidated, either.

Referees cross-commenting

Reading the comment from Reviewer #2 over the lack of a mechanism to explain why only four transcripts with IREs amongst a larger pool are subject to circadian regulation by IRPs somehow reduces the significance of the study, one has to agree that a discovery - likely another component in the system - is wanting. I remain of the view that the present work exposes this "weakness" of the entire field in a global as opposed to a partial manner and in doing so, makes a significant contribution, especially by further sub-classifying the IRE-containing transcripts according to their responsiveness in the diurnal occupancy of their IREs.

I would like to reinforce the comment of reviewer 1 with respect to the antibodies used in this study that should be made available to the community, given the specificity described. My congratulations to the authors.

Significance

A lesson, perhaps, for the field is that sometimes more than one mechanism may be at play in different cellular or physiological contexts, while vigorous testing requires time and resources and we should value examples of such care and openness, an example of which is offered, in my view, by the present study.

Fanis Missirlis

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Referee #2

Evidence, reproducibility and clarity

In the manuscript entitled "Diurnal control of iron responsive element (IRE)-containing mRNAS through iron regular proteins IRP1 and IRP2 is mediated by feeding rhythms", Nadimpalli et al. uncover and mechanistically dissect how the circadian clock and feeding regulates the expression of proteins involved in iron homeostasis in mice. The authors first utilized RNAseq and ribose data and found that a subset of mRNAs containing IREs display rhythmic translation in the liver and/or kidney. The authors then utilized previously published or newly generated datasets to study the origin of these oscillations. After a careful and thoughtful examination, they determine that the oscillations of those mRNAs in the liver are mainly driven by feeding-associated signals, although they are influenced by other factors. This is a very careful and detailed study that addresses an important issue. The study is really rigorous and the logic is very well explained. So overall this study is very solid and the main conclusion of the study (that the oscillations of those mRNAs are driven by feeding) is solidly established. However, the study falls short on addressing the mechanism of this regulation and if it is different of other feeding regulated mRNA oscillations. This diminishes the significance of the study unless additional mechanistic details are provided. Also, the manuscript first sections (which mainly describe negative results) seem too long and descriptive. Still this is an important and solid study.

Significance

The main issue this reviewer has with the manuscript is the significance. Without additional mechanistic insights suggesting that there is something particular different about the regulation of these mRNAs the manuscript is not of extremely high significance.

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Referee #1

Evidence, reproducibility and clarity

Summary

This paper provides evidence for the diurnal regulation of specific subset of iron regulatory elements (IREs)-containing mRNAs in liver by iron regulatory proteins 1 and 2 (IRP1 and IRP2) in mice. The authors show that IRP2 oscillates over 24 h period to regulate IRE-containing mRNAs in the light phase, and collaborates with IRP1 to regulate IRE-mRNAs in the dark phase.

Major Comments

The authors have carefully performed experiments, and convincingly show that 5'-IRE containing transcripts (Fth1, Ftl1, Fpn and Alas2) display significant amplitude rhythms in ribosome occupancy in liver. Tfrc mRNA, which harbors a 3' IRE, also showed a rhythmic pattern in both liver and kidney. The changes in IRE-containing mRNAs correlated with IRP2 protein abundance. Further studies performed using Aco1 and Ireb2 knockout mice showed that both IRP1 and IRP2 are required for rhythmic regulation of IRE-containing mRNAs. Overall, the findings in this paper are interesting and novel, and show for the first time that IRE-containing mRNAs required for maintenance of cellular iron metabolism and IRP2 are subjected to rhythmic regulation. Alas2 is expressed mainly in erythroid cells and not liver, whereas Alas1 is ubiquitously expressed. Therefore, it is possible that Alas2 in this study may originate from red cells/reticulocytes in the liver, and not from hepatocytes.

Minor Comments

The paper is dense and not easy to read. For example, the section on Tfrc regulation and NMD regulation is lengthy and perhaps not necessary for the paper and the section on "Previous observations in IRE-IRP regulation...." could be included in the discussion rather in than in the Results section. Some figures could be included in a supplement. A description of the new anti-IREB2 antibody is needed. What IRP2 sequence was used to generate antibodies? A model summarizing the data would be useful.

Referees cross-commenting

I agree with Reviewer 2 that the first sections in the manuscript are lengthy and not needed. More importantly, clues to the mechanism (e.g. iron, heme) regulating the rhythmic translation of IRP1 and IRP2 IRE-mRNAs in liver would increase the significance of the work. Overall, the findings are novel, and would be of interest to the iron metabolism and circadian rhythm fields.

Significance

Previous studies have reported a role for iron in altering gene expression and circadian rhythms in mice. The current manuscript extends these studies to show that several IRE-containing mRNAs in liver and IRP2 are subjected to rhythmic regulation. These findings will be interest to researchers in circadian rhythm and iron metabolism fields.

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Reply to the reviewers

We would like to thank our reviewers for their constructive criticism and for their appreciation and enthusiasm for our study. Some reviewers expressed opposing views, particularly when it came to the function and identity of the Cdt1-related protein in Toxoplasma gondii. To avoid redundancy in our response, we would like to make a brief statement. Toxoplasma gondii and other apicomplexan parasites utilize unique and highly unusual modes of cell division; numerous studies suggest that multiple phases can run concurrently in apicomplexan cell cycles. The best-known examples include the asynchronous S/M cycles in schizogony and concurrent mitosis and budding in Toxoplasma endodyogeny. These overlapping phases are not a feature exclusive to apicomplexans, since in budding yeast, cytokinesis initiates in G1 phase by marking the location of budding on the surface of the mother. Based on years of previous research and from our experience, we adjusted our approach by focusing on the processes that are associated with each cell cycle phase rather than on their temporal order. While the model of a conventional cell cycle guides our studies, we “follow the breadcrumbs” that we discover and the published studies to create a more accurate model of apicomplexan cell cycle instead of relying on the traditional cell cycle map employed by distantly related eukaryotes. Below are point-to-point responses to reviewers’ comments.

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

Summary: Hawkins et al. employ a reverse genetic approach to analyze the molecular function of the Toxoplasma gondii kinase Crk4 and the Toxoplasma gondii cyclin 4. The authors combine inducible depletion with imaging, (phospho-)proteomics, molecular modeling, and protein-protein interaction studies.

Major comments: - The major conclusion of the manuscript is that TgCrk4/TgCyc4 regulate entry into mitosis and that the primary role of TgCrk4 is to suppress DNA re-replication and chromosome re-duplication (lines 105-106). The authors also provide evidence that TgCrk4 interacts with TgCdt1, a DNA licensing factor ("TgCdt1" is missing in line 107). (had been corrected) By sequence homology, the authors found homologues of TgCrk4 only in apicomplexan parasites with binary division and concluded that the dominant division mode, presumably schizogony, is repressed in these organisms in favor of binary division. Indeed, internal budding and daughter cell formation is defective in the inducible depletion mutants of TgCrk4 and most experiments focus on this developmental stage. However, the analysis of preceding events, such as DNA replication is rather brief. If G2 is indeed regulated by TgCrk4/TgCyc4, one would assume that the parasites are post-S phase and the nucleus contains two copies of the genome, as indicated in Fig. 2C. The data shown in Fig. 3H and 7A, however, show that the TgCrk4 and TgCTD1 depletion induces a developmental arrest pre-S phase. This contradicts the main conclusions of the manuscript.

*We agree that the G2 location is odd for a conventional cell cycle model. Given the high possibility that cell cycle phases can overlap in apicomplexans, we determined the relative position of G2 phase in Toxoplasma endodyogeny by instead focusing solely on the processes that are attributed to a specific cell cycle phase (such as DNA replication for S phase, DNA re-replication for G2 phase, DNA segregation for mitosis). Our approach shows that Toxoplasma G2/M checkpoint operates upstream of SAC, which led to enrichment of parasites with replicated DNA (Fig. 3H and Fig. 7A), which places G2 at the end of S-phase. Our focus in the present study is on the G2 functions, the control of centrosome and chromosome reduplication, but we appreciate the suggestion to examine DNA replication in Toxoplasma, which could be investigated in future studies. *

Indeed, many data of this manuscript could support an alternative conclusion, i.e., that TgCrk4 regulates entry into S-phase (similar to Plasmodium falciparum Crk4: PMID: 28211852). This alternative conclusion is supported by the data showing that TgCyc4 is in the nucleus during S-phase (Fig. 1H) and that TgCrk4 interacts with TgCdt1, which has a well-known role in origin of replication licensing and loading of the MCM complex. MCM subunits were less phosphorylated in absence of TgCrk4, which could also suggest a role for TgCrk4 in S phase. Together, it seems more parsimonious to interpret the data as a DNA replication phenotype rather than a phenotype in G2.

*We understand some confusion from prior data, but PfCrk4 is not orthologous to TgCrk4 (Alvarez & Suvorova, 2017); The true TgCrk4 ortholog had not been found in Plasmodium genomes. Our understanding is that nuclear accumulation of TgCyc4 in S-phase activates TgCrk4, which leads to repression of the DNA reduplication. One of the possible mechanisms involves interfering with loading of the MCM complex on chromatin mediated by hyper-phosphorylated TgiRD1 (former TgCdt1), which has been reported in other eukaryotes. We also believe that increased MCM phosphorylation indicates entry into or active S-phase, while the reduced phosphorylation that was detected in Crk4-depleted cells supports a block at the end of S-phase (G2). *

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The currently provided data on the DNA content are, however, clearly insufficient to draw firm conclusions. The gating strategy (dotted lines in Figs. 3H, 7A) is unclear. Why are populations, e.g., not separated at the lowest part of the depression in the histogram, but shifted towards lower DNA content? This seems to overestimate the percentage of cells that have a higher DNA content and the statement in lines 269-271, i.e., that TgCrk4 deficient parasites break the "once and only once" rule, is not supported by data.

*We corrected the gating of the FACScan plots to separate G1, S, G2+M, and parasites with over-duplicated DNA. Please note that, in general, the cell cycle gating of FACScan data is relative and somewhat subjective when it comes to the gaussian curve. Independent of the chosen gates, our data show that removal of either TgCrk4 or TgiRD1 led to substantial decrease of the G1 population (reduction of 1N peak) accompanied by increase of parasites in the process of replication, completed replication (increase of 1.8 N peak), as well as undergoing DNA re-replication, which supports our claim in lines 269-271. In the case of TgiRD1, the number of parasites with re-duplicated DNA nearly doubled upon 8h of factor deficiency. *

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It is also unclear how may biological replicates are represented by these data (Figs. 3H, 7A), a critical wild type control at t = 4 h is missing, as well as a statistical analysis. Alternatively, the authors could use microscopy to quantify the DNA content of individual nuclei, which would yield a direct read out on whether a nucleus is in pre-S phase, S-phase or post-S phase. Defining the onset of S-phase indirectly by the number of centrosomes per cell seems imprecise, given the small size of the structure and the resolution of the microscope. Without solving these issues, the major conclusions and several minor statements throughout the manuscript are in question.

*Thank you for your point, we performed a minimum of three independent experiments to evaluate the DNA content of TgCrk4- or TgiRD1- (former TgCdt1) depleted tachyzoites and have now indicated this in the figure legends. The 0h time point is a “wild type” control, since the parasites that expressed factors were incubated without auxin (mock treated) for 4h. The DNA content of Toxoplasma has been thoroughly studied and we are thus confident our 0h data is a good representation of asynchronous healthy populations. Although the parental strain had been examined, due to the data density mentioned in the reviews, we included only relative results (control and two experimental points) for clarity. Our concern with using microscopy to analyze DNA content is that it can be highly subjective, hinging on the quality of staining and imaging, while flow cytometry produces more unbiased datasets. We have considered the concern that the start of centrosome duplication can be difficult to identify, but the centrin-positive centrosomes move apart by the middle of S-phase. The independent structures are then distinct and easy to resolve, providing a popular means of marking G1/S transition in Toxoplasma. *

• Lines 187-189: The mentioned checkpoint is unclear and so is the "specific cell cycle population". Fig. 2B analyses budding, but as the final step in the cell cycle, the knock down parasites may have arrested at various other stages of the cell cycle. In addition, it is unclear on which primary data Fig. 2B is based. It appears these may be at least partially shown in Fig. 3. If so, please reorganize as this is highly misleading.

*“A checkpoint” in the indicated lines refers to G2/M and SAC, which are regulated by TgCrk4 and TgCrk6, respectively. We refer to “specific cell cycle population” since each transgenic parasite that is subject to G2/M or SAC arrest can allow us to isolate very different cell cycle stages. TgCrk6-dependent arrest had been confirmed by the presence of unresolved centrocone (not shown but was previously reported in Hawkins et al., 2022), while we thoroughly examined the novel TgCrk4-dependent block by focusing on many parameters, such as joint centrosomes, single-bud assembly, or unresolved apicoplast. Fig. 2 and Fig. S2 summarize our rigorous quantifications of these phenotypes. For convenience, we used budding efficiency as a readout to compare arrest and release of G2/M and SAC, which was incorporated in Fig. 2B. Table S4 contains the primary data used in all figures in the manuscript, including Fig. 2B. *

• Line 246-254: It is unclear how many biological replicates were performed and how many cells were analyzed to conclude that TgCrk4 deficient parasites cannot form a bipolar spindle (Fig. 2H, S3B). This, together with the possibility that the developmental arrest occurs pre-S phase (Fig. 3H), does not support the statement, that the G2/M transition is regulated by the novel TgCrk4-TgCyc4 complex.

We have indicated our replicates in the M&M. As addressed for Fig. 3H above, these IFA experiments were performed in at least three independent experiments.

* * Minor comments: - Throughout the manuscript, please reorganize and present the figures in order of appearance in the text. Also, Fig. 1G summarizes data that are only presented in Fig. 1H. Please reorder. Similarly, Fig. 2C appears to summarize data that are only presented later.

*Thank you for the suggestion, however we must abide by the standards of the publishers. The order of the figures must be maintained, but there is a substantial degree of freedom in organizing panels within figures. Fig. 1G summarizes data shown in Fig. 1F, H, while Fig. 2C summarizes many panels including preceding Fig. 2B and Fig. S2. Most of our schematics are placed at the top of figures to provide guidance for the relevant experiments. *

• Why was only the "G1" timepoint quantified in Fig. 1H? Do the other images shown in F and H represent the majority of cells analyzed?

*You are correct, we indicated the percentage of factor-positive parasites only when the factor emerges during a specific cell cycle phase. For example, the TgCyc4-positive parasites with 1 centrin dot were quantified to show that TgCyc4 emerges in the middle of G1 phase. The lack of a number indicates that the image represents all the parasites progressing through this phase; we have added this explanation to the figure legends. *

• Several micrographs lack scale bars (Fig. 1B, D; 2E, F, H, I; 6D; 7F, H and S2G, S3A, B; S5A, B, D).

*Thank you, we have added the scale bars to indicated images.

*

• Lines 83-85 and 93-95: Recently several publications investigated the cell cycle of the apicomplexan parasite Plasmodium and data are accumulating, showing that there may be a gap between the last S phase and segmentation (e.g., PMID: 35731838; PMID: 35353560), which may be interpreted as a G2 phase. Thus, these statements could be revised to reflect the current literature.

*The studies mentioned provide very valuable insights into S-phase dynamics; the gap that was detected between S-phase and segmentation includes mitotic events such as prophase, metaphase, and anaphase prior to telophase (karyokinesis to segmentation). However, studies using means like stage-specific markers could help resolve the composition and order of events in the apicomplexan cell cycle. We used processes specific to G2 (repression of DNA and centrosome reduplication) and identified TgCrk4/TgCyc4 as the first G2 markers in apicomplexans. *

• Fig. 4 shows the effect on protein abundance and phosphorylation upon TgCrk4 depletion. Fig. 4B seems somewhat redundant as a more detailed analysis with two timepoints is shown in the rest of the figure.

*Fig. 4B is provided in contrast to the plot in Fig. 4A. It demonstrates that TgCrk4 depletion results in a far more pronounced effect on global phosphorylation rather than on proteolysis. While Fig. 4B highlights the checkpoint arrest, panels C and D are dedicated to the search for TgCrk4 substrates: the phospho-sites that immediately lost intensity of phosphorylation and remained low during the 4h block. *

*

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• Lines 146-148: This statement is confusing in light of the expression data in Fig.1 F and H. If they stabilize each other, how is TgCrk4 stabilized in G1, when TgCyc4 is absent?

We believe that multiple mechanisms contribute to the stability and function of TgCrk4. We tested one and found that depleting the cyclin partner led to reduced expression of TgCrk4, and were able to conclude that the complex is stable when both subunits are expressed. Please note that we probed the mixed cell cycle populations by WB, and our proteomics data show that TgCrk4 interacts with many partners (Fig. 1E). Thus, it is likely that G1 stability may have been mediated by other partners, or by a higher transcription/translation rate, which could be evaluated in further experiments that focus on the regulation of TgCrk4/TgCyc4 complex.

• *

• Fig. 2D, and G: Please provide representative images of what has been quantified, as E/F and H/I are apparently UxEM images.

The corresponding images are included in Fig. S2.

• Line 236-243: This statement seems to be based on a single IFA shown in Fig. 2K. If so, the manuscript would benefit from clearly stating that this is a singular observation.

*Thank you, we have provided clarification as described in previous points. *

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• Lines 301-304: In the cited publication, the TgOTUD3A knockout could not be complemented, which raises the possibility that other factors are involved. Thus, this statement would benefit from revision.

*The lack of TgOTUD3A KO complementation is an example of the unappreciated complexity of apicomplexan cell cycle regulation by controlled proteolysis. We highlighted the similarity of TgCrk4 and TgOTUD3A deficiencies, which indirectly confirms their partnerships in the G2 network. Fig. 8A shows that, in addition to TgOTUD3A, the G2 network contains numerous factors. *

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• Lines 421-422: PfCdt1 was annotated in PlasmoDB some time ago and this statement needs to be revised.

*Please see our response to comments made by Reviewer 2. Briefly, we agree with Reviewer 2 comment that TgCdt1 does not function as conventional DNA replication licensing factor CDT1. Therefore, we named TGME49_247040 TgiRD1 – inhibitor of DNA and centrosome ReDuplication 1. *

• *

• Lines 448-450 and Fig. 6F: Are these data from a single biological replicate and how many cells were analyzed for the different time points? Given the insufficient data on the DNA content, the paper would benefit form more conservative conclusions on the role of TgCdt1. The numbers of biological replicates were added throughout the text, also please refer to our response to Reviewer 2 and the comment above.

Reviewer #1 (Significance (Required)):

• This manuscript investigates the role of TgCrk3, TgCyc4 and TgCdt1s and provides a large amount of data.
• These data will contribute to our understanding of the unusual division modes of Apicomplexa, a field of research that recently gained momentum.
• These data will be interesting to the community of cell and molecular biologist, which work on the fundamental biology of eukaryotic microorganisms.
• My field of expertise is the cell biology of Apicomplexa.

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

Summary: In this Manuscript, Hawkins et. al. describe advances in the apicomplexan parasite cell cycle, which is reminiscent but distinct from mammalian cell cycle regulation. These differences include a presumed lack of G2 phase and the ability to replicate in either a multinuclear (schizogony) or binary (endodyogeny) manner. Using Toxoplasma gondii (TG) as a model, the authors seek to expand the current understanding of how these highly variable parasitic cell cycles are regulated by describing a previously unreported G2 phase. Building on the authors earlier work, this manuscript defines the function of TgCrk4 and identifies a novel binding partner, TgCyc4. Crk4 and Cyc4 control a G2/M checkpoint by regulating centrosome duplication and separation.

The authors also identify 247040, a protein with previously no known function, as a binding partner and substrate of TgCrk4/TgCyc4 and several replication fork proteins such as MCM and PCNA. Results indicate that the protein negatively regulates replication and centrosome duplication. The authors propose to rename this protein TgCDT1 despite "low sequence similarity" and having a completely opposite function to eukaryotic CDT1. Using Swiss-Prot modeling the authors claim 247040 bears a "partial resemblance" to mammalian CDT1. Indeed, both of these proteins show high intrinsic disorder and have 2 folded domains. While 247040, like hCDT1, does contain cyclin interacting motifs (Cy), a collection degrons (not all shared with other CDT1 orthologs), and an NLS, the list of nuclear cell cycle proteins that also contain Cy and degron motifs would be very long. Further, 247040 is regulated in an opposite manner to all other CDT1 orthologs because it is absent in TG G1 and present in TG S phase; eukaryotic CDT1 is either degraded or relocalized to the cytoplasm in S phase, and evidence for degradation via APC/C is minimal. Crucially, loss of 247040 resulted in inappropriate replication ("re-replication"), whereas all other eukaryotic CDT1 orthologs are essential for replication. Re-replication in eukaryotic cells can be caused by excess or hyper-active CDT1, not by loss of CDT1 activity as shown here for 247040. Clearly 247040 is a negative regulator of DNA replication, and as such, is not a candidate for the TgCDT1 ortholog. If anything, it is functionally analogous to metazoan geminin, the negative regulator of metazoan CDT1; of note, geminin also has centrosome-related phenotypes. We cannot support naming 247040 TgCDT1 because it will cause confusion in the field.

Aside from this major issue, the study is well-executed, rigorous, quantitative, and thorough; it has many strengths from the unbiased interaction screens. The authors' sequence analysis also suggests broader possibilities for cyclin structures than had previously been appreciated. We appreciate the legend in Figure 2 to the organism-specific terminology.

Major comments: The spatiotemporal dynamics of 247040, its role in repressing TG DNA replication, lack of PIP motif and winged helix domain indicate that some other nomenclature, other than TgCdt1 will be a better name for this protein of previous unknown function.

We would like to thank Reviewer 2 for this highly insightful comment. We agree that TGME49_247040 functions as a CDT1 inhibitor rather than as CDT1 itself, so conserving the name would produce confusion in the cell cycle field. Based on TGME49_247040 protein function we decided to name this factor TgiRD1 – inhibitor of DNA and centrosome ReDuplication 1. We revisited our data, looked deeper into the protein structure, and adjusted our conclusions. Our new Figure S5 shows differences in the predicted folding of HsCDT1 and TgiRD1. We could not ignore the fact that TgiRD1 is phylogenetically related to CDT1 in ancestral branches and metazoans (Fig. 6B), but we identified substantial differences that may indicate a selective loss (or inheritance) of protein features. For example, TgiRD1 does not interact with ORCs that are critical for the licensing step, but TgiRD1 retained an MCM binding domain (winged helix-turn-helix) that plays a role in licensing and firing. Rather than CRL4Cdt2 degrons, TgiRD1 contains APC/C degrons that would be activated late in mitosis (similar to regulation of Geminin). Together with the lack of DNA licensing control in G1 and its opposing expression profile, we concluded that TgiRD1 represents a Cdt1-related protein that controls DNA and centrosome reduplication in S and G2 phases.

Minor comments:

1. For clarity, please include the number of replicates in the figure legends where appropriate. We added the requested information.

For microscopy/imaging, how were representative cells/images chosen? The representative images constituted the most common phenotype of the feature we aimed to highlight, and most are accompanied by quantifications.

In addition to the ELM analysis, the authors could also employ fold recognition software (such as Promal) to analyze 247040 structural models to show similarity to known protein structures.

We use a variety of folding prediction software, including AlphaFold2, PyMol, and template-based SWISS-PRO module to examine protein structures in our study, indicated in the text and figure legends. Our new TgiRD1 (former TgCdt1) analysis is based on an AlphaFold2 prediction (Fig. S5). All the software we used is listed in the M&M section.

Line 107: missing words "TgCdt1"

*We corrected the sentence.

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Line 141: the interpretation that the C terminus is "unstable" is misleading if it is simply that the protein cannot tolerate a fusion to the C-terminus.

*We successfully incorporated a tag at the C-terminus (confirmed by sequencing across the recombinant gene) but could not detect protein expression. If our protein could not tolerate a recombinant tag, the transgenic parasites would not survive because TgCyc4 is essential protein. Therefore, since the parasites survived, we concluded that the lack of TgCyc4-AID-HA expression was due to native truncation at the C-tail (instability). *

Line 221: word choice "reminisced" We have changed the wording.

Line 348 refers to Orc4 expression in Figure 4A, but the data point is not labelled. Fig. 4A references GO group (DNA replication/licensing factors), and the raw data is included in Table S6, which is now indicated in the text.

Lines 407-8 and 510-11: Reference Fig 1E We added the reference.

Line 408: please define what is meant by "dominant interactor" We meant that TgiRD1 is the most prominent interactor of TgCrk4 and TgCyc4. To clarify the confusion, we changed the wording to “primary interactor”.

Reviewer #2 (Significance (Required)):

This manuscript makes great strides in defining apicomplexan cell cycle control and genome replication. These strides include defining a previously unrecognized G2/M checkpoint controlled by TgCrk4 and the novel TgCyc4. Further, the authors identify a binding partner and substrate of the novel Crk4/Cyc4 kinase complex, 247040 that acts as a repressor of replication.

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

Summary The present study Hawkins et al have described the important role of Cyclin-CDK complex in an apicomplexan parasite Toxoplasma(Tg) which exhibit binary mode of cell division like many other eukaryotes. In the apicomplexan field it is generally shown that G2 phase of cel cycle is either absent or has very little role. The authors here demonstrate that the combination of Tg CRK4 and Tg Cyclin4 works during the G2 phase of cell cycle such as chromosome rereplication and centrosome reduplication. In order to show the function of Cyclin-CRK function they used Auxin degradation system to down regulate or deplete the protein and study parasite growth during cell cycle as well as they used tagged parasite to identify the protein complex with these two molecules. In the study they showed that these two molecules Cyc4 and cRK4 formed the complex in protein pulldown method and show identical function in the cell cycle. In addition to thiese two proteins they also found another interacting partner Cdt1 that was further analysed to be involved in controlling Chromosome rereplication and centrosome. So overall the study is nicely performed and three molecules of Cyclin4-CRk4-Cdt1 and their role is illustrated in the binary mode of cell division in Toxoplasma.

Comments 1.Though no new experiments need to be performed but it will be good if some details are given as to which stage of tachyzoite cycle the protein complex were performed and if there is difference in the various phases of cell cycle especially the s phase and the M phase. Are these period changed. Since G2 is suppose to be absent in many apicomplexan do the authors suggest that G2 phase is only coupled to binary mode of cell division. Please discuss how it is then linked to the other part of cell cycle.

*You are correct, we propose that the presence of G2 phase is linked to binary division in apicomplexans and our hypothesis is supported by the overall evolution of the cell cycle (see Discussion section). We also entertained the hypothesis that G2 operates in multinuclear division since all apicomplexans encode TgiRD1 orthologs (please, see the Discussion section). For the first time, we identified the major functions of G2 functions (repression of the DNA and centrosome reduplication) in the apicomplexan cell cycle. However, given the unresolved organization of the Toxoplasma (or any apicomplexan) cell cycle, it is currently impossible to define the boundaries of G2. According to our study, TgCrk4 and TgCyc4 control G2/M transition or the end of G2 phase, and we still lack markers of G2 entry. In our comparative synchronization study (Fig 2), we uncovered the temporal link between G2/M and SAC regulatory points, which is discussed in the results section. *

Ganter et al have studied CRK4 in Plasmodium previously and they do find in their phosphoproteome study the similar association with the DNA replication machinery with CRK4 but no cyclin was identified in their study. In the cyclin study by Roques et al it has been shown that no cell cycle cyclins are found in Apicomplexan so can the author discuss more how these complex can be different in two apicomplexan species. They describe that Crk4 is novel cell cycle kinase though this has been studied earlier. Authors have almost not discussed these previous finding with respect to their in this study.

*We would like to clarify this confusion. We have not discussed Ganter et al. studies because PfCRK4 is not orthologous to TgCrk4, but rather it is related to TgCrk6. Unfortunately, the Plasmodium and Toxoplasma Crk nomenclature was published almost concurrently. Our previous (Alvarez & Suvorova, 2017) and current study show that Plasmodium and other apicomplexans that divide by multinuclear division do not encode TgCrk4 orthologs (and/or TgCyc4). Additionally, the mentioned studies by Roques and Ganter were released prior to newer genome annotations that include additional cyclin-domain proteins, including 10 Toxoplasma cyclins (5 new) that we categorized in our recent publication (Hawkins et al., 2022). Although the newly annotated cyclins are not related to conventional cell cycle cyclins, we had proven empirically that TgCyc1 together with TgCrk6 controls SAC, and now, the specific interaction of TgCyc4 with TgCrk4 controls G2 processes. Lastly, we call TgCrk4 “a novel” kinase only in the meaning that it is a novel cyclin-dependent kinase that is not related to known CDKs in other eukaryotes. The identification of TgCrk4 in our previous study (Alvarez & Suvorova, 2017) is described in the Introduction section and at the opening of the Results. *

The manuscript is too dense, in terms of both figures and text. At times loses the focus and hence can be organised with most important finding in the figure and text. Especially Fig2, Fig4 and Fig7. Fig5 does not give too much in terms of the real finding an in fact take away from the focus. Some parts of these figures can be simplified or moved to supplementary. Some of the figures in Fig2 and 7 are missing the scale bars.

We respectfully disagree with some conclusions made by the Reviewer. Our study contains ample material that is intended to guide the reader through the complexity of the Toxoplasma cell cycle and the intricate structures contained in the parasite. We have also introduced a few novel approaches that require additional schematics and dedicated discussions.

• Fig 2*. The G2/M block, as well as the G2 phase, had never been detected in apicomplexans. We created a new approach to determine the timing of the G2/M checkpoint, which involves comparison to a known cell cycle block. Panels A, B, and C provide visuals and summarize our findings. The main events are highlighted with arrows (Panel C), while graphs (panel B) show differences in responses. The rest of the figure is devoted to quantification of the primary events caused by TgCrk4 deficiency, since the G2 block had never been examined. While the U-ExM images of the entire vacuole (2-4 parasites) may seem overwhelming, they represent that the deficiency is consistent. *
• Fig 7* is devoted to the major Crk4/Cyc4 interactor TgiRD1 (former TgCdt1). This is one of the first mechanistic studies of central cell cycle regulators in Toxoplasma. This Cdt1-related protein was examined at the molecular level to support the main claims of its control of G2 Nevertheless, we moved two panels from Fig. 7 into the supplement. *
• 4* is organized as follows. Top row: panels A, B visualize the G2/M checkpoint block at the protein level. Middle row: panels C, D, and E represent the workflow to find TgCrk4 substrates. Bottom row: panels F, G highlight TgCrk4 substrates of interest that are discussed in the paper. *
• 5* is an in-depth analysis of the central cell cycle regulators across Apicomplexa phylum, a key figure of the study. Its comparative nature supports our main message: binary division is regulated by TgCrk4/TgCyc4, which are only expressed in a subgroup of apicomplexans that divide in a binary mode. *

May be bit more discussion of ORC in relation to their Cyclin-CRK complex as they did find upregulation of the ORC in their genome profiling. So may be instead of CDT1 these are more important in the licencing of DNA replication.

*Our choice to focus on Cdt1-related protein was driven by the fact this protein is a major component of the TgCrk4/TgCyc4 complex, while the ORCs act downstream (as TgCrk4 substrates). Shifting focus to ORCs opens an entire new project, which will be explored in the future. *

5 The model in Fig8B does not take Cyc4 into consideration and I feel is bit oversimplified as there are many factors that may be responsible for centrosome non separation. The S and G2 are no separated in the Cell cycle as given in this Fig.

Referring to comment 3, we focused on empirically supported, central findings and created the first model of centrosome cycle regulation in T. gondii. We intentionally drew focus to TgCrk4, which was extensively studied, while TgCyc4 received less attention due to difficulties in modulating its expression. We have used transcriptional downregulation to evaluate TgCyc4 (tet-OFF model), which is unfavorable for cell cycle studies because it exceeds the duration of the cell cycle. The unclear cell cycle borders are addressed in the introduction to this response. Briefly, the organization of apicomplexan cell cycle is currently unclear, thus most of the schematics are approximate.

It is not clear from the data with CDt1 if this linking the inner and outer centrocone or its down regulation breaks the bipartite centrosome. May be some reflection it will be useful.

*Our model suggests that both TgCrk4 and TgiRD1 (former TgCdt1) affect only the inner core of the centrosome, which we propose is comprised of two types of linkers. The arrows in Fig. 8 point specifically to the linkers whose stability depends on the expression of TgCrk4 or TgiRD1. *

Minor comments

I what is SAINT analysis as it is not described in methods.

*We added the description of our SAINT analysis to M&M.

*

How was budding quantified

*We supplemented the figure legend with the required information. *

Western blot can have predicted size

*Due to density of the figures, we did not supply the predicted MW of the proteins when they display the proper PAGE motility. *

what does red star mean in Blot 1C

*We added the description to the figure legend.

*

What does the number in Fig1H means please explain in the legends and same for Fig6F. In fig 1, removing the inhibition for 5 hours led to very less budding, but in fig 3, removing inhibition showed increased budding (50% in 2 hours). Please explain

*Please see our response to the reviewer 1 minor comment regarding Fig. 1H and 6F. *

*We presume that there is some confusion regarding figure numbers. Perhaps the Reviewer refers to Fig. 2B. Indeed, the 4h block at G2/M led to reduced budding (Fig. 2B), while release from the block for 2 hours (Fig. 3C, post-recovery) allows parasites to continue cell cycle progression and reach the next stage –budding. The numbers over the Fig. 3A, B, and C panels are from the plots in Fig. 2B to help give a comprehensive representation of the analyzed timepoint. *

Fig2 has no scale bars -please add- this figure is too dense. May be fig2A, B,C can be in supplementary, legend in the figure can be in the figure legend.

Please see our response to comment 3. We have included scale bars.

Also this figure2 H and I in not quoted in line 231. Also this figure2 has no panel J but goes directly from I to K

*The alphabetical order was corrected, and the reference added. *

Fig3 the FigG can be more relevant in the Figure 8 while describing about the Crk4 and Cyc4 and CDt1 in binary mode of cell division. Also please define what stars mean either in legend or methods section in terms of significance.

*Thank you for the suggestion. The Fig. 3G schematics summarize the overall findings of the Figure and acts as an intermediate conclusion in this study. We added the meaning of the stars in the M&M section. *

Line 107 the sentence is incomplete

We have corrected the sentence.

Line 217 may be the figure could be referred as then it is not cleat about the description.

Due to the density of the figures and well-established dynamics of the centrocone and basal rings, we included the reference to a publication rather than as a figure panel.

**Referees cross-commenting**

The study is quite rigrous and with analyses of CRK4-CYC4 and CDT. However it will be better if authors please revisit their conclusions on G2 phase of cell cycle in Toxoplasma based on their findings. The study will have important bearing on the community studying apicomplexan parasites and DNA replication as well as who work on eukaryotic cell cycle.

Reviewer #3 (Significance (Required)):

Significance In the manuscript by Hawkins etal have illustrated that in the apicomplexan parasite that have binary mode of cell division present a Cyclin-Crk complex with detailed analysis of Tg Crk4-Cyc4 that are novel in these group pf parasite infect humans and animal alike like malaria parasite and ones affecting cattle and chicken. So these finding are novel as very little is known about this interaction. The significant finding is to show how the G2 phase of cell cycle may be regulated in these parasites and how DNA licencing factor Cdt1 is highly divergent but part of this CRK-Cyclin complex.

So though it discusses more on the Toxoplasma but it may be of interest to the scientist working on eukaryotes with divergent mode of cell cycle.

General Assessment - The findings are novel but the manuscript is too dense and at time loses the focus. May be both text and Figures could be made less dense so that important finding are revealed in better way.

Advance - It does give important insight into the cell cycle in apicomplexan parasite and how even though there are no cell cycle cyclin in Apicomplexa. The findings here suggest how different complexes can substitute for the function. It does extend the knowledge in the field of Cell division in divergent parasites both in terms of mechanistic, functional and technical way.

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Referee #3

Evidence, reproducibility and clarity

Summary

The present study Hawkins et al have described the important role of Cyclin-CDK complex in an apicomplexan parasite Toxoplasma(Tg) which exhibit binary mode of cell division like many other eukaryotes. In the apicomplexan field it is generally shown that G2 phase of cel cycle is either absent or has very little role. The authors here demonstrate that the combination of Tg CRK4 and Tg Cyclin4 works during the G2 phase of cell cycle such as chromosome rereplication and centrosome reduplication. In order to show the function of Cyclin-CRK function they used Auxin degradation system to down regulate or deplete the protein and study parasite growth during cell cycle as well as they used tagged parasite to identify the protein complex with these two molecules. In the study they showed that these two molecules Cyc4 and cRK4 formed the complex in protein pulldown method and show identical function in the cell cycle. In addition to thiese two proteins they also found another interacting partner Cdt1 that was further analysed to be involved in controlling Chromosome rereplication and centrosome. So overall the study is nicely performed and three molecules of Cyclin4-CRk4-Cdt1 and their role is illustrated in the binary mode of cell division in Toxoplasma.

Comments

1.Though no new experiments need to be performed but it will be good if some details are given as to which stage of tachyzoite cycle the protein complex were performed and if there is difference in the various phases of cell cycle especially the s phase and the M phase. Are these period changed. Since G2 is suppose to be absent in many apicomplexan do the authors suggest that G2 phase is only coupled to binary mode of cell division. Please discuss how it is then linked to the other part of cell cycle.<br /> 2. Ganter et al have studied CRK4 in Plasmodium previously and they do find in their phosphoproteome study the similar association with the DNA replication machinery with CRK4 but no cyclin was identified in their study. In the cyclin study by Roques et al it has been shown that no cell cycle cyclins are found in Apicomplexan so can the author discuss more how these complex can be different in two apicomplexan species. They describe that Crk4 is novel cell cycle kinase though this has been studied earlier. Authors have almost not discussed these previous finding with respect to their in this study. 3. The manuscript is too dense, in terms of both figures and text. At times loses the focus and hence can be organised with most important finding in the figure and text. Especially Fig2, Fig4 and Fig7. Fig5 does not give too much in terms of the real finding an in fact take away from the focus. Some parts of these figures can be simplified or moved to supplementary. Some of the figures in Fig2 and 7 are missing the scale bars. 4. May be bit more discussion of ORC in relation to their Cyclin-CRK complex as they did find upregulation of the ORC in their genome profiling. So may be instead of CDT1 these are more important in the licencing of DNA replication. 5 The model in Fig8B does not take Cyc4 into consideration and I feel is bit oversimplified as there are many factors that may be responsible for centrosome non separation. The S and G2 are no separated in the Cell cycle as given in this Fig. 6. It is not clear from the data with CDt1 if this linking the inner and outer centrocone or its down regulation breaks the bipartite centrosome. May be some reflection it will be useful.

Minor comments

I what is SAINT analysis as it is not described in methods. 2. How was budding quantified 3. Western blot can have predicted size 4. what does red star mean in Blot 1C 5. What does the number in Fig1H means please explain in the legends and same for Fig6F. In fig 1, removing the inhibition for 5 hours led to very less budding, but in fig 3, removing inhibition showed increased budding (50% in 2 hours). Please explain 6. Fig2 has no scale bars -please add- this figure is too dense. May be fig2A, B,C can be in supplementary, legend in the figure can be in the figure legend.<br /> 7. Also this figure2 H and I in not quoted in line 231. Also this figure2 has no panel J but goes directly from I to K 8. Fig3 the FigG can be more relevant in the Figure 8 while describing about the Crk4 and Cyc4 and CDt1 in binary mode of cell division. Also please define what stars mean either in legend or methods section in terms of significance.

Line 107 the sentence is incomplete Line 217 may be the figure could be referred as then it is not cleat about the description.

Referees cross-commenting

The study is quite rigrous and with analyses of CRK4-CYC4 and CDT. However it will be better if authors please revisit their conclusions on G2 phase of cell cycle in Toxoplasma based on their findings. The study will have important bearing on the community studying apicomplexan parasites and DNA replication as well as who work on eukaryotic cell cycle.

Significance

In the manuscript by Hawkins etal have illustrated that in the apicomplexan parasite that have binary mode of cell division present a Cyclin-Crk complex with detailed analysis of Tg Crk4-Cyc4 that are novel in these group pf parasite infect humans and animal alike like malaria parasite and ones affecting cattle and chicken. So these finding are novel as very little is known about this interaction. The significant finding is to show how the G2 phase of cell cycle may be regulated in these parasites and how DNA licencing factor Cdt1 is highly divergent but part of this CRK-Cyclin complex.

So though it discusses more on the Toxoplasma but it may be of interest to the scientist working on eukaryotes with divergent mode of cell cycle.

General Assessment - The findings are novel but the manuscript is too dense and at time loses the focus. May be both text and Figures could be made less dense so that important finding are revealed in better way.

Advance - It does give important insight into the cell cycle in apicomplexan parasite and how even though there are no cell cycle cyclin in Apicomplexa. The findings here suggest how different complexes can substitute for the function. It does extend the knowledge in the field of Cell division in divergent parasites both in terms of mechanistic, functional and technical way.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this Manuscript, Hawkins et. al. describe advances in the apicomplexan parasite cell cycle, which is reminiscent but distinct from mammalian cell cycle regulation. These differences include a presumed lack of G2 phase and the ability to replicate in either a multinuclear (schizogony) or binary (endodyogeny) manner. Using Toxoplasma gondii (TG) as a model, the authors seek to expand the current understanding of how these highly variable parasitic cell cycles are regulated by describing a previously unreported G2 phase. Building on the authors earlier work, this manuscript defines the function of TgCrk4 and identifies a novel binding partner, TgCyc4. Crk4 and Cyc4 control a G2/M checkpoint by regulating centrosome duplication and separation.

The authors also identify 247040, a protein with previously no known function, as a binding partner and substrate of TgCrk4/TgCyc4 and several replication fork proteins such as MCM and PCNA. Results indicate that the protein negatively regulates replication and centrosome duplication. The authors propose to rename this protein TgCDT1 despite "low sequence similarity" and having a completely opposite function to eukaryotic CDT1. Using Swiss-Prot modeling the authors claim 247040 bears a "partial resemblance" to mammalian CDT1. Indeed, both of these proteins show high intrinsic disorder and have 2 folded domains. While 247040, like hCDT1, does contain cyclin interacting motifs (Cy), a collection degrons (not all shared with other CDT1 orthologs), and an NLS, the list of nuclear cell cycle proteins that also contain Cy and degron motifs would be very long. Further, 247040 is regulated in an opposite manner to all other CDT1 orthologs because it is absent in TG G1 and present in TG S phase; eukaryotic CDT1 is either degraded or relocalized to the cytoplasm in S phase, and evidence for degradation via APC/C is minimal. Crucially, loss of 247040 resulted in inappropriate replication ("re-replication"), whereas all other eukaryotic CDT1 orthologs are essential for replication. Re-replication in eukaryotic cells can be caused by excess or hyper-active CDT1, not by loss of CDT1 activity as shown here for 247040. Clearly 247040 is a negative regulator of DNA replication, and as such, is not a candidate for the TgCDT1 ortholog. If anything, it is functionally analogous to metazoan geminin, the negative regulator of metazoan CDT1; of note, geminin also has centrosome-related phenotypes. We cannot support naming 247040 TgCDT1 because it will cause confusion in the field.

Aside from this major issue, the study is well-executed, rigorous, quantitative, and thorough; it has many strengths from the unbiased interaction screens. The authors' sequence analysis also suggests broader possibilities for cyclin structures than had previously been appreciated. We appreciate the legend in Figure 2 to the organism-specific terminology.

Major comments:

The spatiotemporal dynamics of 247040, its role in repressing TG DNA replication, lack of PIP motif and winged helix domain indicate that some other nomenclature, other than TgCdt1 will be a better name for this protein of previous unknown function.

Minor comments:

1. For clarity, please include the number of replicates in the figure legends where appropriate.
2. For microscopy/imaging, how were representative cells/images chosen?
3. In addition to the ELM analysis, the authors could also employ fold recognition software (such as Promal) to analyze 247040 structural models to show similarity to known protein structures.
4. Line 107: missing words "TgCdt1"
5. Line 141: the interpretation that the C terminus is "unstable" is misleading if it is simply that the protein cannot tolerate a fusion to the C-terminus.
6. Line 221: word choice "reminisced"
7. Line 348 refers to Orc4 expression in Figure 4A, but the data point is not labelled.
8. Lines 407-8 and 510-11: Reference Fig 1E Line 408: please define what is meant by "dominant interactor"

Significance

This manuscript makes great strides in defining apicomplexan cell cycle control and genome replication. These strides include defining a previously unrecognized G2/M checkpoint controlled by TgCrk4 and the novel TgCyc4. Further, the authors identify a binding partner and substrate of the novel Crk4/Cyc4 kinase complex, 247040 that acts as a repressor of replication.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Hawkins et al. employ a reverse genetic approach to analyze the molecular function of the Toxoplasma gondii kinase Crk4 and the Toxoplasma gondii cyclin 4. The authors combine inducible depletion with imaging, (phospho-)proteomics, molecular modeling, and protein-protein interaction studies.

Major comments:

• The major conclusion of the manuscript is that TgCrk4/TgCyc4 regulate entry into mitosis and that the primary role of TgCrk4 is to suppress DNA re-replication and chromosome re-duplication (lines 105-106). The authors also provide evidence that TgCrk4 interacts with TgCdt1, a DNA licensing factor ("TgCdt1" is missing in line 107). By sequence homology, the authors found homologues of TgCrk4 only in apicomplexan parasites with binary division and concluded that the dominant division mode, presumably schizogony, is repressed in these organisms in favor of binary division. Indeed, internal budding and daughter cell formation is defective in the inducible depletion mutants of TgCrk4 and most experiments focus on this developmental stage. However, the analysis of preceding events, such as DNA replication is rather brief. If G2 is indeed regulated by TgCrk4/TgCyc4, one would assume that the parasites are post-S phase and the nucleus contains two copies of the genome, as indicated in Fig. 2C. The data shown in Fig. 3H and 7A, however, show that the TgCrk4 and TgCTD1 depletion induces a developmental arrest pre-S phase. This contradicts the main conclusions of the manuscript. Indeed, many data of this manuscript could support an alternative conclusion, i.e., that TgCrk4 regulates entry into S-phase (similar to Plasmodium falciparum Crk4: PMID: 28211852). This alternative conclusion is supported by the data showing that TgCyc4 is in the nucleus during S-phase (Fig. 1H) and that TgCrk4 interacts with TgCdt1, which has a well-known role in origin of replication licensing and loading of the MCM complex. MCM subunits were less phosphorylated in absence of TgCrk4, which could also suggest a role for TgCrk4 in S phase. Together, it seems more parsimonious to interpret the data as a DNA replication phenotype rather than a phenotype in G2. The currently provided data on the DNA content are, however, clearly insufficient to draw firm conclusions. The gating strategy (dotted lines in Figs. 3H, 7A) is unclear. Why are populations, e.g., not separated at the lowest part of the depression in the histogram, but shifted towards lower DNA content? This seems to overestimate the percentage of cells that have a higher DNA content and the statement in lines 269-271, i.e., that TgCrk4 deficient parasites break the "once and only once" rule, is not supported by data. It is also unclear how may biological replicates are represented by these data (Figs. 3H, 7A), a critical wild type control at t = 4 h is missing, as well as a statistical analysis. Alternatively, the authors could use microscopy to quantify the DNA content of individual nuclei, which would yield a direct read out on whether a nucleus is in pre-S phase, S-phase or post-S phase. Defining the onset of S-phase indirectly by the number of centrosomes per cell seems imprecise, given the small size of the structure and the resolution of the microscope. Without solving these issues, the major conclusions and several minor statements throughout the manuscript are in question.
• Lines 187-189: The mentioned checkpoint is unclear and so is the "specific cell cycle population". Fig. 2B analyses budding, but as the final step in the cell cycle, the knock down parasites may have arrested at various other stages of the cell cycle. In addition, it is unclear on which primary data Fig. 2B is based. It appears these may be at least partially shown in Fig. 3. If so, please reorganize as this is highly misleading.
• Line 246-254: It is unclear how many biological replicates were performed and how many cells were analyzed to conclude that TgCrk4 deficient parasites cannot form a bipolar spindle (Fig. 2H, S3B). This, together with the possibility that the developmental arrest occurs pre-S phase (Fig. 3H), does not support the statement, that the G2/M transition is regulated by the novel TgCrk4-TgCyc4 complex.

Minor comments:

• Throughout the manuscript, please reorganize and present the figures in order of appearance in the text. Also, Fig. 1G summarizes data that are only presented in Fig. 1H. Please reorder. Similarly, Fig. 2C appears to summarize data that are only presented later.
• Why was only the "G1" timepoint quantified in Fig. 1H? Do the other images shown in F and H represent the majority of cells analyzed?
• Several micrographs lack scale bars (Fig. 1B, D; 2E, F, H, I; 6D; 7F, H and S2G, S3A, B; S5A, B, D).
• Lines 83-85 and 93-95: Recently several publications investigated the cell cycle of the apicomplexan parasite Plasmodium and data are accumulating, showing that there may be a gap between the last S phase and segmentation (e.g., PMID: 35731838; PMID: 35353560), which may be interpreted as a G2 phase. Thus, these statements could be revised to reflect the current literature.
• Fig. 4 shows the effect on protein abundance and phosphorylation upon TgCrk4 depletion. Fig. 4B seems somewhat redundant as a more detailed analysis with two timepoints is shown in the rest of the figure.
• Lines 146-148: This statement is confusing in light of the expression data in Fig.1 F and H. If they stabilize each other, how is TgCrk4 stabilized in G1, when TgCyc4 is absent?
• Fig. 2D, and G: Please provide representative images of what has been quantified, as E/F and H/I are apparently UxEM images.
• Line 236-243: This statement seems to be based on a single IFA shown in Fig. 2K. If so, the manuscript would benefit from clearly stating that this is a singular observation.
• Lines 301-304: In the cited publication, the TgOTUD3A knockout could not be complemented, which raises the possibility that other factors are involved. Thus, this statement would benefit from revision.
• Lines 421-422: PfCdt1 was annotated in PlasmoDB some time ago and this statement needs to be revised.
• Lines 448-450 and Fig. 6F: Are these data from a single biological replicate and how many cells were analyzed for the different time points? Given the insufficient data on the DNA content, the paper would benefit form more conservative conclusions on the role of TgCdt1.

Significance

• This manuscript investigates the role of TgCrk3, TgCyc4 and TgCdt1s and provides a large amount of data.
• These data will contribute to our understanding of the unusual division modes of Apicomplexa, a field of research that recently gained momentum.
• These data will be interesting to the community of cell and molecular biologist, which work on the fundamental biology of eukaryotic microorganisms.
• My field of expertise is the cell biology of Apicomplexa.

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Referee #3

Evidence, reproducibility and clarity

Maaßen and colleagues followed up on their observation that infection with HCMV mutants lacking pUS2 and 3 impaired HLA-DP expression of IFN-gamma treated MRC-5 cells. This phenomenon is interesting because pUS2 and 3 are viral components that have been shown earlier to degrade HLA-DR alpha and HLA-DM alpha and thus inhibit the formation of HLA-DR alpha/beta heterodimers. These data indicated that in addition to pUS2 and 3 some other MHC II inhibitor must be encoded by HCMV. The authors tested this hypothesis by analyzing a HCMV gene expression library for the presence of a new HLA-DP antagonist. Indeed, the data revealed pUS28 as a new MHC II inhibitor that exhibited a posttranscriptional effect on CIITA, which is the key regulator of MHC II expression. In in vitro stimulation experiments, pUS28 impaired activation of antigen-specific CD4+ T cells.

The study provides new and important information on how HCMV evades human immunity. The shown data support the main conclusions. Nevertheless, inclusion of some additional controls would facilitate understanding the overall concept.

Minor points:

A key element of this study is that IFN-gamma induces MHC II expression on MRC-5 fibroblasts. Nevertheless, professional antigen presenting cells such as dendritic cells express MHC II independent of any stimulation. Therefore, in Fig. 1 in addition to IFN-gamma induced DP expression on MRC-5 fibroblasts, DP and DR expression of dendritic cells should be shown. This could be easily done by analysis of dendritic cells in PBMC. Furthermore, the authors should show DP and DR expression of dendritic cells with and without IFN-gamma stimulation. Most likely, DP and DR expression of untreated dendritic cells is significantly higher than DP expression of IFN-gamma treated MRC-5 cells. It is important to include such controls to avoid the impression that IFN-gamma treated fibroblasts can have similar functions as professional antigen presenting cells.

In Fig. 6b the proportion of CD137-positive T cells normalized to T cells activated by HeLa cells transfected with CIITA and pulsed with HCMV lysate is shown. In this kind of data presentation, the magnitude of the original effect, i.e., the percentage of CD4+ T cells that after 24 h of stimulation is CD137-positive, remains unclear. Therefore, it is recommended to first show actual data and then relative values. In the figure legend it is stated n = 4-10. Does this mean that T cells from different donors of the corresponding numbers have been tested? Or have T cells from some donors been tested more than once? More precise information should be given here.

Considering the higher MHC II levels expressed by dendritic cells, it would be interesting to see to which extent pUS28 expression reduces MHC II expression of dendritic cells. Such experiments can be performed by lentiviral pUS28 expression for example in monocyte-derived dendritic cells.

The conclusion in the last paragraph of the discussion that NKG2C+ memory NK cells might have activated antigen-specific CD4+ T cells is confusing. In the end, professional antigen presenting cells that have taken up viral proteins most probably stimulated antigen-specific CD4+ T cells. And since antigen presentation on MHC II is independent of infection of the antigen presenting cell, it is difficult to understand why under such conditions a red-queen race should have been taken place.

Significance

This is a highly relevant study. It adds important new information about pUS28 and how different viral components interact to evade human immunology. My expertise is on HCMV infection of human dendritic cells and the impact on antigen presentation.

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Referee #2

Evidence, reproducibility and clarity

In this study, Maaßen and colleagues investigate how HCMV US28 functions to antagonize the class II Transactivator (CIITA) transcription factor and subsequent HLA class II expression. Through physical interaction with CIITA, US28 triggered a post-transcriptional decline in CIITA protein, leading to reduced cell surface expression of HLA class II molecules, including HLA-DR, HLA-DQ, HLA-DM, CD74, and HLA-DP. Moreover, the authors show that US28-mediated degradation of CIITA hindered the activation of HCMV-specific CD4+ T cells.

Strengths of this article include the rigorous methodologies and analysis, clear and concise writing, and relevance within a clinical context. Despite the strengths, a few deficiencies were identified. Many figures lack statistical analysis to support the claims made by the authors. Where applicable, the authors should include these or explicitly state that only significant comparisons are shown. There is a lack of information regarding how the expression library screen was performed and how hits were determined/chosen for further analysis. While the observation that US28 antagonizes CIITA is well supported, the mechanism behind the antagonism is somewhat lacking.

These findings have major implications for understanding the immune response to HCMV, particularly in immunocompromised patients where impaired HLA-II presentation poses clinical risks. The authors suggest that a comprehensive understanding of the molecular mechanisms governing HCMV immune evasion could guide the development of tailored protocols for risk protection, such as vaccination, cellular therapies, or drugs targeting US28-mediated CIITA degradation.

Significance

Major Comments:

• Figure 1: Lacks statistical analysis and the number of replicate experiments that were performed.
• Figure 2: Lacks information regarding how hits from the expression screen were determined. It would be helpful to understand the selection criteria.
• Figure 3: While semi-quantitative RT-PCR is a useful method for determining the levels of mRNA, it would be beneficial to conduct RT-qPCR experiments to support the claim that US28 does not affect CIITA mRNA levels.
• Figure 3: While the blots here support the authors claim that US28 antagonize CIITA at the post transcriptional level, it would be beneficial to make these observations within the context of viral infection.
• Figure 5B: Labeling of this panel is confusing. The authors should attempt to relabel, or perform the experiment again and run samples on one gel.
• Figure 5: data for the claim that US28-mediated antagonism of CIITA is independent of neddylation, proteasomal degradation, etc. should be shown if the authors wish to make this claim.

Minor Comments:

• Labeling for immunoblots should be clearer regarding transfection conditions. The terms "empty" and "vector" is ambiguous and is not descriptive enough for the conclusions the authors are drawing.
• Many figure legends lack the information regarding the number of replicate experiments that were performed.
• Many figures, lack statistical analysis supporting the claims being made. If observations do not reach statistical significance, these should be explicitly stated within the legends. (i.e. comparisons are shown where statically significant).
• The authors should move away from making conclusions without showing any data substantiating their claims.
• Minor grammatical and citation errors were identified throughout the manuscript. The authors should carefully read and fix any errors prior to publication.

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Referee #1

Evidence, reproducibility and clarity

In this study entitled "The human cytomegalovirus-encoded pUS28 antagonizes CD4+ T-cell recognition by targeting CIITA", Maassen et al. tried to identify viral genes/proteins downregulating the HLA class II molecule HLA-DP. In a transfection-based screening assay, they identified US28 as a viral gene downregulating CIITA-dependent HLA-DP expression in transfected HeLa cells. Other HLA class II molecules and other proteins expressed in a CIITA-dependent manner were downregulated as well. The authors went on to show that CIITA transcripts were not reduced in the presence of pUS28, but CIITA protein levels were massively reduced, suggesting that US28 downregulates CIITA on the post-transcriptional level. A signaling-deficient US28 mutant, but not a mutant lacking the cytoplasmic carboxy terminus, was capable of reducing CIITA levels. In a final set of T cell activation experiments, the authors showed that US28-expression in HeLa cells reduced HLA-II-dependent restimulation of CD4+ T cells.

The data presented in the paper are generally very clean and convincing. However, not all conclusions are sufficiently supported by the data. A major weakness of the study is the fact that most experiments were done with transfected HeLa cells. Whether the proposed US28-mediated HLA-II downregulation occurs in HCMV-infected cells remains unclear. Moreover, the proposed pUS28-CIITA interaction was demonstrated in a single co-IP experiment, and the mechanism of CIITA downregulation remains obscure. Hence, the conclusion that they have identified "a mechanism employed by HCMV to evade HLA-II-mediated recognition by CD4+ T cells" (abstract) is not justified.

Major comments:

1. The mechanism of US28-dependent CIITA downregulation remains unresolved. The authors have made several attempts to clarify the mechanism, but these experiments have not met with success. Therefore, conclusions on the underlying mechanism should be toned down or removed.
2. The claim that US28-dependent CIITA downregulation occurs by pUS28 interacting with CIITA is based on a single co-IP experiment. The result would be more convincing if the authors could show the same interaction in a reverse IP, and ideally also in HCMV-infected cells. Is the US28 C-terminus required for this interaction?
3. The authors could not demonstrate US28-dependent HLA-II downregulation in HCMV-infected cells. Hence, they cannot conclude that HCMV employs this mechanism. Transfected HeLa cells are a somewhat artificial system. This does not invalidate the data, but one has to be careful when interpreting the data. Others have shown that HCMV downregulates CIITA transcript levels in myeloid cells (PMID 21458073 and 31915281). This apparent discrepancy could either be explained by several redundant mechanisms (as proposed by the authors of this manuscript) or by differences and limitations of the respective experimental systems.
4. The possibility that US28 might downregulate CIITA in latently infected cells is intriguing. Have the authors tested this in an HCMV latency system, e.g. in infected THP-1 or Kasumi-3 cells? I acknowledge that such experiments are not trivial and may be beyond the scope of the present study. However, as latently infected cells express US28 but not the other viral genes previously shown to affect HLA-II expression (US2, US3, IE1 and 2), the latency model might a way to demonstrate biological significance in virus-infected cells.

Minor comments:

1. Figure 2. Why was US29 used as a control and not US27 as in other experiments. The authors pointed out themselves that US27 is probably an ideal control for US28 as both genes encode related GPCRs.
2. Figure 2. The use of "empty" for mock-transfected cells is confusing, particularly as empty vector-transfected cells are labeled "vector".

Significance

Recognition of virus-infected cells by CD4+ T cells is an important immune defense mechanism. Viruses like HCMV have evolved numerous immune evasion mechanisms. Previous studies have identified HCMV proteins targeting HLA-II for degradation (US2, US3) or downregulating CIITA transcription (probably IE1+IE2). The findings of the present manuscript now demonstrate that US28 is capable of contributing to HLA-II downregulation. This is potentially of great significance as US28 is expressed in latently infected cells. However, the significance of the present study is limited by the fact that the studies were done in transfected HeLa cells, not in HCMV-infected cells, and that the mechanism of CIITA post-transcriptional downregulation remains unknown.

In its present form, the study should be of interest for virologists and immunologists interested in new viral immune evasion strategies. The significance and appeal to a wider audience would be massively increased if the authors could clarify the mechanism or show its importance in virus-infected cells (or both).

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Referee #3

Evidence, reproducibility and clarity

Major comments:

1. I don't understand the meaning of the sentence beginning on line 61. There are published structures of taste receptors and many papers have looked at activation mechanisms.

2. The results are extremely difficult to follow. There is far too much information in here about methods and without sub-headings is impossible to follow. I'd suggest moving a lot of the methods information to the Materials and Methods and then adding more sub-headings.

3. In Figure 1, the conclusion seems to be that the authors identified GPRC6A and taste receptors as most closely related. However, they stated in the Introduction that these were known to be most closely related, so this just confirms what is known. The authors should acknowledge this and shorten this section significantly.

4. On line 349 the authors state that 'any substitution on the receptor disrupts the function of the receptor'. This is not true. There are several known benign mutations that have no effect on CaSR function.

5. I found the section based around Table 2 very difficult to follow. Initially I presumed these were variants that have not been functionally characterized that the authors would predict, then test in vitro. However, this is not the case as several have been functionally assessed (e.g. I857X, T186N, T699N, R701G, T808P). The authors should add another column to state which have been functionally assessed and what this showed. This is important as their predictions are clearly wrong for some residues (e.g. T699N has been functionally assessed and shown to be LOF). This makes it difficult to understand what the point of the tool is. The authors should expand out their analysis to look at many more residues that are known to cause disease to really assess how useful the tool is (e.g. those reported in multiple families or those that have been functionally assessed). They should also test on residues with both GOF/LOF mutations.

6. It was unclear why the authors focussed on one cryo-EM model. There are multiple models that have been published that implicate different residues in receptor activation. The authors should look at these models too.

7. The authors state that mutations in the TM domain result in GOF. There are many examples of known inactivating mutations in the TMD and several switch residues (with LOF/GOF). This statement needs revising.

8. The discussion largely re-states the results and doesn't place the research within the context of the current literature. This needs extensive re-writes.

Minor comments:

1. Abstract - The first sentence doesn't seem to fit with the rest of the abstract. I suggest removing.

2. The authors should define 'clade' on its first usage as it is not a common word.

3. The authors italicise some sentences for unknown reasons. This needs removing.

4. Figure 2 and Figure 7 need revising as they are too small and/or illegible.

Significance

Mutations in the CaSR cause diseases of calcium homeostasis. Specifically inactivating mutations cause disorders of hypercalcemia, while activating mutations result in hypocalcemia. Bircan et al explore the evolutionary conservation of CaSR and try to use these findings to predict whether residues would be associated with hyper/hypocalcemia. This could be useful to researchers focussed on CaSR, particularly clinical geneticists or practising clinicians that may identify genetic variants in the receptor and require tools to predict pathogenicity. However, the manuscript does not fulfil these aims in its current form.

It is very difficult to follow what the authors have done and what the purpose of the research is. The results section needs more sub-headings as at the moment it is too long, has too many methodological details and is very difficult to follow. The discussion needs completely re-writing as it doesn't really discuss the findings in the context of the current literature. I have tried to outline the areas that need improving the most.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Bircan et al. employ phylogeny-based methods and machine learning to determine positions in the Calcium Sensing Receptor (CaSR) that are specific for this receptor compared to those residues that are important for CaSR and related subfamilies. Using machine learning, the authors predict whether selected mutations in CaSR will lead to loss- or gain-of-function and compare this with experimental results from literature.

Minor comments:

• line 13/14: 'there are still gaps in our understanding of its specific residues' - possibly change to 'there are still gaps in our understanding of the specific function of its residues'?

• line 17/18: 'The analysis revealed exceptional conservation of the CaSR subfamily, with high SDP scores being critical in receptor activation and pathogenicity' - are the SDP scores critical or some aspect of the receptor, i.e. the residues with high SDP scores?

• lines 42-44: 'L-amino acid binding site at the interdomain cleft of LB1-LB2 and multiple Ca2+ amino acid binding sites on the VFT domain' - Should this be 'Ca2+ binding sites' instead?

• lines 45-47 'While Ca2+ is the composite agonist for the CaSR, L-amino acids promote receptor activation along with Ca2+, but they are not able to activate the receptor alone'. - Unclear

• lines 139, 146 'a ML tree' - should be 'an ML tree'

• line 153 'γ-aminobutyric acid-B receptorsreceptors' - remove 'receptors'

• line 162-164 'Comparison analysis of branch lengths (Patil, 2021) among common species between CaSR, GPRC6A and taste receptors shows that the CaSR subfamily is significantly more conserved than its closest subfamilies' - could you please give a very short explanation here for the non-specialists?

• Fig 2A is unfortunately mostly unreadable. I would suggest replacing panel A with (an) alternative panel(s) clearly showing the stated results and moving the tree into the supplementary and/or making it available in a format that can be studied more closely.

• Fig. 4A, right side. Both the x-axis and the bar colour are labelled 'SDP scores', but they don't agree with each other. Please clarify what is what.

• Fig. 5 the numbers associated with the colour scales are unfortunately not readable

• lines 394/5: 'Because CaSR is a highly conserved subfamily, any substitution on the receptor disrupts the function of the receptor and causes either GoF or LoF mutations.' - do you mean that no mutation in CaSR may be neutral?

• Fig 7 is mentioned earlier than Fig 6.

• line 516/7 and 532/3: ' we repeated the train-validation-test splitting procedure fifty times' - repetitive

• Fig 6: what are the features in the bottom panel of 6B?

Significance

General assessment: The study uses computational methods to assess the importance of residues in the CaSR for function. The results are compared with the literature, as far as data are available. The study could be made more accessible to non-experts by putting results in context, more explanations in the figure legends and by making sure that the results mentioned in the text can easily be followed by looking at the figures. Another option could be to change subtitles in the results section to summarise the main findings of the section.

Advance: This study uses phylogeny-based methods to advance our understanding of the role of residues in a GPCR and adds to our pool of techniques available for addressing such questions.

Audience: The described research should be of interest for researchers working on CaSR, those interested in the evolution of GPCRs, and those studying the impact of point mutations in GPCRs on function and/or human health. I do not have sufficient expertise to evaluate the phylogeny-based methods used in this manuscript. At present the manuscript seems more likely to be of interest to a specialised audience, which could very likely be changed by making the manuscript more accessible to GPCR researchers that don't have a background in phylogeny-based methods.

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Referee #1

Evidence, reproducibility and clarity

This study aims at identifying key positions in the CaSR responsible for its specific properties. For that aim, they aligned all class C GPCR sequences and classified them according to their sequence identity and degree of conservation among orthologs. The final aim was to be able to predict the functional consequences of point mutations, as based on the degree of conservation of each residue within the orthologs, and within homologs. They include some considerations to predict whether the mutations of some of the conserved residues may lead to gain or loss of function. I definitively believe much can be learned from the sequence evolution of a protein, as highly conserved residues mean something. As such, a study like this one is of interest. However, I am far from convinced on their final approach to predict LoF and GoF mutations. Indeed, as far as I understood, they did consider the residue position, and its conservation either in the orthologs only, or also in some homologous sequences. However, they did not consider the type of mutation. In my opinion, a mutation at a given position may well be either LoF or GoF depending on the new residues. One can easily understand that a mutation into Gly or Trp may have very different effect. They also considered that mutations in the 7TM core domain are more prone to generate GoF. This is a statistical view of what could be going on, but by no way this can be included as a criteria to decide on the consequence of the mutation, as both LoF and GoF mutations can be found in this domain. Lastly, there exist a very long list of mutation of the CaSR with known functional consequences. These must be used to validate the authors' approach. In my opinion, validating theyr approach would mean making a long list of what their analysis can prediction with a large number of positions of the CaSR, not considering our actual knowledge along these lines, and then compare they prediction with what is already known. Eventually, for a few predictions for which there is no data supporting either their LoF or GoF effect, these should simply be tested to give the readers an expectation on the viability of their approach.

Significance

I must clearly state that I not a specialist of the bioinformatic approaches used in this study, and as such cannot judge all these aspects of the work presented in this story. However, I am also far from convinced with the analysis and the conclusions, that, in my opinion, are not in line with my views on this topic. One key aspect is that the authors only considered mutations at specific positions in the CaSR, with the aim to predict their loss of gain of function effect. However, in my opinion, such a functional consequence not only depends on the residue mutated, but also into which residue it is converted. I cannot see that a mutation into Ala, Gly or TRP could have the same effect. As such, I cannot recommend acceptance of this paper.

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Reply to the reviewers

Response to the three reviewers:

We thank the reviewers for the time they spent reading and evaluating our work, and for their comments and constructive criticisms.

The three reviewers contested the novelty and significance of our findings. Their main arguments were that the role of plakin/desmosomes in the regulation of epithelial polarity is already known and that our work does not provide any novel mechanistic link between them and the process of cell polarization.

To the first point we would like to argue that although a general relationship between plakins and cytoskeletal filaments networks, and notably cytokeratin, has been involved in the regulation of both intercellular junction strength and cell migration, their involvement in the asymmetric positioning of organelles in polarized cells has not yet been proposed nor demonstrated. However, in the light of reviewers’ comments, we admit that our wording has been misleading and that we have used the term “epithelial polarity” when it would have been more rigorous to use the term “asymmetric centrosome position in polarized epithelial cells” to describe our observations. We have modified our text to make this clearer and to streamline our descriptions and conclusions on the regulation of centrosome position and the associated asymmetry of the microtubule network. Considering this, we would like to stress out that our discovery about the specific involvement of three plakins (epiplakin, periplakin and desmoplakin) in the regulation of centrosome position in epithelial cells is novel (see our more detailed argumentation below) and fully demonstrated with our data. We insist that these discoveries are significant since we identified these plakins thanks to the changes of their expression levels in two set of cell lines representing progressive stages of mammary breast cancer. Finally, it is important to stress out that our experimental approach is also original since we used a cellular metric, the centrosome position, to interpret and sort transcriptomic data sets. This strategy of mixing cell biology and bioinformatics has proved fruitful and is thus likely to also become influential.

        To support our argumentation that the identification of the role of plakins in the regulation of epithelial cell polarity is novel, we searched for the words “polarity” and “(epi/peri/desmo)plakin” in PubMed.

• “Polarity and epiplakin” returned 1 review (PMID 24352042)
• PMID 24352042: It is a review that we cited, in which it is argued that plakins contribute to cell polarity as they bind to all cytoskeleton filaments and connect them with intercellular junctions. The section dedicated to polarity referred to two specific studies: one about BPAG1e, a member of the plectin family of plakin which is involved in the front-rear polarity of migrating keratinocytes, and one about the spetraplakin MACF1, which crosslinks actin and microtubules and is involved in the polarization of epidermal stem cells. The review also refered to the role of plectin in the regulation of centrosome position by attaching it to intermediate filaments.
• “Polarity and periplakin” returned 1 review, the same as above, and 2 experimental papers (PMID 23777851 and 18823282)
• PMID 23777851: It is a study on the protein expression profiles of skin cells derived from patients with Atopic dermatis. Authors found that TH17 cytokines, a inflamatory pathway involved in the differentiation and polarization of naive lymphocytes, was activated and the expression of TH17-related molecules was negatively correlated with periplakin.
• PMID 18823282: It is a characterization of the ubinuclein, which is known to be essentially nuclear but was could be localized to lateral cell borders in differentiated keratinocytes characterized by the expression of involucrin and periplakin.
• “Polarity and desmoplakin” returned 87 references, most of them related to the role of desmosomes in the establishment of the apical pole of epithelial cells, but only two of those references are specifically related to the centrosome. They showed that CSSP1 and ninein, two centrosomal proteins, can bind to desmosomes via desmoplakin (PMID 26241740, 17227889). But they are not related to centrosome positioning. The two papers are now cited in our discussion anyway. Based on this search, it seems to us that the establishment of the causal role of these three plakins in the role of centrosome position in polarized epithelial cells is clearly novel.

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

Summary The manuscript by Geay and colleagues examine potential regulators of centrosome positioning in an immortalised breast cell line in vitro on micropatterns that promote cell doublet formation. The authors mine expression data from breast cancer cell lines in vitro to identify microtubule-related transcripts that are potentially downregulated in cells with a mesenchymal phenotype. The authors identify some Plakin proteins, which upon depletion, are reported to change centrosome positioning relative to junctions. The authors propose that plakins are involved in the maintenance of epithelial polarity.

Major comments I applaud the authors for attempting to identify novel regulation of epithelial polarity. However, I am sorry to say that this manuscript is overtly preliminary. It is a collection of observations without any mechanistic insight (described below). Despite what I write below, I apologise in that these shortcomings as so extensive that I cannot recommend experiments that would 'fix holes', without essentially writing an entirely new project. Even after addressing the points below, I think it unlikely that the observations would make a coherent, mechanistic contribution to the field of epithelial polarity. I do not like to give reviews like this, but unfortunately, the submission of such preliminary works puts us in this position.*

Authors: It is correct that we did not investigate the underlying mechanism, and thus our work is preliminary from this point of view, but we provided the first set of evidence that the three plakins (epiplakins, periplakins and desmoplakins) are involved in the regulation of centrosome position and the associated asymmetry of the microtubule network in polarized epithelial cells. This identification was far from obvious, and relied on an unusual way to exploit transcriptomic. Data, which we think is quite valuable. We correlated the level of transcripts to a quantitative measurement of cell organisation (the distribution of nucleus-centrosome vectors). This strategy is novel and proved useful since we identified novel regulators of centrosome positioning.

1. • 'Epithelial polarity' Throughout manuscript the authors refer to a 'polarity score' and the term 'epithelial polarity' when what they have actually measured is a specific angle of orientation of centrosomes in cell doublets in vitro. This is an overstatement and adds confusion. The term 'epithelial polarity' has overtones of a polarised epithelium, which such doublets do not model. There is no mechanistic investigation into how this polarity score relates to the ability to form a polarised epithelial monolayer, with apical-basal polarity orientations, either a monolayer on a substrate or a monolayer surrounding a single central lumen, such as these MCF10A cells are often used for in 3-dimensional culture. I suggest that the authors simply mention what they actually measure (and in their own words): "coordination of the centrosome along the nucleus-junction axis." *

Authors: This is correct and we apologize for the confusion. We have now corrected the text and refer specifically to the “position of the centrosome in polarized epithelial cells” instead of “epithelial polarity”. However, it should be noted that we and others already showed that this position is relevant to the establishment of polarity in vitro in 3D culture, and in vivo in developing mouse embryo (Rodriguez-Fraticeeli et al., J Cell Biol, 2012) (Burute et al., Dev Cell, 2017). We have now added a paragraph at the end of the introduction to clarify this point and justify our experimental approach.

• In Figure 1A-C, cell doublets are reported and apparently quantified to measure a 'polarity score', which is the angle of orientation of centrosomes in cell doublets. Yet, there is no clear information that explains how the cutoff for what defines this polarity score is generated (e.g. why is the cutoff point chosen to be where it is?), or what it means for epithelial polarity (e.g. why is this cutoff point important to be at that site?). Moreover, there is no indication that these cells actually form connected doublets. Labelling and quantitation of potentially connected cells is absent. Do these actually form junctions to the same extent, such that any differences have been exhaustively excluded to be only from the centrosome orientation, rather than cell spreading and cell-cell contact differences (that would alter geometry)? In addition, statistical analysis for part C is missing. *

Authors: First, it is true that the geometrical sectioning of cells in order to define a region where centrosomes are considered as polarized toward the junction is arbitrary. But isn’t it the case for most thresholds in image analysis? This is how it has been done in all studies of the polarity of migrating cells during would healing for example. What we think is key here, is that the chosen angular sector for polarized centrosomes, is the same for all conditions, so it allowed us to compare the frequency of polarized centrosome based on this criterium.

Second, it is also true that for the sake of conciseness we did not show too many data about the characterization of the doublets in order to focus on the criteria that we used for our study. But we analyzed the shape of the doublets. In this example below, we measured how “pinched” were the doublet as compared to a a fully convex envelope. Small intercellular junctions lead to high difference between the area of the convex hull and the area of the doublets. However, we did not find that doublets of comparable cell lines with distinct polarity index, such as HCC1937 and HCC1143, had distinct junction length:

Finally, there is no statistical analysis for in the histogram shown in Figure 1C since we did not compare the polarity index of the different cell lines. We related them to their transcriptomic profiles (Figure 1D).

3.

*Fig 1D, 2A,B present select example genes correlated with either polarity score or EMT score (Fig 1D, 2B). It is unclear what insight providing select genes from many that are changed provides. In Fig 2A, an apparent EMT score (seemingly derived from mining of existing expression data not from this laboratory) is provided, ranked by an EMT. No description is provided for what these alterations are (e.g. what is a 'HME_Ras_Twist1E12_TGFb' sample?). Further, what this is supposed to indicate as a mechanistic insight is unclear. *

Authors: These panels illustrate examples of protein for which the level of transcripts was well correlated (negatively or positively) to the polarity or EMT scores of the various cell lines we tested. We did not describe again these cell lines and referred to the study where they have been described in details since the conditions leading to their phenotypes were less relevant than the consequence on gene expression and EMT progression, which were described in our text and data. There was no specific value in the chosen proteins in Figure 1D and 2B, they simply illustrate how various transcript levels can be compared, and potentially correlated, to geometrical measurement (in the case of the polarity score, 1D) or to a identity measurement (in the case of the EMT score, 2B). There is no mechanistic insight at this stage. Figure 1 and 2 only illustrate the novel method we proposed to extract information about cell architecture or cell identity from transcriptional data sets. The most valuable information will come in Figure 3 in which we will cross these two pieces of information.

• Figure 3 is highly preliminary. The entirety of Figure 3 is a correlation plot between EMT score and polarity score for microtubule-related transcripts. *

Authors: We respectfully disagree. Some misunderstanding might explain reviewers’ comment. This is not a “correlation plot between EMT score and polarity score for microtubule-related transcripts”. The values are not the scores but the correlation between the transcript level and the scores (which were described in Figure 1D and 2B that we discussed in the two previous comments of the reviewer). This is much more informative and definitely not preliminary, since it revealed potential structural (polarity score) and functional (EMT score) implications of proteins that were not known before. Proteins on the top-left or bottom right of the graph are all candidate to influence EMT by acting on the structural polarisation of cells.

*The authors state: "The graph showed an overall negative trend, which means that many genes were positively correlated with an EMT in HME were instead negatively correlated with epithelial polarity of TNBCs (Figure 3). This was expected and confirmed that the progression along EMT is associated with a loss of epithelial polarity." No statistical analysis is presented, no correlation scores and indication of robustness is provided. It is unclear how this provides any mechanistic insight. The authors themselves state that this association is expected. *

Authors: We apologize for this. We now reported the statistical analysis that confirmed our previous description of a negative trend in this graph. Pearson correlation coefficient is -0.35 (p-value = 0.00023, 95% confidence interval: [-0.50, -0.17]. We have added these details in the main text and Material and Methods. It is correct that this tendency could be expected by considering various studies together, but it is still better when rigorously demonstrated.

*Moreover, the authors state "Interestingly, three plakins, namely epiplakin (EPPK1), desmoplakin (DSP) and periplakin (PPL) all appeared as clear outliers (Figure 3)." How is an outlier defined & why is this clear? Is the association of these key cell-adhesion molecules with an epithelial cell state novel or known? *

Authors: We define classically outliers as genes with a score higher than the 75th Percentile + 1.5 times the InterQuartile Range (IQR). 7 genes were outliers, including the three plakins. We have now detailed the procedure in a dedicated section in Material and Methods.

• Figure 4. The authors perform siRNA-mediated depletion of Desmoplakin, Epiplakin and Periplakin in MCF10A cells. The authors report, "Interestingly, knocked-down cells in culture displayed abnormal shapes, being more elongated and less cohesive (Figure 4C)." No quantitation of such changes are provided. Moreover, cells with KD appeared to be at lower density. Can the authors exclude that these are not merely density-dependent effects.*

Authors: This is really just a description of the images. The densities didn't seem that different to us, but it is true that we can't rule out a density effect. We didn't do a detailed quantitative description of these phenotypes because they were not central to the argument about centrosome position. However, we thought these images of knock-down cells were worth showing.

• Throughout the work, the polarity index is reported from plakin depletion conditions with data from a reported 3 independent experiments seemingly pooled (no indication of graph of which independent experiment each data point comes from). Is the statistical analysis performed (missing in Fig 4E, present in Fig 5A-C, S2, S3) from pooled data? If so, this is in appropriate and should be from the averages of independent experiments, to understand batch effects. If not from pooled data, please alter graphs to display this appropriately. *

Authors: We showed only one data set per conditions to avoid graph over-crowding. We know show these 3 different experiments with distinct colors in the graphs (SuperPlots). Noteworthy, the exact same experiments were performed with another set of siRNA for each of the three plakins and they show exactly the same effect (see Figure S2).

• Figure 5A. It is unclear how F-actin is measure in the images. Is F-actin labelling a truly representative proxy for junction length? *

Authors: This is correct, we assumed that the frontier between the two cells, which could be seen with F-actin, corresponded to the intercellular junction.

• Fig 5C. Why are images of vimentin now provided not on micropatterns? The labelling of vimentin in siPeriplakin cells does not look appropriately controlled for by the other cell conditions. siPeriplakin is clearly at the edge of a colon, whereas this is not clear whether an appropriate region is labelled in the other conditions. *

Authors: We performed experiments on micropattern when the aim was to characterize the localization of a protein or a compartment, since micropattern normalize cell shape and orient cell architecture. Here our aim was to visualize the global amount of a protein, so micropatterns were not needed. Actually, western blots would have been better suited for these experiments. But these were the data we had. Pictures that were shown have all been taken at the edge of a colony. The boundary is visible on all images.

Reviewer #1 (Significance (Required)):

*In the literature, there is a rich understanding of the molecular mechanisms of the cross-talk between cell-cell junctions, cell polarity complexes, and the organisation of the cytoskeleton. The authors are applauded for efforts to investigate whether there are common transcriptional downregulations of microtubule-related proteins that could potentially be key regulators of cellular polarisation. It is unfortunate that the work, as presented, is a series of modest observations, often the insight of which is overstated. Despite the analysis of plakins as a potential regulators of centrosome positioning between cell doublets, there is no mechanistic insight into a) how these plakins contribute to centrosome alignment asymmetry, or b) whether this is any way has an effect on true epithelial polarisation (beyond potential doublets on a micropattern). If significant development of mechanistic insight was added (requiring extensive additional experimentation, expected: 1-2 years of work), then the manuscript might be of interest to the cell biology community. *

Authors: Our observations can be considered as modest but they are solid and novel and, to our point of view, significant. We acknowledge that the use of the term “epithelial polarity” instead of “asymmetric centrosome positioning” is an overstatement the impact of our observations and corrected it (including in the title). However, we think, based on previous works that are now better described in the revised version of our introduction, that the position of the centrosome in micropatterned cell doublets is a meaningful readout of the polarization of the organization of epithelial cells.

It is true that we don’t provide the molecular and physical mechanism by which plakins affect centrosome position. And this would indeed deserve another complete study. However, since no previous work reported that plakins were involved in centrosome position, we think our work will be a valuable contribution to the field of cell polarity and to the recently rapidly growing field of plakins.

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

Summary The new paper by Geay and colleagues studies epithelial cell polarity of triple negative breast cancer (TNBC) cell lines using a special H-shaped microculture device and confocal microscopy of centrosomes. Using a quantification method that calculates a polarity score, the polarity phenotype of each breast cancer cell line is associated to the corresponding transcriptome analyzed using an Affymetrix microarray platform. In this manner, expression of specific genes is correlated to the polarity score.

In its second part, the study shifts its interest to the transdifferentiation process of EMT (epithelial-mesenchymal transition) and uses a published transcriptomic dataset based on human mammary epithelial cells that overexpress a series of oncogenic (Ras, TGF-beta) and EMT (ZEB1, ZEB2, TWIST1, E12) factors, and calculates an EMT score that is correlated to the expression of different genes identified in the published dataset. The interest in EMT is logical as EMT often correlates with the loss of epithelial cell polarity.

Based on the two gene lists and their respective phenotypic correlation, known regulatory components of microtubule dynamics that can potentially regulate centrosomal position and thus epithelial cell polarity, are selected. Among these are genes encoding for components of desmosomes, the plakin family, that link membrane-based intercellular adhesions intracellularly to intermediate filaments, mainly cytokeratins, and indirectly with microtubules. Using traditional siRNA-based technology and an immortalized, non-malignant breast epithelial MCF10A cell line, silencing of specific plakin family mRNAs is shown to lead to polarity defects that correlate with concomitant high expression of the intermediate filament vimentin, the latter often used as a molecular marker of the EMT process. In other words, silencing of plakins leads to loss of breast epithelial cell polarity and gain of vimentin, a sign of enhanced EMT. This is the central observation of this study that is also captured in the title and it is not carried any further towards a mechanistic or deeper analysis. *

Authors: We thank the reviewer for this fair and accurate description of our work

*Major comments: I have two general or conceptual comments and one major technical comment: 1) Unfortunately, the study does not provide an advance in terms of understanding the action of plakins as regulators of cell polarity or EMT. Both cellular processes are well characterized, and in the case of EMT, specific guidelines have been published that dictate the large number of complementary assays required for a proper assessment of EMT (see Yang, J., et al. Nat Rev Mol Cell Biol. 2020 Jun;21(6):341-352). *

Authors: This is correct. We did not elucidate the underlying mechanism but we identified the involvement of plakins in the regulation of centrosome position in polarized epithelial cells. Note that our aim was not to reveal new EMT regulator, but to reveal new regulator of centrosome positioning. We only took advantage of EMT as a natural mechanism that involves the destabilisation of epithelial polarity and the reversal of centrosome position. The focus and the experimental strategy of our study are now better explained in the revised version of our introduction.

*2) The plakins studied make the intracellular adaptor interface that links desmosomes to intermediate filaments, primarily cytokeratins. The paper does not even mention at all these two important epithelial protein networks, which I believe should have been studied in both TNBC and HME-EMT cell models. Furthermore, the paper tries to emphasize the regulation of microtubular networks because of their established importance in organizing proper centrosomal positioning. Yet, the presentation of results and the discussion appears rather confusing and unclear as to whether the data present any real effects of plakin expression manipulation on microtubules. It appears that such effects were not scored, which leaves the central aim of the project incomplete and raises issues that demand further and deeper analysis of the regulation of centrosome positioning by plakins. Can the centrosomal effects be completely indirect or bypasser effects due to the overall architectural change that epithelial cells undergo when their desmosomes lose their rigid coupling to cytokeratins? *

Authors: It is true that we did not study at all the mechanism by which plakins affect centrosome position. And cytokeratins would definitely by on the top list for such a study. We we focused our transcriptomic analysis to microtubule-binding protein, since they are likely involved in the regulation of centrosome positioning. But we did not investigate in details the role of microtubules in the mispositioning of centrosome we found in plakin mutants. As stated by the reviewer, centrosome mispositioning might not result from a direct role of plakins on microtubules. The mechanism could definitely involve desmosomes, cytokeratins or many other cytoskeleton components. The exploration of all these possibilities should be the focus of future studies. Our work simply provides multiple and solid evidences for the implication of plakins in the regulation of centrosome positioning and open the way for interesting follow-up studies.

*3) The classic siRNA-based method is used to silence plakin family mRNAs. This well-established technology today demands the use of multiple independent siRNAs per mRNA and also rescue experiments in order to confirm the absence of so-called off-target effects. *

Authors: This is correct. We used two distinct siRNAs per targeted proteins. The effect on centrosome mispositioning were quite similar with both sequences (see Figure S2). We did not have time to confirm the absence of off-target effects by rescue experiment. This is missing indeed and unfortunately, we don’t have the human resources to perform those experiments. But we would like to stress out that a direct correlation between the level of expression of the tree plakins we tested and centrosome mispositioning was established in the first part of the study that was based on the natural variation of their expressions in 12 cells lines.

Specific comments: I also enlist here some specific comments in the order of the figure presentation:

*3) Fig. 1A lacks the images of Hs-578T and MCF10A cells. *

Authors: This is correct. But MCF10A were already shown in our previous publication (Burute et al., Dev Cell, 2017). We did not want to insist on something already shown. Then we decided to show only 10 images as it would be odd to organise a panel with 11 images. Individual images are not so informative in this case, they are more illustrative and they are not so different from each other.

*4) The data of Fig. 1C demonstrate score of 15-30% for the TNBC and "normal" epithelial cells. These data must be discussed in the context of the established literature on cell polarity. Is a 30% score anticipated for a polarized cell type? Is the difference between 30 and 20% significant in terms of the polarity of cells within a tissue? What would such scores be if one studied highly polarized cell monolayers on transwell filters? Is the H-shaped microsystem reliable? *

Authors: This is a good remark and a fair concern. We can’t compare directly this “polarity score”, which is a metric about the position of centrosome, to the complete polarization of structures and signalling pathways in actual epithelial tissues in vivo. But we already studied the polarity of MDCK and MCF10A doublets (Burute et al, Dev Cell, 2017), which showed similar level of asymmetry in their centrosome position.

It is also fair to doubt of the reliability of H-shaped micropatterned. In our revised introduction (see last paragraph), we have now listed all the features that made us believe that the polarized organisation of intercellular junctions and associated components in micropatterned cell doublets is relevant to the establishment of polarity in polarized epithelial tissues in vivo. The list of polarized components was based on two independent works (Rodriguez-Fraticeeli et al., J Cell Biol, 2012) (Burute et al., Dev Cell, 2017). In addition, it should be noted that we also previously reported the inversion of centrosome position in epithelial cell doublets during TGF-beta-induced EMT in MCF10A, and that we also observed this repositionging in vitro in 3D mammary gland cultured cells and in vivo in vivo, in mouse mammary gland epithelia and in developing mouse embryo at gastrulation (Burute et al., Dev Cell, 2017).

*5) The gene expression data of the TNBCs or publicly available data for the same cell lines from TCGA should be used to generate a heat map that illustrates the positioning of the examined cells in the spectrum of luminal epithelial to claudin-low, mesenchymal breast cancer cells. *

Authors: Such an analysis would be interesting indeed. Actually, a lot of information about the role of plakin in the maintenance of epithelial polarity could be extracted from the comparison of transcriptomic profiles of these various stages of EMT. But this is a bit beyond the scope of our study which was more focused on the consequences of these changes on centrosome position.

*6) The 13 HME cell models used in Fig. 2A should be described in detail despite their earlier publication 11 years ago. This is important because the derived EMT scores are slightly counterintuitive: the parental HME cells are plotted as having a higher EMT score than the transformed HMEs expressing Ras or Twist1. How can this be explained? P53 is well established as an epithelial differentiation factor that counteracts EMT. Why does shp53 and especially combined with Ras overexpression not lead to EMT? I note that this cell model is listed as having epi and mes varieties. What are these and why are these important phenotypes not presented in the results? TGF-beta is presented in the results as a transcription factor, yet it is a secreted growth factor. What does TGF-beta mean? HME cells overexpress the cDNA for TGF-beta (which one? There are 3 TGF-beta genes)or were the cell cultured in the presence of this cytokine? *

Authors: These are interesting comments. Actually, one of the important observations of this earlier study was that mice over-expressing Ras alone or Twist alone in mammary tissues, either during embryonic development or later during mammary development induced by lactation, did not form invasive tumours. The expression of Ras induced low grade splenic lymphomas as well as anal and oral papillomas but they never progressed to the malignant stage. However, the combination of Ras and Twist expression had dramatic effects on the reduction of mice survival due to the formation of multifocal breast carcinomas with metaplastic features. So the absence of increase of the EMT score upon the overexpression of Ras or Twist alone is not so counterintuitive. But we can’t really explain how cells became “more epithelial” though. We think that it would be long and not so conclusive to enter into those details in the main text.

        Cells silenced for p53, to resist from oncogene-induced senescence and apoptosis, and over-expressing Ras could express or not EpCAM and thus were sorted in EpCAM positive (epi) or EpCAM negative (mes). In some conditions, TGF-beta was added to cells to induce EMT. The combinations of these various treatments induced more or less aggressive transformations that are described in this earlier study but we think it would take too long to describe them here.

In the end, what mattered for our study, was that this set of cell lines allowed us to explore a broad range of EMT scores, which we could correlate to variations of transcriptomic profiles.

*7) Minor semantic comment: does Fig.2B show collagen V or collagen XV? Related to this, the article has abundant typographical errors. *

Authors: It was collagen V. We checked for other typos and hope to have corrected them.

*8) Fig. 4: based on the major comment, this experiment requires analysis of rescue clones. *

Authors: We fully agree, these experiments are missing indeed. Unfortunately, we don’t have the human resources to perform those experiments. However, it should be noted that the specificity of the target is somehow supported by the observation of the exact same phenotypes upon the use of another siRNA sequence for each plakins (Figure S2). In addition, we would like to stress out that a direct correlation between the level of expression of the tree plakins we tested and centrosome mispositioning was established in the first part of the study that was based on the natural variation of their expressions in 12 cells lines (Figure 1).

*9) Fig. 5C: the vimentin microscopy needs to be complemented with full EMT analysis using both microscopic and protein expression assays (see major comment). More importantly, desmosomal and cytokeratin organization analysis is missing. *

• *

Authors: We agree that an immunostaining of vimentin is way too preliminary to conclude about an actual induction of EMT. Hence our tempered conclusion about the “suggestion that cells might be engaged in a form of EMT”. As also mentionned by reviewer #1 a full characgterization of the EMT state of these cells would require a long list of measurements, including the quantification of EMT-related transcripts and other structural analysis like desmosome and cytokeratins. But we don’t have the manpower to perform these experiments. Considering the broad interest of our community for the induction of EMT we thought that these observations were sufficiently interesting to be reported although they were somehow distant from the focus of our study on centrosome positioning.

*10) Fig. 5C: In the desmoplakin and periplakin knock-down experiments the cells stained for vimentin appear to have their vimentin "baskets" rather well polarized. Is this true or my impression based on the few cells illustrated in the images? If the cytoskeleton is polarized, what does one mean with loss of cell polarity? Is centrosomal polarity change associated with mesenchymal (back to front) polarity gain? If this is true can polarity be established by studying only 2 cells in the H-shaped microcultures? Is it not more relevant to allow cells build a cohort of inter-adherent cells? *

Authors: This is an interesting observation and a thoughtful analysis. And indeed, it can be seen in the quantification of polarity indices of periplakin knocked-down cells (see Figure 4E and figure S2) that the distribution seems to contain two distributions, one of epithelial-like orientation (values closed to +1) and one of reversed orientation (values closed to -1), toward the ECM, similar to our previous description of polarity reversal during EMT (Burute et al, Dev Cell, 2017). This suggest that indeed the knockdown of periplakin might not only impair the epithelial apico-basal polarity but also promote mesenchymal front-back polarity. Although interesting, we found it a bit too speculative to be stated in our revised version.

*Reviewer #2 (Significance (Required)): *

* Significance: The paper provides a quantitative analysis of single cell polarity and gene expression-based EMT and identifies plakin gene family members as potential regulators of cell polarity. If this finding can be substantiated via mechanistic work it will make an important contribution to epithelial cell biology. *

* General assessment: As explained above, the paper is in a preliminary state, as it describes an observation that demands further analysis. Key cell biological constituents (desmosomes, cytokeratins) have not been included in the analysis. Specific key figure data are presented without explanation for the non-specialist, especially those data that have been generated based on older publications by some of the authors. *

* Advance: At the present state, the paper does not make any advance but describes potentially interesting observations. *

* Audience: This paper can stimulate interest in the broader field of cell biology and definitely more to the cell polarity and EMT sub-fields. *

Authors: It is true that we don’t provide the molecular and physical mechanism by which plakins affect centrosome position. And this deserves indeed further characterisation. However, our work provides multiple and solid evidences for the implication of plakins in the regulation of centrosome positioning in epithelial cells and thus opens the way for interesting follow-up studies. Since no previous work reported this role of plakins, we think our work will be a valuable contribution to the field of cell polarity and to the recently rapidly growing field of plakins.

*My field of expertise: I study signal transduction and transcriptional mechanisms that regulate the EMT and its association with cell proliferation in cancer cells. I have also specialized on studying dynamics of cytoskeletal assembly and architectural cell organization.

*

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

In this article the authors have analyzed the genes related to epithelial cell polarity and report the relevance of the desmosomal proteins epiplakin, desmoplakin and periplakin in this process. These genes are downregulated in cells that have lost cell polarity and their lack of expression correlates with the emergence of an EMT program. Moreover, interference in the expression of these proteins increase vimentin and likely other mesenchymal markers. The experiments are very neatly done, with all the appropriate controls; the methodology is adequate, the figures are well designed and are reader-friendly and the results have some interest. Therefore, I do not have objections related to these issues, other than two minor question indicated below. *

Authors: We thank the reviewer for this positive assessment of our work

*- Other EMT markers should be easily assessed in the cells transfected with the plakins shRNAs to analyze the extent of EMT in these cells. *

Authors: We agree that an immunostaining of vimentin is way too preliminary to conclude about an actual induction of EMT. Hence our tempered conclusion about the “suggestion that cells might be engaged in a form of EMT”. As also mentionned by reviewer #1 a full characterization of the EMT state of these cells would require a long list of measurements, including the quantification of EMT-related transcripts and other structural analysis like desmosome and cytokeratins. But we don’t have the manpower to perform these experiments. Considering the broad interest of our community for the induction of EMT we thought that these observations were sufficiently interesting to be reported although they were somehow distant from the focus of our study on centrosome positioning.

*- It would be interesting if the article is reviewed by a scientist with a deeper knowledge in EMT because the text contains some inaccuracies related to this process and the main references are outdated. *

Authors: It is unfortunate that the reviewer was not more specific in his/her assessment. There are lots of references in the field of EMT. Not so many are related to the polarized organization of cells and we tried to cited those we found significant. We have added more recent references in the revised version of our introduction. We hope this will be satisfactory but we would be happy to complement this list.

*Reviewer #3 (Significance (Required)):

However, the significance of the conclusions is very limited. The relevance of desmosomes in cell polarity was described time ago by the Fuchs' group (see Lechler T, Fuchs E, J Cell Biol 2007, 176, 147-154); since then, this topic has been investigated by many other labs. For a more recent work see "Desmosomes polarize and integrate chemical and mechanical signaling to govern epidermal tissue form and function" Broussard et al, Curr Biol 2021, 31, 3275-3291. *

Authors: This is correct. The role of desmosome in the establishment and maintenance of the apical pole of epithelial has been well established. However, their role in the positioning of centrosome is much less clear.

Please note that the paper by Lechler and Fuchs is not about epithelial polarity. It describes the loss of astral organisation of microtubules in differentiating epidermal cells forming desmosomes thanks to the recruitment of ninein to desmosoems by desmoplakin.

Please also note that the other study by the group of Kathleen Green is about the role of desmoplakin in ensuring distinct mechanical states in the apical and basal pole of epidermal cells. It is not related to the organisation of the microtubules, nor is it related to the position of the centrosome. So it is unclear to us how these works limit the significance of our findings about the role of plakins in the control of centrosome position and the establishment of apico-basal polarity. We were happy to include them in the revised version of our discussion anyway.

Furthermore, our work is about three distinct plakins: periplakin, epiplakin and desmoplakin. Although they all localise to desmosomes their specific roles in the establishment and maintenance of epithelial polarity has not yet been established (as detailed in the general comments we wrote in the opening of this letter and in the revised version of our discussion). In addition, their specific roles should be distinguished from the multiple roles of desmosome in cell polarity, which involve inter-cellular junctions and connections to various inner cytoskeleton networks.

So, although we acknowledge that a mechanistic understanding would significantly increase the strength of our study, we still believe that the demonstration of the involvement of these three plakins in the regulation of centrosome position in polarized epithelial cells is novel and significant.

*Therefore, the authors need to analyze the mechanism with a greater detail if they want to contribute to the advance of this field. As a possible suggestion, they might use their plakin shRNA-transfected cells to investigate the signaling pathways that are altered, to transfect different desmoplakin mutants and describe their effects. *

* Related to desmosome alterations and EMT, this has also been indirectly concluded in an article quoted by the authors (Chun and Hanahan). This might be also studied by the authors assessing if the main transcriptional factors related to EMT are altered in these cells. *

Authors: We thank the reviewer for these constructive suggestions to deepen our investigation. The identification of these pathways could definitely highlight the mechanisms involved in the regulation of centrosome positioning. However, this is somehow beyond the scope of this study which was focused on the identification of regulators of centrosome asymmetric positioning in polarized epithelial cells. Counterintuitively, molecular motors did not seem to be involved. But several plakins were revealed. Further studies are now required to understand how they impact centrosome position.

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Referee #3

Evidence, reproducibility and clarity

In this article the authors have analyzed the genes related to epithelial cell polarity and report the relevance of the desmosomal proteins epiplakin, desmoplakin and periplakin in this process. These genes are downregulated in cells that have lost cell polarity and their lack of expression correlates with the emergence of a n EMT program. Moreover, interference in the expression of these proteins increase vimentin and likely other mesenchymal markers. The experiments are very neatly done, with all the appropriate controls; the methodology is adequate, the figures are well designed and are reader-friendly and the results have some interest. Therefore, I do not have objections related to these issues, other than two minor question indicated below.

• Other EMT markers should be easily assessed in the cells transfected with the plakins shRNAs to analyze the extent of EMT in these cells.

• It would be interesting if the article is reviewed by a scientist with a deeper knowledge in EMT because the text contains some inaccuracies related to this process and the main references are outdated.

Significance

However, the significance of the conclusions is very limited. The relevance of desmosomes in cell polarity was described time ago by the Fuchs' group (see Lechler T, Fuchs E, J Cell Biol 2007, 176, 147-154); since then, this topic has been investigated by many other labs. For a more recent work see "Desmosomes polarize and integrate chemical and mechanical signaling to govern epidermal tissue form and function" Broussard et al, Curr Biol 2021, 31, 3275-3291.

• Therefore, the authors need to analyze the mechanism with a greater detail if they want to contribute to the advance of this field. As a possible suggestion, they might use their plakin shRNA-transfected cells to investigate the signaling pathways that are altered, to transfect different desmoplakin mutants and describe their effects.

• Related to desmosome alterations and EMT, this has also been indirectly concluded in an article quoted by the authors (Chun and Hanahan). This might be also studied by the authors assessing if the main transcriptional factors related to EMT are altered in these cells.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The new paper by Geay and colleagues studies epithelial cell polarity of triple negative breast cancer (TNBC) cell lines using a special H-shaped microculture device and confocal microscopy of centrosomes. Using a quantification method that calculates a polarity score, the polarity phenotype of each breast cancer cell line is associated to the corresponding transcriptome analyzed using an Affymetrix microarray platform. In this manner, expression of specific genes is correlated to the polarity score.

In its second part, the study shifts its interest to the transdifferentiation process of EMT (epithelial-mesenchymal transition) and uses a published transcriptomic dataset based on human mammary epithelial cells that overexpress a series of oncogenic (Ras, TGF-beta) and EMT (ZEB1, ZEB2, TWIST1, E12) factors, and calculates an EMT score that is correlated to the expression of different genes identified in the published dataset. The interest in EMT is logical as EMT often correlates with the loss of epithelial cell polarity.

Based on the two gene lists and their respective phenotypic correlation, known regulatory components of microtubule dynamics that can potentially regulate centrosomal position and thus epithelial cell polarity, are selected. Among these are genes encoding for components of desmosomes, the plakin family, that link membrane-based intercellular adhesions intracellularly to intermediate filaments, mainly cytokeratins, and indirectly with microtubules. Using traditional siRNA-based technology and an immortalized, non-malignant breast epithelial MCF10A cell line, silencing of specific plakin family mRNAs is shown to lead to polarity defects that correlate with concomitant high expression of the intermediate filament vimentin, the latter often used as a molecular marker of the EMT process. In other words, silencing of plakins leads to loss of breast epithelial cell polarity and gain of vimentin, a sign of enhanced EMT. This is the central observation of this study that is also captured in the title and it is not carried any further towards a mechanistic or deeper analysis.

Major comments:

I have two general or conceptual comments and one major technical comment:

1) Unfortunately, the study does not provide an advance in terms of understanding the action of plakins as regulators of cell polarity or EMT. Both cellular processes are well characterized, and in the case of EMT, specific guidelines have been published that dictate the large number of complementary assays required for a proper assessment of EMT (see Yang, J., et al. Nat Rev Mol Cell Biol. 2020 Jun;21(6):341-352).

2) The plakins studied make the intracellular adaptor interface that links desmosomes to intermediate filaments, primarily cytokeratins. The paper does not even mention at all these two important epithelial protein networks, which I believe should have been studied in both TNBC and HME-EMT cell models. Furthermore, the paper tries to emphasize the regulation of microtubular networks because of their established importance in organizing proper centrosomal positioning. Yet, the presentation of results and the discussion appears rather confusing and unclear as to whether the data present any real effects of plakin expression manipulation on microtubules. It appears that such effects were not scored, which leaves the central aim of the project incomplete and raises issues that demand further and deeper analysis of the regulation of centrosome positioning by plakins. Can the centrosomal effects be completely indirect or bypasser effects due to the overall architectural change that epithelial cells undergo when their desmosomes lose their rigid coupling to cytokeratins?

3) The classic siRNA-based method is used to silence plakin family mRNAs. This well-established technology today demands the use of multiple independent siRNAs per mRNA and also rescue experiments in order to confirm the absence of so-called off-target effects.

Specific comments:

I also enlist here some specific comments in the order of the figure presentation:

1) Fig. 1A lacks the images of Hs-578T and MCF10A cells.

2) The data of Fig. 1C demonstrate score of 15-30% for the TNBC and "normal" epithelial cells. These data must be discussed in the context of the established literature on cell polarity. Is a 30% score anticipated for a polarized cell type? Is the difference between 30 and 20% significant in terms of the polarity of cells within a tissue? What would such scores be if one studied highly polarized cell monolayers on transwell filters? Is the H-shaped microsystem reliable?

3) The gene expression data of the TNBCs or publicly available data for the same cell lines from TCGA should be used to generate a heat map that illustrates the positioning of the examined cells in the spectrum of luminal epithelial to claudin-low, mesenchymal breast cancer cells.

4) The 13 HME cell models used in Fig. 2A should be described in detail despite their earlier publication 11 years ago. This is important because the derived EMT scores are slightly counterintuitive: the parental HME cells are plotted as having a higher EMT score than the transformed HMEs expressing Ras or Twist1. How can this be explained? P53 is well established as an epithelial differentiation factor that counteracts EMT. Why does shp53 and especially combined with Ras overexpression not lead to EMT? I note that this cell model is listed as having epi and mes varieties. What are these and why are these important phenotypes not presented in the results? TGF-beta is presented in the results as a transcription factor, yet it is a secreted growth factor. What does TGF-beta mean? HME cells overexpress the cDNA for TGF-beta (which one? There are 3 TGF-beta genes)or were the cell cultured in the presence of this cytokine?

5) Minor semantic comment: does Fig.2B show collagen V or collagen XV? Related to this, the article has abundant typographical errors.

6) Fig. 4: based on the major comment, this experiment requires analysis of rescue clones.

7) Fig. 5C: the vimentin microscopy needs to be complemented with full EMT analysis using both microscopic and protein expression assays (see major comment). More importantly, desmosomal and cytokeratin organization analysis is missing.

8) Fig. 5C: In the desmoplakin and periplakin knock-down experiments the cells stained for vimentin appear to have their vimentin "baskets" rather well polarized. Is this true or my impression based on the few cells illustrated in the images? If the cytoskeleton is polarized, what does one mean with loss of cell polarity? Is centrosomal polarity change associated with mesenchymal (back to front) polarity gain? If this is true can polarity be established by studying only 2 cells in the H-shaped microcultures? Is it not more relevant to allow cells build a cohort of inter-adherent cells?

Significance

Significance: The paper provides a quantitative analysis of single cell polarity and gene expression-based EMT and identifies plakin gene family members as potential regulators of cell polarity. If this finding can be substantiated via mechanistic work it will make an important contribution to epithelial cell biology.

General assessment: As explained above, the paper is in a preliminary state, as it describes an observation that demands further analysis. Key cell biological constituents (desmosomes, cytokeratins) have not been included in the analysis. Specific key figure data are presented without explanation for the non-specialist, especially those data that have been generated based on older publications by some of the authors.

Advance: At the present state, the paper does not make any advance but describes potentially interesting observations.

Audience: This paper can stimulate interest in the broader field of cell biology and definitely more to the cell polarity and EMT sub-fields.

My field of expertise: I study signal transduction and transcriptional mechanisms that regulate the EMT and its association with cell proliferation in cancer cells. I have also specialized on studying dynamics of cytoskeletal assembly and architectural cell organization.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript by Geay and colleagues examine potential regulators of centrosome positioning in an immortalised breast cell line in vitro on micropatterns that promote cell doublet formation. The authors mine expression data from breast cancer cell lines in vitro to identify microtubule-related transcripts that are potentially downregulated in cells with a mesenchymal phenotype. The authors identify some Plakin proteins, which upon depletion, are reported to change centrosome positioning relative to junctions. The authors propose that plakins are involved in the maintenance of epithelial polarity.

Major comments:

I applaud the authors for attempting to identify novel regulation of epithelial polarity. However, I am sorry to say that this manuscript is overtly preliminary. It is a collection of observations without any mechanistic insight (described below). Despite what I write below, I apologise in that these shortcomings as so extensive that I cannot recommend experiments that would 'fix holes', without essentially writing an entirely new project. Even after addressing the points below, I think it unlikely that the observations would make a coherent, mechanistic contribution to the field of epithelial polarity. I do not like to give reviews like this, but unfortunately, the submission of such preliminary works puts us in this position.

1. 'Epithelial polarity' Throughout manuscript the authors refer to a 'polarity score' and the term 'epithelial polarity' when what they have actually measured is a specific angle of orientation of centrosomes in cell doublets in vitro. This is an overstatement and adds confusion. The term 'epithelial polarity' has overtones of a polarised epithelium, which such doublets do not model. There is no mechanistic investigation into how this polarity score relates to the ability to form a polarised epithelial monolayer, with apical-basal polarity orientations, either a monolayer on a substrate or a monolayer surrounding a single central lumen, such as these MCF10A cells are often used for in 3-dimensional culture. I suggest that the authors simply mention what they actually measure (and in their own words): "coordination of the centrosome along the nucleus-junction axis."

2. In Figure 1A-C, cell doublets are reported and apparently quantified to measure a 'polarity score', which is the angle of orientation of centrosomes in cell doublets. Yet, there is no clear information that explains how the cutoff for what defines this polarity score is generated (e.g. why is the cutoff point chosen to be where it is?), or what it means for epithelial polarity (e.g. why is this cutoff point important to be at that site?). Moreover, there is no indication that these cells actually form connected doublets. Labelling and quantitation of potentially connected cells is absent. Do these actually form junctions to the same extent, such that any differences have been exhaustively excluded to be only from the centrosome orientation, rather than cell spreading and cell-cell contact differences (that would alter geometry)? In addition, statistical analysis for part C is missing.

3. Fig 1D, 2A,B present select example genes correlated with either polarity score or EMT score (Fig 1D, 2B). It is unclear what insight providing select genes from many that are changed provides. In Fig 2A, an apparent EMT score (seemingly derived from mining of existing expression data not from this laboratory) is provided, ranked by an EMT. No description is provided for what these alterations are (e.g. what is a 'HME_Ras_Twist1E12_TGFb' sample?). Further, what this is supposed to indicate as a mechanistic insight is unclear.

4. Figure 3 is highly preliminary. The entirety of Figure 3 is a correlation plot between EMT score and polarity score for microtubule-related transcripts. The authors state:

"The graph showed an overall negative trend, which means that many genes were positively correlated with an EMT in HME were instead negatively correlated with epithelial polarity of TNBCs (Figure 3). This was expected and confirmed that the progression along EMT is associated with a loss of epithelial polarity."

No statistical analysis is presented, no correlation scores and indication of robustness is provided. It is unclear how this provides any mechanistic insight. The authors themselves state that this association is expected.

Moreover, the authors state "Interestingly, three plakins, namely epiplakin (EPPK1), desmoplakin (DSP) and periplakin (PPL) all appeared as clear outliers (Figure 3)."

How is an outlier defined & why is this clear? Is the association of these key cell-adhesion molecules with an epithelial cell state novel or known?

1. Figure 4. The authors perform siRNA-mediated depletion of Desmoplakin, Epiplakin and Periplakin in MCF10A cells. The authors report, "Interestingly, knocked-down cells in culture displayed abnormal shapes, being more elongated and less cohesive (Figure 4C)."

No quantitation of such changes are provided. Moreover, cells with KD appeared to be at lower density. Can the authors exclude that these are not merely density-dependent effects.

1. Throughout the work, the polarity index is reported from plakin depletion conditions with data from a reported 3 independent experiments seemingly pooled (no indication of graph of which independent experiment each data point comes from). Is the statistical analysis performed (missing in Fig 4E, present in Fig 5A-C, S2, S3) from pooled data? If so, this is in appropriate and should be from the averages of independent experiments, to understand batch effects. If not from pooled data, please alter graphs to display this appropriately.

2. Figure 5A. It is unclear how F-actin is measure in the images. Is F-actin labelling a truly representative proxy for junction length?

3. Fig 5C. Why are images of vimentin now provided not on micropatterns? The labelling of vimentin in siPeriplakin cells does not look appropriately controlled for by the other cell conditions. siPeriplakin is clearly at the edge of a colon, whereas this is not clear whether an appropriate region is labelled in the other conditions.

Significance

In the literature, there is a rich understanding of the molecular mechanisms of the cross-talk between cell-cell junctions, cell polarity complexes, and the organisation of the cytoskeleton. The authors are applauded for efforts to investigate whether there are common transcriptional downregulations of microtubule-related proteins that could potentially be key regulators of cellular polarisation. It is unfortunate that the work, as presented, is a series of modest observations, often the insight of which is overstated. Despite the analysis of plakins as a potential regulators of centrosome positioning between cell doublets, there is no mechanistic insight into a) how these plakins contribute to centrosome alignment asymmetry, or b) whether this is any way has an effect on true epithelial polarisation (beyond potential doublets on a micropattern). If significant development of mechanistic insight was added (requiring extensive additional experimentation, expected: 1-2 years of work), then the manuscript might be of interest to the cell biology community.

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Reply to the reviewers

Manuscript number: RC-2023-02247

Corresponding author(s): Heinz Jacobs

Description of the planned revisions

Reviewer #1

This manuscript by de Groot et al. is focused on investigating the role of the DNA damage tolerance (DDT) pathway for maintaining genomic stability in mammalian cells. All experiments are well designed and executed, and the conclusions are strongly supported by the experimental data. The authors generate a pair of congenic T cell lymphoma cell lines with either WT or PcnaK164R/-Rev1-/- genotype (the latter are referred to as double-mutant [DM] cells throughout the proposal). The DDT-deficient DM cells are surprisingly normal under standard growth conditions but show a strongly increased sensitivity to DNA damaging agents. Thus, the authors conclude that in the absence of exogenous stress a backup pathway exists to allow for normal growth, and a CRISPR screen reveals the CDC13/CTC1, STN1, and TEN1 (CST) complex as central for cell survival and cell cycle progression. Subsequent DNA fiber assays reveal that this survival relies on increased repriming of replication, and that exogenous stress overwhelms this backup pathway. Finally, the consequences of DDT deficiency were tested by whole genome sequencing of the WT and DM cells were exposed after a single round of UV stress. and subsequent whole genome sequencing was used to identify DNA alterations. The absence of DDT led to a striking increase in the number of deletions ranging in size from 0.4 to 4.0 kbp (called to a type 3 deletions). Importantly, such mutations are also present in many human tumor genomes and their level appears to be linked to alterations in DNA repair pathways (but no clear causal relationship was shown). The main take home message is that repriming after the lesion is the last resort when a replication forks stalls at a DNA lesion as this leads to the loss of 400-4000 bp of genome information at every such event. The DDT pathway serves to channel the responses towards less deleterious (or even error-free) replication outcomes.

The authors like to thank this reviewer for the very positive summary of our study.

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Major points:

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1) The authors rely on a genetically modifed cell line in which the Pcna and Rev1 genes are altered (the latter by CRISPR/Cas9 technology). To rule out that any additional inadvertent genetic changes occurred that may influence the phenotypes see here, it would be important to show for at least a subset of the experiments that ectopic re-expression of Rev1 and WT PCNA can rescue the survival defects seen here.

To rule out any inadvertent genetic changes, we opted for an isogenic system and used two independent clones which provided consistent phenotypes. Furthermore, the double mutant model has been often and independently published, showing very similar phenotypes as observed in this study (PMID: 36669105, PMID: 18498753, PMID: 37498746, PMID: 17105346). Additionally, in a p53-WT setting, Rev1-deficient and PCNA-K164R mutant mice are viable, develop normally, and are born at the expected mendelian frequencies, indicating a rescue in the absence of stress would not show an effect. In our published NAR paper (PMID: 35819193), we do not observe sensitivity of REV1-ko lymphomas (which is an isogenic SM clone of the DM and WT lymphoma), indicating that a rescue experiment would likely not help us much; and in the context of a single PCNA-K164R mutant, these become sensitive to genotoxic agents, in line with widely available literature. These aspects will be clarified by textual amendments.

2) It is unclear whether all experiments were conducted with a single clone of each genotype or if different clones were tested. This should be clarified.

A valid point, to exclude inter-clonal variations, two different isogenic clones were used for both DM and WT. This important aspect will be clarified in the results section.

3) The increase in the type 3 deletions in human cancers is very obvious, and as the authors clearly demonstrate DDT-deficiency results in the very same type 3 deletions. Although there is no data for this shown here, I'm assuming that a single deficiency in Rev1 would show a distinctly different mutation pattern. Given alterations of DNA repair/DNA damage tolerance gene mutations in the human tumors, it appears very unlikely to me that all tumors lack the DDT in its entirety. So why would the type 3 deletions then emerge? The authors should provide a clearer model of how this might work that could be tested in the future.

Indeed, the human tumors analyzed in the manuscript are unlikely to have DDT defects but do have the indicated alteration in other DNA repair genes. This led us to hypothesize that these type 3 deletions are not specific for DDT defects but more a general phenotype that results from replication stress, a hallmark of tumors and especially those suffering from specific DDR defects. We consider that future studies should address this important aspect in more detail and will extend the discussion section accordingly.

4) The authors only assess the genome alterations after a single dose of UV irradiation. Do the type 3 deletions also accumulate (albeit at a much lower rate) when these cells are grown for an extended period of time under normal conditions and do such cultures ultimately undergo senescence once too many deletions have been acquired?

We did culture these cells for an extended period of 5 months and compared the mutation profiles of pre-cultured and post cultured WT and DM cells. On the genomic level no major differences appeared between the pre- and post-cultured samples, indicating that these deletions likely do not accumulate easily over time. Furthermore, DM grow indefinitely and do not display any signs of senescence. We will clarify this relevant point and further extend on hypothesis that replication stress is likely to underlie the generation of type 3 deletions.

Minor points:

1) In the methods section the description of how the cell lines that are central to this work were generated is not clear. The authors start with a p53-/-PcnaK164R/loxP Rev1wt/wt background. Then the Rev1 was inactivated using CRISPR technology, but how the Pcna wt/- genotype in the WT was restored is unclear. It would be helpful to provide a schematic drawing of the gene targeting strategies as a supplementary figure.

An important point, we will add a schematic figure and legend to clarify the generation of the isogenic cell lines.

2) The authors should describe whether (and how many) independent clones of the DM (and may be WT) cell lines were tested and used in the experiments.

As stated above, two independent clones were studied to exclude inter-clonal variation, and this info will be added to the result and material and methods sections.

3) The approach by which the genome-wide mutation load was assessed for each genotype is not described in sufficient detail. Did the authors compare WT before and after UV exposure and DM before and after UV exposure separately or were just the genomes of WT and DM after UV exposure compared.

We extensively analyzed the data in both pre- and post-UVC exposures. Based on these analyses we chose to display our data as revealed in figure 4, where 4B indicates the deletions prior to UVC exposure, and figure 4C the deletions acquired upon UVC exposure. Additional analyses can be provided upon request.

Reviewer #2

The manuscript by de Groot and colleagues investigates the cellular and mutational phenotypes of mouse cells that are mutant for REV1 and also carry a PCNA-K164R mutation that prevents post-translational modifications at this residue. This double mutant (DM) likely removes all mechanisms for the recruitment of canonical translesion synthesis polymerases (Y family and pol zeta), thus the authors use it as a general DNA damage tolerance (DDT) deficient model. Using the cell line, they find signs of increased replication stress and a reliance on repriming. A whole genome CRISPR screen revealed a genetic dependence of the DM cells on the CST complex. Sequencing the genome of DM cells showed a specific increase in a distinct category of large deletions, which were also shown to be present in cancer genomes. While the study raises interesting points and contains much valuable data, I find major issues with both the study design and especially with the methodology, which appear to make it unsuitable for publication in its present form.

We like to thank this reviewer for the careful analyses of our data. Remarkably, while reviewer 1 praised the study design and methodology, this reviewer raised some concerns which feel are addressed and clarified appropriately as outlined below.

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Major points:

__ __Study design:

The paper focuses on the double mutant PCNAK164R/- REV1-/- cells throughout, without testing the single mutants. This is a major drawback. It is unclear whether such single mutant cell lines were available to the authors. A PCNA-K164R appears to have been published previously (Ref.46) but do they also have a REV1 mutant lymphoma in a tp53 muntant background? By comparing a double mutant to the wild type the authors miss the opportunity to assign phenotypes to either mutation. For example, large deletions very similar to those found here have been recently reported in human cells (Ref79, noted at the end of this manuscript). That paper shows that these are due to the loss of REV1 or REV3, and the concurrent loss of PCNA ubiquitination does not contribute to this phenotype (partially?).

We do have the WGS data of single mutants, but as this data did not show significant mutational differences, we felt like it would distract from the main story and decided to leave these data out. The major difference of our findings compared to Gyüre et al. (PMID: 37498746) is lack of a specific deletion phenotype in REV1 single mutant clones. With this independent study, we consider the overlap of our findings as most relevant.

A second example is the interesting observation that the DM cells rely on repriming even during unperturbed DNA replication. However, this could also potentially be the consequence of the inactivation of REV1. Again, single REV1 mutants should be assayed, and REV1-related literature discussed.

The role of REV1 in repriming and replication fidelity has been studied extensively in multiple systems (PMID: 31178121, PMID: 3797129, PMID: 31607544, PMID: 32330130, PMID: 32577513, PMID: 36669105, PMID: 34508659, PMID: 34624216, and others). Given the fact that this has been firmly elucidated, we decided to focus on the DM. However, we agree that this important aspect deserves to be discussed in detail and will add this to the discussion section.

Mutation detection methodology:

The analysis of small scale mutations shows some unexpected results. Not only is there no effect of the DDT mutations, there is also no effect of UV irradiation (Fig. S6E). Several papers have described in vitro experiments with UV treatment showing the clear mutation spectra that are also seen in cancers (SBS7). UV induces these spectra in mice even in vivo (PMID: 34210801 - though this paper used UVB). So it is difficult to believe that there would be no mutagenic effect in the cells used in this manuscript. Could there be an analysis problem instead?

The lack of UV signature has also come to our attention, but we clearly see an effect of the UV in the large deletions and cell viability, indicating these cells were exposed to UV. Additionally, we also provided the data to several independent bioinformaticians confirming our results. This excluded an experimental and analytical bias. Given these assurances, we theorized that the lack of a UV-mutation signature relates to the very low UVC dose these cells were exposed to. This is an experimental limitation caused by the marked UVC sensitivity of the DM cells. Of note, other published data employing DDT deficient systems also accumulated very low numbers of de novo mutations (PMID: 29323295, PMID: 37498746, PMID: 32330130). We agree that the surprising observation regarding the lack of a UVC signature deserves detailed explanation, which will be argued in the discussion section.

The mutagenesis experiment and the mutation calling are incompletely described. Precisely how many clones were sequenced? A table should be provided with such data, and sequencing data must be uploaded to an accessible database.

As mentioned for reviewer one, for the mutagenesis analyses two independent clones have been used for both genotypes, these provided very similar results. This relevant aspect will be indicated in the revised manuscript. The sequencing data have been uploaded and the link will be provided upon acceptance. Furthermore, we will extend the method section to clarify mutation calling.

Most importantly, how was the mutation calling done? Did the authors sequence an initial cell clone, to which the post-treatment clones could be compared? Without doing that, detected 'mutations' include many heterozygous SNPs which are differently called in different samples due to stochastic read count differences. Indeed, the mutation spectra in Fig. S6D and E look precisely like standard SNP spectra: flat in the C>T and T>C segment. If this is indeed the issue, mutation calling can be improved somewhat by filtering against mouse SNP databases, but the experiment cannot be fully rescued.

The mutation calling has been performed with the use of a standard (MM10, from a C57BL/6 mouse, the same background as our cell lines) mouse reference genome for all samples. We opted for this method as it is widely used (similar method as used by Gyüre et al., PMID: 37498746, but for human). Additionally, we used alternative filtering strategies to call mutations with high confidence, such as joint genotype calling. Importantly, we also used the untreated WT lymphoma as a reference, all of these methods provided very similar results that did not change the interpretation of our results. We agree that the original mouse genome sample would have served as the most ideal reference genome, however given the above outline of steps taken, we are confident in our conclusions. We will address these points in an extended discussion and method section.

The detection of large deletions is equally problematic. Fig. S5 suggests that the deletions are found in the same locations in the WT and the mutant cells. The probable reason for this is that the authors are finding the exact same deletions in both cell lines, which pre-existed even the making of the mutant cells, and are simply differences compared to whatever reference genome they are using! The DM appears to produce enough extra deletions to be detectable, but the real difference between the WT and the DM is likely much stronger than found here.

We thank this reviewer for pointing out this relevant comment. In accordance with the data gathered, we hypothesize that replication stress favors the formation of type 3 deletions. Consequently, our p53 deficient WT cell lines experience replication stress and thus will generate type 3 deletions. Using this cell line to generate the DM cell lines, we agree that these pre-existing type 3 deletions will be present in subsequent sequencing analyses. However, due to the enormous increase of replication in the DM additional type 3 deletions will accumulate. This aspect was the intended message of figure S5 A&B. We have also figures that only depict the differences between the type 3 deletions in WT and DM in predefined genomic regions (bins of 1 million bp).

Figure:

(A) Genome wide distribution of the difference in the number of type 3 deletions comparing DM minus WT in untreated conditions.

(B) Genome wide distribution of the difference in the number of type 3 deletions comparing DM minus WT after 0.4 J/m2 UV-C exposure.

(A)

Figure could not be uploaded in this portal.

(B)

Figure could not be uploaded in this portal.

We feel that generally, the issue that is put forward is that the use of a widely used standard reference would increase the background and thereby prevent the detection of small mutational changes. This however does not subtract from the mutational changes we did detect, leaving the core of the story and results unchanged. We agree that the effect size is likely to be stronger and we will address this aspect in the results and discussion section.

Some specific comments:

The CRISPR screen in the DM cells no doubt provided very valuable data, and CST is an interesting hit. The authors found that the STN1 gene could not be knocked out in the DM, but it could be when apoptosis was inhibited by Bcl2 overexpression. Unexpectedly, Bcl2 overexpression reduced the increased replication speed in the DM, thus interfering with the very effect the authors were trying to measure. Without understanding the mechanism of this effect, it is difficult to draw conclusions from this cell line. And again, the effect of Bcl2 and Stn1 should have also been assayed in a WT background as controls, not just in triple/quadruple mutant combinations.

Would single CST mutants also affect the cell cycle profile? The authors conclude that CST appears to have a role in tolerance of endogenous replication impediments, but without seeing the effect of the single mutant on the cell cycle they can only conclude about such impediments that are created in the absence of REV1 and PCNA-Ub. These may well be the breaks that result in the large deletions shown later.

Our prime interest in CST is only in the context of DDT. This means that we conclude that in the absence of DDT, CST seems to have a role in damage tolerance of endogenous replication impediments. We will highlight this better in the revised text to prevent confusion. Indeed, we initially speculated that CST would have a role in forming these deletions but due to lack of evidence we decided not to make this connection.

Additionally previous studies reported extensively on the role of CST in telomere maintenance (PMID: 28934486 and many others), DSB repair (PMID: 29768208), maintenance of genetically unstable regions (PMID: 34520548, PMID: 29481669) and its role in DDT (PMID: 35150303, PMID: 37590191).

The analysis of deletion size distribution in tumors is interesting and does appear to show that the 'type 3' deletions are a general phenomenon. However, the last point seems tautological: those tumors with a higher proportion of type 3 deletions have 'a sizeable increase of type 3 deletions'? (Fig. 5C). The fact that these deletions were also abundant in the WT cell line (Fig. 4B), where they are likely pre-existing genomic variations, suggests that such deletions can arise as part of spontaneous mutagenic processes even in normal cells. Their presence in all tumor types to similar degrees agrees with this.

Indeed, we agree that the process that leads to these types of deletions would be present in WT or normal cells. The increase in replication stress is likely underlying the formation of type 3 deletions. Their accumulation in the DDT deficient system is likely because this system generates replication stress similarly as in the presented human tumors, which in both cases appears to favor the formation of type 3 deletions.

Figure 5C is meant to give an overview of 5B using the density profiles similarly as shown in the previous figures. Additionally, this figure provides a direct comparison between the mouse and human density profiles of large deletions. Tumors with the cutoff of 25% of deletions that fall in type 3 range, have density profile similar to those of DM cells. We will alter the text accordingly to explain this relevant issue more clearly.

Minor comments:

__ __- The model organism for the DM cells (mouse) should be mentioned in the abstract.

Will be done.

• In the introduction, 4 modes of DDT are described including template switching without the formation of a post-replicative gap, but there is little evidence for this. Ref18 is the authors' own review, which cites further reviews.

We agree that this specific mode of DDT is less well documented, we will adjust the text to clarify this point and provide additional references.

• In the first Methods item, the plasmid used for transfection is not specified. "To obtain WT and PcnaK164R/-;Rev1-/- lymphoma cell lines, 10 x 106 lymphoma cells from a p53-KO, PcnaK164R/loxP mouse(46) were nucleofected."

The plasmid used was pX333. We will provide the info and reference.

• The y axis label of Figure 4F appears to be wrong (frequency vs. percentage)

We will change this legend to percentage.

Reviewer #3

The manuscript by De Groot et al investigates the impact of the PCNA(K164R)-REV1 double inactivation on genome integrity in lymphoma cells. The group had previously demonstrated that the double mutant is lethal in mice (papers in PNAS and NAR) but here, in lymphoma cells, additional mechanistic work could be performed. Chiefly, they were able to conduct a CRISPR screen to investigate backup mechanisms in these double mutant lymphoma cells and they identified a specific complex (CST). Mutating one of the CST complex proteins within double mutant cells led to lethality that was rescued by Bcl2 overexpression, allowing for further mechanistic studies. WGS on such cells identified specific types of structural variants that would normally kill cells (mostly large deletions). Finally, they identify similar type deletions in databases of human tumours, with specific preferences with regard to treatment modality (more deletions with chemo, immunotherapy and hormonal therapy, and fewer in tumours treated with tamoxifen, imatinib and some other small molecule inhibitors).

The authors like to thank the reviewer for the time invested and the appreciation of our novel insights.

Please find below our responses to the remaining specific comments.

Specific comments:

1) can the authors comment on the physiological relevance of the screen, considering that the double mutation is lethal in normal tissues?

The screen was performed to understand how cancer cells can survive in a DDT deficient setting. This increases our understanding of the general function of DDT and identify alternative pathways that enable cancerous as well as normal cells to cope with DNA damage. Furthermore, tumors can have defects in the DDT system, knowledge on DDT function may help to target these tumors with specific inhibitors and chemotherapeutics. A relevant aspect, that we will elaborate on in the revised discussion.

2) can the authors suggest a mechanism regarding how CST would work to maintain the viability of the double knockout lymphoma cells?

An important point, our insights gathered so far favor a model where the CST prevents the formation of single stranded DNA gaps. As the double mutant DDT deficient cells already accumulate a high number of post-replicative gaps, the lack of CST complex further increases those, leading to genomic instability and eventually cell death. To clarify our model, we will extend our discussion section.

3) it is implied that STN1 deletion would only kill double mutant lymphoma cells but is this actually the case? (a similar deletion in wildtype and single mutant cells is a necessary control).

The role of CST, and its ablation, has been extensively studied by many others. Our main interest in CST is in the context of DDT and how CST maintains cells in a DDT deficient setting. Because the single DDT mutants have been studied in detail, we here focused on the role of CST in our double mutant DDT deficient setting. This setting enabled us to identify CST as a potential novel back up mechanisms to cope with replication impediments.

4) I really liked the data from human tumour databases (figure 5) but are the deletions there correlated with the same DDT profiles as investigated here?

The human tumors discussed in the manuscript do not contain similar specific DDT defects as in the lymphomas. However, we do see that human tumors with varied DDR defects have an increase in these deletions. This led us to speculate that the type 3 deletions arise due to general replication stress, present in both the human tumors and the DM lymphomas.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by De Groot et al investigates the impact of the PCNA(K164R)-REV1 double inactivation on genome integrity in lymphoma cells. The group had previously demonstrated that the double mutant is lethal in mice (papers in PNAS and NAR) but here, in lymphoma cells, additional mechanistic work could be performed. Chiefly, they were able to conduct a CRISPR screen to investidate backup mechanisms in these double mutant lymphoma cells and they identified a specific complex (CST). Mutating one of the CST complex proteins within double mutant cells led to lethality that was rescued by Bcl2 overexpression, allowing for futher mechanistic studies. WGS on such cells identified specific types of structural variants that would normally kill cells (mostly large deletions). Finally, they identify similar type deletions in databases of human tumours, with specific preferences with regard to treatment modality (more deletions with chemo, immunotherapy and hormonal therapy, and fewer in tumours treated with tamoxifen, imatinib and some other small molecule inhibitors).

Specific comments:

1. can the authors comment on the physiological relevance of the screen, considering that the double mutation is lethal in normal tissues?
2. can the authors suggest a mechanism regarding how CST would work to maintain the viability of the double knockout lymphoma cells?
3. it is implied that STN1 deletion would only kill double mutant lymphoma cells but is this actually the case? (a similar deletion in wildtype and single mutant cells is a necessary control).
4. I really liked the data from human tumour databases (figure 5) but are the deletions there correlated with the same DDT profiles as investigated here?

Referees cross-commenting

Nice to see that most of the comments are aligned.

Significance

Reasonable significance, potentially ablated by the (lack of) physiological relevance of the screen (see comments above).

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Referee #2

Evidence, reproducibility and clarity

The manuscript by de Groot and colleagues investigates the cellular and mutational phenotypes of mouse cells that are mutant for REV1 and also carry a PCNA-K164R mutation that prevents post-translational modifications at this residue. This double mutant (DM) likely removes all mechanisms for the recruitment of canonical translesion synthesis polymerases (Y family and pol zeta), thus the authors use it as a general DNA damage tolerance (DDT) deficient model. Using the cell line, they find signs of increased replication stress and a reliance on repriming. A whole genome CRISPR screen revealed a genetic dependence of the DM cells on the CST complex. Sequencing the genome of DM cells showed a specific increase in a distinct category of large deletions, which were also shown to be present in cancer genomes. While the study raises interesting points and contains much valuable data, I find major issues with both the study design and especially with the methodology, which appear to make it unsuitable for publication in its present form.

Study design:

The paper focuses on the double mutant PCNAK164R/- REV1-/- cells throughout, without testing the single mutants. This is a major drawback. It is unclear whether such single mutant cell lines were available to the authors. A PCNA-K164R appears to have been published previously (Ref.46) but do they also have a REV1 mutant lymphoma in a tp53 muntant background? By comparing a double mutant to the wild type the authors miss the opportunity to assign phenotypes to either mutation. For example, large deletions very similar to those found here have been recently reported in human cells (Ref79, noted at the end of this manuscript). That paper shows that these are due to the loss of REV1 or REV3, and the concurrent loss of PCNA ubiquitination does not contribute to this phenotype. A second example is the interesting observation that the DM cells rely on repriming even during unperturbed DNA replication. However, this could also potentially be the consequence of the inactivation of REV1. Again, single REV1 mutants should be assayed, and REV1-related literature discussed.

Mutation detection methodology:

The analysis of small scale mutations shows some unexpected results. Not only is there no effect of the DDT mutations, there is also no effect of UV irradiation (Fig. S6E). Several papers have described in vitro experiments with UV treatment showing the clear mutation spectra that are also seen in cancers (SBS7). UV induces these spectra in mice even in vivo (PMID: 34210801 - though this paper used UVB). So it is difficult to believe that there would be no mutagenic effect in the cells used in this manuscript. Could there be an analysis problem instead? The mutagenesis experiment and the mutation calling are incompletely described. Precisely how many clones were sequenced? A table should be provided with such data, and sequencing data must be uploaded to an accessible database. Most importantly, how was the mutation calling done? Did the authors sequence an initial cell clone, to which the post-treatment clones could be compared? Without doing that, detected 'mutations' include many heterozygous SNPs which are differently called in different samples due to stochastic read count differences. Indeed, the mutation spectra in Fig. S6D and E look precisely like standard SNP spectra: flat in the C>T and T>C segment. If this is indeed the issue, mutation calling can be improved somewhat by filtering against mouse SNP databases, but the experiment cannot be fully rescued. The detection of large deletions is equally problematic. Fig. S5 suggests that the deletions are found in the same locations in the WT and the mutant cells. The probable reason for this is that the authors are finding the exact same deletions in both cell lines, which pre-existed even the making of the mutant cells, and are simply differences compared to whatever reference genome they are using! The DM appears to produce enough extra deletions to be detectable, but the real difference between the WT and the DM is likely much stronger than found here.

Some specific comments:

The CRISPR screen in the DM cells no doubt provided very valuable data, and CST is an interesting hit. The authors found that the STN1 gene could not be knocked out in the DM, but it could be when apoptosis was inhibited by Bcl2 overexpression. Unexpectedly, Bcl2 overexpression reduced the increased replication speed in the DM, thus interfering with the very effect the authors were trying to measure. Without understanding the mechanism of this effect, it is difficult to draw conclusions from this cell line. And again, the effect of Bcl2 and Stn1 should have also been assayed in a WT background as controls, not just in triple/quadruple mutant combinations. Would single CST mutants also affect the cell cycle profile? The authors conclude that CST appears to have a role in tolerance of endogenous replication impediments, but without seeing the effect of the single mutant on the cell cycle they can only conclude about such impediments that are created in the absence of REV1 and PCNA-Ub. These may well be the breaks that result in the large deletions shown later.

The analysis of deletion size distribution in tumours is interesting, and does appear to show that the 'type 3' deletions are a general phenomenon. However, the last point seem tautological: those tumours with a higher proportion of type 3 deletions have 'a sizeable increase of type 3 deletions'? (Fig. 5C). The fact that these deletions were also abundant in the WT cell line (Fig. 4B), where they are likely pre-existing genomic variations, suggests that such deletions can arise as part of spontaneous mutagenic processes even in normal cells. Their presence in all tumour types to similar degrees agrees with this.

Minor comments:

• The model organism for the DM cells (mouse) should be mentioned in the abstract.
• In the introduction, 4 modes of DDT are described including template switching without the formation of a post-replicative gap, but there is little evidence for this. Ref18 is the authors' own review, which cites further reviews.
• In the first Methods item, the plasmid used for transfection is not specified. "To obtain WT and PcnaK164R/-;Rev1-/- lymphoma cell lines, 10 x 106 lymphoma cells from a p53-KO, PcnaK164R/loxP mouse(46) were nucleofected."
• The y axis label of Figure 4F appears to be wrong (frequency vs. percentage)

Referees cross-commenting

I agree with comments by the other reviewers.

Significance

General assessment:

My assessment is provided above, the manuscript is not suitable for publication in its present form. If I am correct about the faults of the experimental design, it would be advisable to repeat the entire mutagenesis experiment starting from newly isolated and sequenced single cell clones. Ideally, single mutants should also be included. Even if this is done, the novelty of the expected results is unfortunately compromised by the very similar recent data published from human cell lines. Alternatively, the mutation data could be left out, and the CST-based data could be expanded with more controls and hopefully more mechanistic insight.

Advance:

The CST-dependence of PCNAK164R/- REV1-/- cells and the general presence of 400-4000 bp deletions in tumours are both significant findings, but limited mechanistic insight is provided.

Audience:

DNA repair field.

I have expertise in the field of DNA repair and mutagenesis.

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Referee #1

Evidence, reproducibility and clarity

This manuscript by de Groot et al. is focused on investigating the role of the DNA damage tolerance (DDT) pathway for maintaining genomic stability in mammalian cells. All experiments are well designed and executed, and the conclusions are strongly supported by the experimental data. The authors generate a pair of congenic T cell lymphoma cell lines with either WT or PcnaK164R/-Rev1-/- genotype (the latter are referred to as double-mutant [DM] cells throughout the proposal). The DDT-deficient DM cells are surprisingly normal under standard growth conditions but show a strongly increased sensitivity to DNA damaging agents. Thus the authors conclude that in the absence of exogenous stress a backup pathway exists to allow for normal growth, and a CRISPR screen reveals the CDC13/CTC1, STN1, and TEN1 (CST) complex as central for cell survival and cell cycle progression. Subsequent DNA fiber assays reveal that this survival relies on increased repriming of replication, and that exogenous stress overwhelms this backup pathway. Finally, the consequences of DDT deficiency were tested by whole genome sequencing of the WT and DM cells were exposed after a single round of UV stress. and subsequent whole genome sequencing was used to identify DNA alterations. The absence of DDT led to a striking increase in the number of deletions ranging in size from 0.4 to 4.0 kbp (called to a type 3 deletions). Importantly, such mutations are also present in many human tumor genomes and their level appears to be linked to alterations in DNA repair pathways (but no clear causal relationship was shown). The main take home message is that repriming after the lesion is the last resort when a replication forks stalls at a DNA lesion as this leads to the loss of 400-4000 bp of genome information at every such event. The DDT pathway serves to channel the responses towards less deleterious (or even error-free) replication outcomes.

Major points:

1. The authors rely on a genetically modifed cell line in which the Pcna and Rev1 genes are altered (the latter by CRISPR/Cas9 technology). To rule out that any additional inadvertent genetic changes occurred that may influence the phenotypes see here, it would be important to show for at least a subset of the experiments that ectopic re-expression of Rev1 and WT PCNA can rescue the survival defects seen here.
2. It is unclear whether all experiments were conducted with a single clone of each genotype or if different clones were tested. This should be clarified.
3. The increase in the type 3 deletions in human cancers is very obvious, and as the authors clearly demonstrate DDT-deficiency results in the very same type 3 deletions. Although there is no data for this shown here, I'm assuming that a single deficiency in Rev1 would show a distinctly different mutation pattern. Given alterations of DNA repair/DNA damage tolerance gene mutations in the human tumors, it appears very unlikely to me that all tumors lack the DDT in its entirety. So why would the type 3 deletions then emerge? The authors should provide a clearer model of how this might work that could be tested in the future.
4. The authors only assess the genome alterations after a single dose of UV irradiation. Do the type 3 deletions also accumulate (albeit at a much lower rate) when these cells are grown for an extended period of time under normal conditions and do such cultures ultimately undergo senescence once too many deletions have been acquired?

Minor points:

1. In the methods section the description of how the cell lines that are central to this work were generated is not clear. The authors start with a p53-/-PcnaK164R/loxP Rev1wt/wt background. Then the Rev1 was inactivated using CRISPR technology, but how the Pcnawt/- genotype in the WT was restored is unclear. It would be helpful to provide a schematic drawing of the gene targeting strategies as a supplementary figure.
2. The authors should describe whether (and how many) independent clones of the DM (and may be WT) cell lines were tested and used in the experiments.
3. The approach by which the genome-wide mutation load was assessed for each genotype is not described in sufficient detail. Did the authors compare WT before and after UV exposure and DM before and after UV exposure separately or were just the genomes of WT and DM after UV exposure compared.

Referees cross-commenting

It appears that our comments are mostly overlapping.

Significance

This manuscript is a continuation of the very systematic work by the Jacobs lab to dissect the molecular mechanisms by which DDT factors act and the role of DDT in DNA damage responses. Here the authors demonstrate that in complete absence of DDT factors is not lethal, but reveals the priming of replication as the last resort response to avoid cell death. The analyses of the human tumor genome sequences suggest that dysfunctional DDT response are likely intimately involved in the generation of a distinct set of genetic lesions found in many tumors. What remains unclear is how the DDT pathway is inactivated in tumors as there is no consistent pattern of DDT factors being mutated. Overall this manuscript is of broad general interest far beyond the DNA repair community. The novelty of this manuscript is how reduced by the fact that another group published similar data in the human RPE cells 2023 (see reference 79 as acknowledged by the authors), but observing the same phenomena in two distinct system provides additional weight to these discoveries.<br /> Expertise: My expertise is in the gene diversification processes that assemble and alter TCR and immunoglobulin genes. They involve a broad range of DNA repair factors and DDT plays a unique role in somatic hypermutation that allows for the generation of high affinity antibodies.

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Reply to the reviewers

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

Summary: In this work, Kant and co-workers describe a two drugs regimen for therapeutics treatment of SARS-CoV-2 infection. SARS-CoV-2 infection of cells is dependent on the cleavage of the spike S protein by cellular proteases that prime S allowing the envelop protein to fuse of host membrane during entry and delivery of the viral genome to the target cell. The most important cellular protease is TMPRSS2 located at the surface of the cell. However, in cells with low TMPRSS2 levels, Cathepsins, located in endosomes have been shown to be able to also prime S. The therapeutic strategy of the authors relies on the combined usage of an inhibitor of TMPRSS2 (nafamostat) together with a compound that impairs endosomal maturation (apilimod) which is a key step for the activation of cathepsin. The rationale is that a dual regimen would be more effective to inhibit SARS-COV-2 infection. Using cell lines and a combination of SARS-CoV2 infection and pseudotyped VSV particles (VSV virus where the glycoprotein has been replaced by the SARS-CoV-2 spike proteins), the authors could show that a two-drug regimen was more efficient in preventing SARS-CoV-2 infection compared to single drug regimen. The authors next employed a mouse model of SARS-CoV-2 infection and similarly could show that bi-therapy was more efficient in preventing infection. Importantly, the authors describe a new formulation of the drugs that improve stability of the compounds and shelve life which could be of great benefit with respect to storage needs in therapeutic setting of the population.

While the reviewer thinks the work is potentially very relevant, some of the conclusions are not fully supported by the data and additional experiments/quantifications should be performed to improve rigor and fully support the author conclusions.

Major comments:

• Throughout the paper, statistical analysis of the results should be performed to support the conclusion of the authors. Currently many experiments do not have statistical analysis and P values or statical significance are missing in most of the figures: Figure 1B, 1D, 4A, 5B, and S2. RESPONSE: As requested by the reviewer, the results of the statistical analysis of the differences are now reported for Figures 1B, 1D, 4A, 5B, and S2. There is no change in our conclusions as first reported in the original manuscript.

• Quantification of the various pathology observed in mice should be quantified and scored. In the current version, the authors provided a supplementary table describing the pathology observed in individual mice upon SARS-CoV-2 infection. Adapted scoring of the different pathologies should be performed to obtain a statistical view of the pathology induced by SARS-CoV-2 and how this is prevented by the mono and bi-therapy approaches. RESPONSE: The mouse model employed in the present study, i.e. SARS-CoV-2 Beta infection in BALB/c mice, is characterised by a limited and short-lived viral infection of the lungs and rather subtle pathological changes, as described in detail in our previous publication (Kant et al., 2021. Viruses).

We chose this model because it better mimics the typical (short-lived) respiratory infection observed in human patients than the K18-hACE2 model where infection is detected in nasal mucosa and lung parenchyma, generally sparing the respiratory epithelium, but also spreads to the brain (Seehusen et al., Viruses, 2022; De Neck et al., Viruses, 2023).

In our model, infection of the lungs (i.e., alveoli) occurs strictly in association with infection of the airways, including the tracheal, bronchial, and bronchiolar epithelium, like the in hamster model. Pulmonary infection is, however, short-lived and wanes off around day 4. The histopathological changes, i.e. degenerative changes, and an inflammatory response, are at best mild in the untreated mice and not observed at all in successfully treated mice. (as summarized for each individual animal in Supplementary Table 2). . For these reasons, this information cannot be quantified by morphometry (which would be the most objective, hence best approach) or scored (a more subjective approach that would only be valid with distinct quantitative differences).

Nevertheless, and in agreement with the reviewer that a quantitative approach is useful where possible we provide results from morphometry and to confirm the reduction in the degree of tissue damage (i.e., the extent of apoptotic death of infected respiratory epithelial cells; see comment below).

• Additionally, table 1, is very difficult to read as mice are classified in 3 experiments but this does not match with the individual figures, making it very hard to look for the phenotypes. Is it an order issue within the table or are murine infection experiments performed in the order described in table 1? In this case, can the data be compared between the experiments as some conditions belong to experiment 2 and other to experiment 3? Given the low number of mice, do the experiments have statistical power? RESPONSE: We agree with the reviewer’s assessment of the figure and have therefore modified the graphs in Figure 2 B, to specifically relate experiments and data, by using circles for Experiment set 1 and squares for Experiment set 2.

We can confirm the reported results have statistical power, particularly important given the constrain due to the low number of animals we were limited to use. As noted in the figure legends, that now includes the results from the statistical analysis, each of the three experiments included at least three control infected mice treated with vehicle. The infection levels in all the control vehicle treated infected mice are very similar in all three experiments.

• To show that treatment of mice at 3 or 6 hpi indeed reduce the number of clv-capsase3 positive cells, the authors should perform a complete quantification and not limit their analysis to one representative tissue section from one animal. RESPONSE: Following the reviewer’s recommendation, we have now taken a quantitative approach in addition to illustrating the difference in cleaved caspase-3 expression. We have kept the images that illustrate the effect in tissue sections (Figure 4C).

Briefly, we compared the extent of viral NP and cleaved caspase-3 expression between lungs of vehicle treated mice and mice treated with the drugs from 6 hpi onwards (3 mice per condition), using morphometry. Indeed, there was no significant difference in the extent of viral antigen NP expression in the lungs of the two groups of mice (Figure 4 B and C), which supports the PCR results representing viral RNA levels (Fig. Figure 4 A). However, there was a significant difference in the extent of cleaved caspase-3 expression in the consecutive sections. The results are shown in the new Figure 4D.

• the authors insist on the new formulation that improves drug stability. To make this statement, this will need to be actively tested both in cell culture and in animal models: currently, the authors test the drugs stored 3 months at 25c or -20c and show that they remain active, but in this experiment freshly made drug was not directly tested in parallel. RESPONSE: As requested by the reviewer, we have extended our tests, and confirm our original view that the new formulation improves drug stability. Now shown in revised Figure 1C and D, we found equivalent inhibition in the cell infection assay using freshly made drugs and drugs stored at room temperature for 2 months.

• Additionally, to make such a statement, different concentration of the drugs should be tested to calculate a IC50 for freshly prepared drug and stored drugs (as the current concentration tested might be at saturating concentration). RESPONSE: As requested by the reviewer, we have determined the IC50 for infection in cells of the drugs freshly prepared or stored. As reported in the revised Figure 1D, there were no differences detected.

• Finally, the mouse experiments are performed with freshly made compounds and if the authors want to highlight the new formulation and increased stability, experiments in mice should be performed also with stored compounds. RESPONSE: We respectfully disagree with the reviewer on the need to perform additional in vivo experiments. We find no differences in the IC50 antiviral activity of the drugs prepared with our formulation and tested with cells in culture, whether fresh or kept for up to 2 months at room temperature. Given these observations, we feel that we cannot justify further animal experiments, neither ethically nor financially, using the same drugs with the same ab initio antiviral activity.

• Alternatively, statement on drug stability should be removed or strongly tuned down from text. RESPONSE: We believe that the updated information included in the revised manuscript showing no difference in the IC50s of the compounds freshly prepared and stored at room temperature fully supports our original statement.

• Statistical analysis on figure 2b should be done between Nafamostat alone and dual treatment to show that both drugs are cooperative in term of antiviral activities RESPONSE: We have carried the requested statistical analysis (Figure 2 B and C) and confirm that dual treatment is not only cooperative, but it also shows synergy, as we originally showed in our published work (Kreutzberger et al., Journal of Virology, 2021).

• The authors state "A quantitative assessment of the in vivo synergy is shown here by the enhanced decrease of viral RNA in lungs of mice treated with both drugs at very low concentrations (Figure 2 B, compare using 2 mg/Kg apilimod dimesylate and 4 mg/Kg nafamostat mesylate alone, and in combination)." I guess, the authors want to comment on the fact that 0.2 mg/kg of apilimod and 0.4 mg/kg of nafamostat are as potent as 2 and 4 mg/kg. is that correct? If YES, to make this statement, bi therapy should be compared to mono therapy at the same concentration. RESPONSE: We apologise for not being clearer in the way we presented the information in our original version of the manuscript.

Briefly, we compared the effect of high and low bi-therapy doses to the effect of Apilimod or Nafamostat used as single drugs at the highest concentrations. When administered alone, high dose Apilimod did not reduce infection. Nafamostat alone, even at 4 mg/Kg, decreases but does not completely block infection. When combined, even at low doses, the two drugs have a stronger antiviral effect than Nafamostat alone (and of course Apilimod, which was ineffective). Importantly, if the combined effect of the two drugs was merely additive, i.e. the arithmetic sum of the single effects, the addition of Apilimod, which alone has no in vivo antiviral activity, would not have improved the effect of Nafamostat. Instead, even at 10 times lower doses, the bi therapy significantly outperformed the single drug Nafamostat. Thus, the effect is synergistic (i.e. the effect of combined drugs is stronger than the mere sum of effects of each single drug).

• when drugs are injected after infection (Fig 4), the drugs are not active. In fact, unless the reviewer mis-understood the plot, the mouse are even more infected compared to vehicle. The authors wrote that both regimes (3 and 6hpi) are equally less effective compared to drug administered during infection. The authors should write that both regimes are equally non protective. RESPONSE: We thank the reviewer for pointing out this imprecision. The modified text now reads “Both regimes, compared to drug administration at the time of virus inoculation, were equally ineffective in reducing the viral RNA load and NP expression in lungs as determined at 48 h.p.i. (Figure 4A, B).” (Line 236-238).

• If drugs are not active after infection, does this approach really represent a therapeutic solution. The authors suggest that it does by limiting pathologies, but this needs to be better quantified (see comment above). RESPONSE: Our results suggest that application of the drugs post infection reduced the cytopathic effect of the virus in the respiratory epithelium in the lungs, reflected by a reduced extent of apoptotic cell death in association with infection. The finding is supported by quantitative morphometric analysis as shown in the new Figure 4D (see also comment above).

• In the rebound experiment: unless the reviewer misunderstood, it appears that no conclusion can be driven from this experiment. Q-PCR data for vehicle animal a 4dpi show no sign of infection, so the experiment is not really interpretable since control animals are no longer positive. The authors suggest that there is less pathologies but this needs to be better quantified (see comment above). RESPONSE: We have tried to better word the rationale and interpretations of this experiment in the text. Following our drug treatments, viral antigen is still present in epithelial cells within the nasal mucosa, we also surmised that a small number of intact virions could have remained attached to the epithelial cells, trapped within their endosomes, or still within the environment surrounding the cells, any of them capable of triggering infection after removal of the drugs. Thus, the rationale behind the rebound experiment was to ask whether such remaining potentially intact virions could lead to a full reinfection of the lung two days after the treatment was stopped - which we found did not.

We found that the virus did not regain full infectivity once the drug treatment was interrupted, resulting in undetectable lung PCR signal and very limited, sporadic antigen signal in the lung tissue.

Minor comments:

• I__t will make reading easier if the authors always mentioned which drugs inhibit what. For example: addition of the TMPRSS2 inhibitor nafamostat etc.... or addition of apilimod to block cathepsins activities..... __RESPONSE: Done

• Figure 1: make a comment in the text that cells with low TMPRSS2 are more sensitive to the cathepsin inhibitor apilimod and vice versa, cells with high TMPRSS2 are more sensitive to nafamostat. This is expected and it could be highlighted. RESPONSE: Done

• Figure 2B: how are the data normalized? should not RdRp, E and SubE all have a mean at 100% for the vehicle? RESPONSE: Done. Data are now normalized to the mean of RdRp measurements (which is indicated as 100%).

• Line 211: something is missing here "when (Fig 2...) RESPONSE: Corrected

• Line 221 should figure 4c RESPONSE: Corrected

• Figure legends should only contain the details of the experimental design but should not contain description and interpretation of data. This is very minor and maybe a question of taste. __RESPONSE: __ Our figure legends are descriptive for some results and are in accordance with the style of PLOS Pathogens, the journal we are aiming this study.

Editorial note:

Referees cross-commenting: The other reviewers have highlighted the same limitations concerning the lack of quantifications of the immunochemistry and also the lack of robust statistical analyses. This should be highlighted to the authors as it appears to be the minimum to do prior publication. This should not take too much time as the data are in principle already available

Reviewer #1 (Significance):

The work by Kant and co-workers is potentially very significant but some limitations (as highlighted above) impair the impact of the work in his current version. The approach employing a two-drug regimen to combat SARS-COV-2 infection by targeting both TMPRSS2 and cathepsin activities is not new and was described before by the authors themselves. Employing this approach in an animal model is new and the new formulation improving drug stability and facilitating storage could be a game changer in therapeutic setting of patients. As such, this work could be highly significant and of broad interest. However, additional experiments and clarifications are needs to elevate this work to high impact standards. The reviewer believes that the requested experiments are easily achievable by the research teams of this project and think that the project will ultimately have a strong impact in the field.

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Reviewer #2 (Evidence, reproducibility and clarity):

In this paper, the authors tested the antiviral activity of a combination of compounds by intranasal instillation in a mouse model of SARS-CoV-2. The two compounds used are PIKfyve Kinase inhibitor apilimod dimesylate, which inhibits endosomal maturation, and TMPRSS2 protease inhibitor nafamostat mesylate. The authors have previously shown that a combination of these two inhibitors acts synergistically to prevent entry and infection of SARS-CoV-2 in cell culture. Here, they further investigated the anti-SARS-CoV-2 activity of their combination of compounds by in vivo testing. They used Balb/c mice intranasally inoculated with the Beta variant of SARS-CoV-2. Their data show that concurrent administration of the combo together with the virus prevented lung infection without blocking nasal replication. Delayed administration of the compounds did not reduce replication in the lungs. The only effect was a decrease in bronchiolar cell death. Furthermore, they also tested the stability of the combo at room temperature and their data indicate that these compounds can be kept at room temperature for at least 3 months without losing antiviral activity, at least when resuspended in water. These data are potentially interesting, but they need to be consolidated by additional experiments.

Major comments:

• The authors only present immunohistochemistry to investigate viral replication in the nose. A quantitative analysis of replication would allow for better conclusions concerning viral replication in this organ. RESPONSE: We appreciate the reviewer’s comment and the wish to see viral antigen expression quantified in the nasal mucosa. As described below, however, practicalities associated with sample preparation prevented us from performing morphometric analysis. The complementary quantification of viral replication requires viral RNA by PCR. Unfortunately, we had not planned this aspect of the study and therefore did not collect the required fresh samples from nasal turbinates required for this analysis. Although interesting to investigate, we feel this is not vital for reaching the interpretation and conclusions derived from the current study. We thereby don’t think that this would be sufficient reason to undertake another round of infections, particularly taking into consideration that it would require sacrificing another significant number of animals.

We could extend our morphometric analysis used in the lung and adapt it to the nasal mucosa. However, we are of the opinion that this would not provide trustworthy results. The main reason for this limitation is due to a problem that occurs during decalcification and paraffin embedding of the heads, which results in large variations in the area of the nasal mucosa as well as the olfactory epithelium in each section in different animals (Figure 3C provides some evidence of this).

Briefly, we cut the entire heads longitudinally in the midline with a diamond saw and then gently decalcify the two halves of the head. This is followed by paraffin embedding. At some point during the process some of the thin and soft bits of nasal mucosa can become twisted and distorted, moving away from the cut surface exposed to the microtome blade. Therefore, the paraffin sections (appr. 3 µm thick) will in their majority not comprise full sections of the nasal mucosa. An objective comparative quantification of the extent of NP expression in the nasal mucosa would require (nearly) the entire mucosa to be assessed.

• Complementary investigation on a potential anti-inflammatory effect of the drugs would also be welcome. Furthermore, it is surprising that the authors did not report potential weight changes. RESPONSE: Our mouse model, i.e. SARS-CoV-2 Beta infection in BALB/C mice, is characterised by the limited and short-lived viral infection of the lungs, rather subtle pathological changes and a limited inflammatory response strictly associated with the presence of viral antigens, as we previously described (Kant et al., 2021. Viruses). Hence, other animal models (for example the hamster model) would be more appropriate. Though potentially interesting, such investigations are beyond the current scope of our studies.

In our study, the animal weight did not change during infection, in agreement with our earlier published work with the same animal model (Kant et al., 2021. Viruses). These data is now included in this manuscript.

• It would have been interesting to complete the experiments with a demonstration that the compounds block viral transmission. RESPONSE: While it would be interesting to see whether the combined drugs also block viral transmission, such an experiment would require the use of a different animal model (possibly hamsters), an endeavour that is beyond the scope of our study. In our experience BALB/C mice infected with SARS-CoV-2 Beta variant do not transmit the virus. We have co-housed naïve BALB/C mice for 4 days with BALB/C mice intranasally challenged with 6 x 10^4 PFU SARS-CoV-2 Beta and have no evidence of virus transmission to the naïve mice (unpublished results). Similar results with C57BL/6 WT mice were obtained by Pan et al., Signal Transduction and Targeted Therapy, 2021).

Minor comments:

• The second paragraph of the introduction is not clear. It needs to be re-written. Furthermore, there is no evidence that Calu3 cells do not express cathepsins. RESPONSE: We have clarified this section of the introduction as follows:

“It has been shown previously that SARS-CoV-2 infection can be blocked by serine protease inhibitors such as nafamostat mesylate in cells that express high levels of TMPRSS2 but very low or undetectable levels of cathepsin B/L (e.g. Calu-3 cells)5-7. In cells that instead express cathepsins but not TMPRSS2 (e.g. VeroE6 or A549 cells), infection depends on the delivery of endocytosed viruses to endo/lysosomes, a process that can be efficiently inhibited by drugs that interfere with endosome maturation and acidification such as Bafilomycin A1, chloroquine or ammonium chloride”.

• Figure 4C: Is there any explanation for the lack of apoptosis? The authors should at least provide some hypotheses. Furthermore, this figure is quoted as Figure 4B in the text instead of Figure 4C. RESPONSE: For the revised manuscript, we have quantified the extent of apoptosis by a morphometric analysis of cleaved caspase-3 expression in the lung sections (now provided in new Figure 4C).

We presently do not have an explanation for the reduction in the cytopathic effect of the virus, particularly in respiratory epithelial cells. This is an area of research we plan to continue investigating in future. We have commented on this in the Discussion session of the revised manuscript (Line 301-307).

• Line 199: The authors claim that the effect of their combo is synergistic. However, this cannot be clearly concluded without appropriate additional experiments where they vary the concentration of the compounds. RESPONSE: The work we report here with mice is a follow up of our earlier work demonstrating the antiviral synergy of nafamostat and apilimod with cells in culture (Kreutzberger et al., Journal of virology, 2021). See comments to Reviewer 1.

• Line 211: The sentence is incomplete RESPONSE: Fixed.

• The lettering in the panels needs to be doublechecked. RESPONSE: Done.

Reviewer #2 (Significance):

__General assessment: __Finding new antiviral against SARS-CoV-2 remains a priority to fight against COVID-19. The validation of a combination of two molecules showing a partial antiviral activity in vivo is therefore of interest. However, this combo does not block viral replication in the nose and is inefficient when the treatment is added after infection, limiting the use of these molecules to prevent people in contact with COVID-19 patient of being infected. However, the authors should demonstrate that their molecules block viral transmission.

__ Advance:__ The number of antivirals used in the clinics to treat COVID-19 patients remains extremely limited. Increasing the number of drugs available is still sorely needed. Audience: This paper potentially of large interest since the general population has been well informed of and/or have experienced COVID-19. Therefore, it is of interest beyond the virology and infectiology fields.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary: In manuscript reference RC-2023-02113, the authors addressed the impact of inhibitors of cell host factors as therapeutics against SARS-CoV-2 infection. They tested the combined inhibition of the enzymatic activities of the endosomal PIKfyve phosphoinositide kinase and the serine protease TMPRSS2, known as essential to meditate viral entry pathways: Conclusion: They showed a reduction, as assessed in vitro experiment (cell line) and in lung infection in mice intranasally- infected with SARS-CoV-2 beta. Moreover, the reduced viral infection is, as expected, associated to lower cell damage.

Reviewer #3 (Significance (Required)):

Positive points:

• The topic is of interest.

• Robust impact of the treatment although kinetic analysis post infection/symptoms are missing. Limitations:

• Such a robust level of infection in this model (female BALB/c mice) is surprising, owing that the ACE is not the appropriate homologue. RESPONSE: We respectfully disagree with this concern. The BALB/c strain employed in the current study can be infected by the natural Beta variant, with mutations in the viral spike that allow it to bind to the murine ACE2 receptor and hence can efficiently infect the mice, as we previously described (Kant et al., 2021. Viruses).

We chose the wt BalB/c model as it better mimics natural respiratory infection in human patients, while the transgene K18-hACE2 model also results in strong infection of the brain. As discussed above, while infection with the Beta variant is efficient, it is not associated with clinical signs, it has only limited pathological effects (mild tissue damage and very limited inflammatory response) and is naturally cleared after 4 days. The ancestral Wuhan strain of SARS-CoV-2 as well as most other variants, in contrast, are unable to bind murine ACE, hence would require the use of transgenic mouse models expressing the human ACE receptor.

• It would have been interesting to complete the experiments with a demonstration that the compounds block viral transmission. RESPONSE: We apologize for our oversight of not including the statistical analyses in the original version of the manuscript. As requested, it is now included. We are pleased to confirm that in all cases, the differences were statistically significant between presence and absence of combined drugs, and fully support our original conclusions.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In manuscript reference RC-2023-02113, the authors addressed the impact of inhibitors of cell host factors as therapeutics against SARS-CoVé infection. They tested the combined inhibition of the enzymatic activities of the endosomal PIKfyve phosphoinositide kinase and the serine protease TMPRSS2, known as essential to meditate viral entry pathways: Conclusion: They showed a reduction, as assessed in vitro experiment (cell line) and in lung infection in mice intranasally- infected with SARS-CoV-2 beta. Moreover, the reduced viral infection is, as expected, associated to level cell damage.

Positive points:

• The topic is of interest
• Robust impact of the treatment although kinetic analysis post infection/symptoms are missing

Significance

Positive points:

• The topic is of interest
• Robust impact of the treatment although kinetic analysis post infection/symptoms are missing

Limitation

• Such a robust levels of infection in this model (female BALB/c mice) is surprising, owing that the ACE is not the appropriate homologue.
• Statistical analysis are missing for most of the results

Should be improved to support the strong conclusions.

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Referee #2

Evidence, reproducibility and clarity

In this paper, the authors tested the antiviral activity of a combination of compounds by intranasal instillation in a mouse model of SARS-CoV-2. The two compounds used are PIKfyve Kinase inhibitor apilimod dimesylate, which inhibits endosomal maturation, and TMPRSS2 protease inhibitor nafamostat mesylate. The authors have previously shown that a combination of these two inhibitors acts synergistically to prevent entry and infection of SARS-CoV-2 in cell culture. Here, they further investigated the anti-SARS-CoV-2 activity of their combination of compounds by in vivo testing. They used Balb/c mice intranasally inoculated with the Beta variant of SARS-CoV-2. Their data show that concurrent administration of the combo together with the virus prevented lung infection without blocking nasal replication. Delayed administration of the compounds did not reduce replication in the lungs. The only effect was a decrease in bronchiolar cell death. Furthermore, they also tested the stability of the combo at room temperature and their data indicate that these compounds can be kept at room temperature for at least 3 months without losing antiviral activity, at least when resuspended in water. These data are potentially interesting but they need to be consolidated by additional experiments.

Major comments:

1. The authors only present immunohistochemistry to investigate viral replication in the nose. A quantitative analysis of replication would allow for better conclusions concerning viral replication in this organ.
2. Complementary investigation on a potential anti-inflammatory effect of the drugs would also be welcome. Furthermore, it is surprising that the authors did not report potential weight changes.
3. It would have been interesting to complete the experiments with a demonstration that the compounds block viral transmission.

Minor comments:

1. The second paragraph of the introduction is not clear. It needs to be re-written. Furthermore, there is no evidence that Calu3 cells do not express cathepsins.
2. Figure 4C: Is there any explanation for the lack of apoptosis? The authors should at least provide some hypotheses. Furthermore, this figure is quoted as Figure 4B in the text instead of Figure 4C.
3. Line 199: The authors claim that the effect of their combo is synergistic. However, this cannot be clearly concluded without appropriate additional experiments where they vary the concentration of the compounds.
4. Line 211: The sentence is incomplete
5. The lettering in the panels needs to be doublechecked.

Significance

General assessment:

Finding new antiviral against SARS-CoV-2 remains a priority to fight against COVID-19. The validation of a combination of two molecules showing a partial antiviral activity in vivo is therefore of interest. However, this combo does not block viral replication in the nose and is inefficient when the treatment is added after infection, limiting the use of these molecules to prevent people in contact with COVID-19 patient of being infected. However, the authors should demonstrate that their molecules block viral transmission.

Advance:

The number of antivirals used in the clinics to treat COVID-19 patients remains extremely limited. Increasing the number of drugs available is still sorely needed.

Audience:

This paper potentially of large interest since the general population has been well informed of and/or have experienced COVID-19. Therefore, it is of interest beyond the virology and infectiology fields.

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

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Referee #1

Evidence, reproducibility and clarity

Summary

In this work, Kant and co-workers describe a two drugs regimen for therapeutics treatment of SARS-CoV-2 infection. SARS-CoV-2 infection of cells is dependent on the cleavage of the spike S protein by cellular proteases that prime S allowing the envelop protein to fuse of host membrane during entry and delivery of the viral genome to the target cell. The most important cellular protease is TMPRSS2 located at the surface of the cell. However, in cells with TMPRSS2 levels, Cathepsins, located in endosomes have been shown to be able to also prime S. The therapeutic strategy of the authors relies on the combined usage of an inhibitor of TMPRSS2 (nafamostat) together with a compound that impairs endosomal maturation (apilimod) which is a key step for the activation of cathepsin. The rational is that a dual regimen would be more effective to inhibit SARS-COV-2 infection. Using cell lines and a combination of SARS-CoV2 infection and pseudotyped VSV particles (VSV virus where the glycoprotein has been replaced by the SARS-CoV-2 spike proteins), the authors could show that a two drug regimen was more efficient in preventing SARS-CoV-2 infection compare to single drug regimen. The authors next employed a mouse model of SARS-CoV-2 infection and similarly could show that bi-therapy was more efficient in preventing infection. Importantly, the authors describe a new formulation of the drugs that improve stability of the compounds and shelve life which could be of great benefit with respect to storage needs in therapeutic setting of the population. While the reviewer think the work is potentially very relevant, some of the conclusions are not fully supported by the data and additional experiments/quantifications should be performed to improve rigor and fully support the author conclusions.

Major comments

• Throughout the paper, statistical analysis of the results should be performed to support the conclusion of the authors. Currently many experiments do not have statistical analysis and P values or statical significance are missing in most of the figures: Figure 1B, 1D, 4A, 5B,and S2.
• Quantification of the various pathology observed in mice should be quantified and scored. In the current version, the authors provided a supplementary table describing the pathology observed in individual mice upon SARS-CoV-2 infection. Adapted scoring of the different pathologies should be performed to obtain a statistical view of the pathology induced by SARS-CoV-2 and how this I prevented by the mono and bi-therapy approaches. Additionally, table 1, is very difficult to read as mice are classified in 3 experiments but this does not match with the individual figures, making it very hard to look for the phenotypes. Is it an order issue within the table or are murine infection experiments performed in the order described in table 1?. In this case, can the data be compared between the experiments as some conditions belong to experiment 2 and other to experiment 3? Given the low number of mice, do the experiments have statistical power? To show that treatment of mouse at 3 or 6hpi indeed reduce the number of capsase positive cells, the authors should perform a complete quantification and not limit there analysis to one representative tissue section from one animal
• the authors insist on the new formulation that improves drug stability. To make this statement, this will need to be actively tested both in cell culture and in animal models. Currently, the authors test the drugs stored 3 months at 25c or -20c and show that they remain active, but in this experiment freshly made drug was not directly tested in parallel. Additionally, to make such a statement, different concentration of the drugs should be tested to calculate a IC50 for freshly prepared drug and stored drugs (as the current concentration tested might be at saturating concentration). Finally, the mouse experiments are performed with freshly made compounds and if the authors want to highlight the new formulation and increased stability, experiments in mice should be performed also with stored compounds. Alternatively, statement on drug stability should be removed or strongly tuned down from text.
• Statistical analysis on figure 2b should be done between nafamostat alone and dual treatment to show that both drugs are cooperative in term of antiviral activities
• The authors state "A quantitative assessment of the in vivo synergy is shown here by the enhanced decrease of viral RNA in lungs of mice treated with both drugs at very low concentrations (Figure 2 B, compare using 2 mg/Kg apilimod dimesylate and 4 mg/Kg nafamostat mesylate alone, and in combination)." I guess, the authors want to comment on the fact that 0.2 mg/kg of apilimod and 0.4 mg/kg of nafamostat are as potent as 2 and 4 mg/kg. is that correct? If YES, to make this statement, bi-therapy should be compared to mono-therapy at the same concentration.
• when drugs are injected after infection (Fig 4), the drugs are not active. In fact, unless the reviewer mis-understood the plot, the mouse are even more infected compared to vehicle. The authors wrote that both regimes are equally less effective compared to drug administered during infection. The authors should write that both regimes are equally none protective. If drugs are not active after infection, does this approach really represent a therapeutic solution. The authors suggest that it does by limiting pathologies but this needs to be better quantified (see comment above)
• In the rebound experiment: unless the reviewer misunderstood, it appears that no conclusion can be driven from this experiment. Q-PCR data for vehicle animal a 4dpi show no sign of infection, so the experiment is not really interpretable since control animals are no longer positive. The authors suggest that there is less pathologies but this needs to be better quantified (see comment above)

Minor comments

• It will make reading easier if the authors always mentioned which drugs inhibit what. For example: addition of the TMPRSS2 inhibitor nafamostat etc.... or addition of apilimod to block cathepsins activities.....
• Figure 1: make a comment in the text that cells with low TMPRSS2 are more sensitive to the cathepsin inhibitor apilimod and vice versa, cells with high TMPRSS2 are more sensitive to nafamostat. This is expected and it could be highlighted.
• Figure 2B: how are the data normalized?. should not RdRp, E and SubE all have a mean at 100% for the vehicle?
• Line 211: something is missing here "when (Fig 2...)
• Line 221 should figure 4c
• Figure legends should only contain the details of the experimental design but should not contain description and interpretation of data. This is very minor and maybe a question of taste.

Referees cross-commenting

the other reviewers have highlighted the same limitations concerning the lack of quantifications of the immunochemistry and also the lack of robust statistical analyses.

this should be highlighted to the authors as it appears to be the minimum to do prior publication. this should not take too much time as the data are in principle already available

Significance

The work by Kant and co-workers is potentially very significant but some limitations (as highlighted above) impair the impact of the work in his current version. The approach employing a two-drug regimen to combat SARS-COV-2 infection by targeting both TMPRSS2 and cathepsin activities is not new and was described before by the authors themselves. Employing this approach in an animal model is new and the new formulation improving drug stability and facilitating storage could be a game changer in therapeutic setting of patients. As such, this work could be highly significant and of broad interest. However, additional experiments and clarifications are needs to elevate this work to high impact standards. The reviewer believes that the requested experiments are easily achievable by the research teams of this project and think that the project will ultimately have a strong impact in the field.

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Reply to the reviewers

Manuscript number: RC-2023-02224R

Corresponding author(s): Austin Smith

1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

We thank the reviewers for constructive comments and helpful suggestions which we have adopted to clarify and improve the manuscript. In addition, we have added a link to a web portal that will allow readers to visualise gene expression profiles and create their own plots using our early human embryo UMAP embedding (https://bioinformatics.crick.ac.uk/shiny/users/boeings/radley2024umap_app/). Stefan Boeing created this tool and is added to the author list with agreement of other authors.

2. Point-by-point description of the revisions

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

Summary In this manuscript, Arthur Radley and Austin Smith designed a new feature selection method for scRNA-Seq, which is a successor to ESFW previously proposed by the same authors. As an evolution of this earlier framework, cESFW is also based on the idea that informative genes share information with other genes, whereas non-informative genes have a more random relative expression. The authors emphasize the key importance of feature selection in the scRNA-Seq workflow and assess the current state of the art for this step. They also propose that better feature selection leads to less data transformation. They show that cESFW outperforms Scran and Seurat feature selection in most cases of synthetic datasets. cESFW is then used in the context of early human development, re-analysing data from several published datasets where they show that they do not require batch correction. They also further strengthen the conclusion that a "2-step" model for TE-ICM and EPI-Hyp differentiation is also present in human embyros. Finally, they map several types of in vitro pluripotent stem cells, in particular primed and naive, to their manifold and study the evolution of the gene signatures during early human development. Overall, the manuscript is well written and presents a solid methodology. The re-analysis of human early development is convincing and justified. The main critic is that the quality of figures can be greatly improved: their resolution is too low and they are hard to read. For instance, more contrasted color schemes could be used to improve clarity, and given the high number of clusters for some UMAPs, indicating the name of some cluster near their centroids should improve clarity.

We agree that the resolution of the figures should be improved. We had to compress the images to satisfy the size limit for uploaded documents to bioRxiv. Our final submission will be of higher quality (original figures are at 900dpi). With regards to colour schemes, this is a surprisingly difficult problem. We tried multiple colour palettes but could not achieve greater contrast. The suggestion to add key cluster names near to their centroids on the UMAPs is an excellent idea, which we have implemented.

Comments: Page 2 I think the criticism of PCA is unfair because it is not a true feature selection method, and it is mainly used for computational purposes. I believe that for most workflows, between 30 and 50 PCs are retained, which do not significantly change the results in the downstream analyses. The citation (Yeung and Ruzzo 2001) does not seem appropriate, as they examine cases where only a small number of PCs are retained, outside the context of scRNA-seq.

We agree that the criticism of PCA is insufficiently justified by the citation. We thank the reviewer for pointing this out and have removed the comment.

"Furthermore, HVG selection has been found to be biased toward selecting highly expressed genes over low expressed genes." Could the author justify or remove this statement, as the Seurat and Scran methods are specifically designed to consider average expression to determine HVG? The cited article (Yip, Sham, and Wang 2019) raises this issue for methods other than Seurat and scran.

The reviewer is correct that the provided citation highlights Seurat and Scran HVG selection as relatively insensitive to the average gene expression levels compared with other HVG selection methods. We again thank the reviewer and have deleted the comment.

More generally, we have shortened the introduction, focusing on cESFW as a new approach to feature selection rather than critiquing alternative methods.

Page 6 I might have missed it, but I do not understand the number of cells in the early human development dataset also shown in Figure S2B. The Petropoulos et al. dataset alone is larger than the sum of cells from different cell types. Is there some filtering step that is not described?

We have added text in the data availability section to clarify the cells used in our analysis:

“The pre-implantation raw counts scRNA-seq data from Yan et al. 2013, Petropoulos et al. 2016, Fogarty et al. 2017, and Meistermann et al. 2021, were compiled into a single gene expression matrix by Meistermann et al. 2021. For information regarding quality control and cell filtering of these 4 datasets, please refer to Meistermann et al. 2021.”

The unsupervised clustering used to annotate cell types is unconventional (especially with the high number of clusters chosen), which is not a problem, but should be clarified. Improving the figure 3D to make it clearer and providing a cell cluster correlation plot might help to better appreciate the relationship between cell types.

We agree that the gene expression heatmap in figure 3D contributed little to the interpretation of the data/results. As suggested, we have replaced this heatmap with a cell cluster correlation plot to help appreciate cell state similarities. (Changes in figure 3.)

It could be emphasized that the ICM/TE branch cell type is a major difference with the mouse topology, as the readers might not be aware that the ICM/TE is an unspecified blastocyst state that only exists in humans.

There appears to be some misunderstanding around the use of “ICM/TE branch”. The cluster comprises an uncommitted population at the branching point from morula to either ICM or TE, as also described in the mouse embryo. We have adjusted the discussion to make more clear that the two branching point clusters are heterogeneous populations, not unitary cell types or states:

“The branching populations reside at critical junctures in blastocyst formation, the partitioning of extraembryonic and embryonic lineages. These branchpoint clusters do not define unitary states. On the contrary, cells in these clusters are heterogeneous and may become specified to alternative fates. For example, PDGFRA, a hypoblast marker (Corujo-Simon et al. 2023), and NANOG, an epiblast marker (Allegre et al. 2022), are heterogeneously distributed in the Epi/Hyp branching population. Furthermore, branch cluster boundaries extend beyond the topological bifurcation, potentially indicating that cells remain plastic and may be redirected. This would be consistent with the demonstration in mouse embryos that cells expressing ICM genes remain capable of generating TE up to the late 32-cell stage (Posfai et al. 2017).”

Page 9 To further substantiate the stepwise ICM/TE and EPI/PrE specification events, authors could project cells from each embryo on the UMAP, and analyze what are the co-occurrence of cells (as performed for instance in Meistermann et al 2021). This should show as reported (and cited by the authors) that some GATA3 positive cells (TE fated) start appearing from late morula stage and that ICM cells almost never co-exist with EPI nor Hyp in embryos.

We appreciate this suggestion. We have generated the requested plots showing where cells from individual embryos at different developmental timepoints are positioned on our UMAP embedding. (new supplemental figure (New figure, Figure S6). We present a summary heatmap of cell co-occurrence in revised Figure 4. These results offer greater insight than the RNA velocity analysis, which we have moved to supplemental Figure S6. We have added discussion of these analyses in the “Lineage branching blastocyst development” Results section.

Reviewer #1 (Significance (Required)):

The presented methodology shows significant value especially in the field of scRNA-Seq, where the critical step of feature selection is often inadequately addressed. Furthermore, this field is characterized by a limited set of feature selection methodologies. cESFW appears to be an important alternative to HVG methods that could improve scRNA-Seq analysis in certain contexts.

The new findings on early human development are somehow incremental, but a welcome addition to solidify the two-step model and refine the concept of reject cells. The audience for this early development context is specialized, but cESFW will most likely have an impact to the entire field of scRNA-Seq analysis.

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

Here, Radley and Austin present a novel approach for feature weighting in scRNAseq data based on entropy sorting. Feature selection is a central part of scRNAseq analysis, and it is most likely the case that there is no single approach that outperforms all others across all datasets. Hence, innovation in this space is needed for the field. The cESFW method presented here has several appealing properties from a theoretical point of view, and it also performs well on the synthetic and real datasets considered. Nevertheless, there are several major issues that need to be addressed before I can recommend the manuscript for publication:

1 The original entropy sorting (eq 1 in SI 1) is based on only two discrete states. However, calculating entropy for continuous distributions can be more tricky and it is unclear to me what assumptions are made regarding the gene expression. Could the authors clarify what properties of the distribution are required for the updated ESE equation to be valid? Is the only assumption that values are drawn from the [0, 1] interval? What happens if values are highly skewed, ie forming a bimodal or power-law distribution rather than something close to a uniform distribution?

We agree that it is beneficial to clarify these points. We have added a section titled “Assumed properties of underlying sample distributions” to the supplemental information. Briefly, we show that the ESS correlation metric is directly linked to the commonly used correlation metric, Mutual Information (MI). A desirable properly of MI is that it is able to capture non-linear/skewed relationships between features. The ES framework and ESS share this property with MI, allowing the ES framework to be relatively robust to presence of non-uniform distributions.

The main assumption for applying ES is that the features can be meaningfully scaled between values of 0 and 1. For gene expression, an intuitive way of achieving this is to inspect each gene and designate 0 count values as having 0 expression activity, and the maximum counts as having activities of 1, and all values in between existing within the [0,1] interval. A useful property of ES is that we do not need to assume a particular shape or distribution of the samples within the [0, 1] interval. The ES framework is non-parametric and does not require an assumed distribution to calculate the conditional entropy (CE), even in the continuous form. This is possible because the ES framework is formulated by turning the probabilistic form of CE into an ordinary differential equation (ODE), where the only dependent variable, x, is the overlap between the minority state activities of each individual sample. This calculation is explicitly identifiable/calculable, and is permutation invariant, meaning the shape of the distributions of a reference feature (RF) and query feature (QF) does not need to be assumed/defined. In other words, the ES framework quantifies to what degree active expression states enrich/overlap with one another in a manner that is robust to different distribution shapes.

2 How robust is the procedure for the choice of percentile for normalizing the gene expression scores? Does one get roughly the same results for 90-99th percentile or is it sensitive to this choice?

We have carried out a sensitivity analysis on the choice of percentile for each of the synthetic datasets and added it to the manuscript. (New figure, Figure S11). We find that on each of our 4 synthetic datasets the final results of cESFW are robust to a wide range of normalisation percentiles.

3 Similarly, I am concerned about the procedure for how to choose the number of significant genes. How robust is this process? Also, it is not altogether clear how to generalize the procedure outlined on p19. Most potential users would benefit from more quantitative guidelines. In particular, having to rely on interpretation of GO terms typically requires a considerable amount of understanding about the system at hand which could make it challenging to apply the procedure for others. For most users it would be helpful to know how robust the procedure is to this step and also if there could be more stringent guidelines for how to decide which genes to include.

We understand the reviewers concern regarding the robustness of feature selection on real scRNA-seq datasets. We have now applied our cESFW workflow to peripheral blood mononuclear cells (PBMC) scRNA-seq data, and found cESFW feature selection to be comparable, and by one metric more robust, than Seurat and Scran HVG selection (New Figure S2).

As cESFW is applied to more scRNA-seq data, we will learn more about how results compare to highly variable gene selection, and how workflows may be adapted to optimise results in different scenarios. For example, we have found that supervising the selection of gene clusters using a small set of markers known to be important in the system of study can help identify which clusters of genes should be retained during gene selection. We have added this to the materials and methods with the following paragraph:

“Furthermore, we suggest supervising the selection of gene clusters using a small set of markers known to be important in the system of study. In this work, we found that genes known to be important during early human embryo development (FigS4) are enriched in the dark blue cluster of genes, further suggesting that this cluster of genes is more likely to separate cell type identities in downstream analysis.”

While gene cluster selection supervision in this manner requires a degree of domain expertise, we believe this is not unreasonable for most applications, and is the case for many scRNA-seq analysis pipelines.

Our primary software contribution is the cESFW algorithm which calculates the ESS and EP matrices. With this manuscript we provide 6 commented workflows for applying cESFW to different datasets (4 synthetic data, human embryo data, PBMC data). We believe these workflows provide a good balance of documented use cases and user flexibility for cESFW usage. This is important because it is advantageous to be able easily to adapt workflows to incorporate domain expertise and different methodologies. Although workflows such as Seurat and Scran are user-friendly, their rigidity can be difficult when wanting to deviate from their standard workflows. In summary, we believe that our provided workflows are suitable for users to implement cESFW, while providing the flexibility to apply adapted pipelines.

4 The comparison of the clusterings on p6 is not really fair is it? If I understand it correctly, the 3,012 genes identified by cESFW was used to define clusters in fig 3c through unsupervised clustering. The authors then use HVG methods to identify 3,012 genes and then carries out clustering based on those. To evaluate the methods the silhouette score is used, but the labels from the cESFW clustering is used as ground truth. This does not sound like a fair way to compare. Could the authors please clarify, and if needed come up with an approach where the three methods have a more level playing field if needed.

The reviewer raises a fair point regarding the comparison of cluster identities and ranked gene lists. This issue is a chicken and egg problem, in that we require a baseline to benchmark different methodologies but lack an explicitly defined ground truth. For that reason we used synthetic datasets for initial comparison.

For the human embryo data, we have presented substantial evidence that our cluster annotations are biologically coherent and consistent with prior knowledge. We therefore consider it legitimate to compare the ranked lists of Seurat, Scran and cESFW. However, we acknowledge the potential bias and have mentioned this in the “Limitations of the study” section.

In addition, we have now analysed the peripheral blood mononuclear cells (PBMC) scRNA-seq dataset that is used in the tutorial workflows of Seurat and Scran. This PBMC dataset is arguably better defined since it has more discrete populations of cells, and by using the Seurat generated cell type labels we bias the analysis towards Seurat rather than cESFW. The results show that cESFW performs comparably to Seurat and Scran, and that the cESFW ranked gene list may be more stable than Seurat and Scran. These results suggest that cESFW can be widely applicable as a suitable alternative for feature selection. We have included this analysis in the Results and as a supplemental figure (New figure, Figure S2).

5 The main cESFW.py file in the github repository is clearly well structured and commented. However, I would like to see a much better documentation so that one does not have to go through the source code to understand what functions there are and what they do. In particular, I would like to see a vignette to make it easier for others to incorporate cESFW into their workflows.

We thank the reviewer for the positive comments regarding our cESFW.py commenting. We accept that our initial submission failed to point the reader directly towards our example workflows that provide step by step, well commented vignettes for using cESFW to analyse scRNA-seq data. In our initial submission we provided 5 workflows (4 synthetic data and the human embryo data), and in the re-submission we have added a workflow for analysing PBMC data. We have updated our cESFW Github to guide users to these example workflows (https://github.com/aradley/cESFW/tree/main).

Please note, the embryo workflow will be easily accessible through GitHub, whereas the synthetic data and PBMC workflows will be provided through a Mendeley data link (referenced in the manuscript and on our GitHub). However, the content of the Mendeley link cannot be made public until the paper is finalised, as it cannot be changed after publication. We provide a temporary public Dropbox link for the reviewers so that they may access the additional workflows (https://www.dropbox.com/scl/fo/xr5o9xm6490ftjsa55wxg/h?rlkey=maindrxwdqnirsw1en3my5qsr&dl=0).

Minor:

Why are the figures not always in order? For example, fig S10 is mentioned before fig S2 on p 6

Thank you for pointing this out; we have amended the text.

I am not sure if the indexing in eq 1 (p 18) is correct. j is both on the LHS and it is also being summed over on the RHS. Should one of these be i instead?

The indexing is correct. Each column j of a matrix refers to gene/feature on the RHS, and in the calculation on the RHS we take the column averages, leading to vector on the LHS that is still indexed by genes/features j. We have clarified this in the text.

Reviewer #2 (Significance (Required)):

The work presents a new method for feature selection in scRNAseq. Feature selection is a very important step and can have a big impact on findings. The method presented here is theoretically sound and it seems to provide interesting result when applied to early embryo development. However, as cESFW is only tested for one dataset it is unclear how well the method generalizes to other problems and datasets.

Appreciation of the utility of cESFW will grow as it is applied to more datasets. However, we would like to highlight that the human embryo dataset consists of 6 independent scRNA-seq datasets from different laboratories, and that cESFW was able to identify common and differing structure between them without any batch correction, smoothing or feature extraction. We have added to our summary that we propose cESFW may be best suited to analysis of transcriptome trajectories in time course and developmental data. However, we have also now performed comparison of Seurat, Scran and cESFW feature selection in a different context, using a reference PMBC scRNA-seq dataset. The results demonstrate that cESFW is a viable alternative for feature selection in that static system also (New figure, Figure S2).

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Referee #2

Evidence, reproducibility and clarity

Here, Radley and Austin present a novel approach for feature weighting in scRNAseq data based on entropy sorting. Feature selection is a central part of scRNAseq analysis, and it is most likely the case that there is no single approach that outperforms all others across all datasets. Hence, innovation in this space is needed for the field. The cESFW method presented here has several appealing properties from a theoretical point of view, and it also performs well on the synthetic and real datasets considered. Nevertheless, there are several major issues that need to be addressed before I can recommend the manuscript for publication:

1. The original entropy sorting (eq 1 in SI 1) is based on only two discrete states. However, calculating entropy for continuous distributions can be more tricky and it is unclear to me what assumptions are made regarding the gene expression. Could the authors clarify what properties of the distribution are required for the updated ESE equation to be valid? Is the only assumption that values are drawn from the [0, 1] interval? What happens if values are highly skewed, ie forming a bimodal or power-law distribution rather than something close to a uniform distribution?
2. How robust is the procedure for the choice of percentile for normalizing the gene expression scores? Does one get roughly the same results for 90-99th percentile or is it sensitive to this choice?
3. Similarly, I am concerned about the procedure for how to choose the number of significant genes. How robust is this process? Also, it is not altogether clear how to generalize the procedure outlined on p19. Most potential users would benefit from more quantitative guidelines. In particular, having to rely on interpretation of GO terms typically requires a considerable amount of understanding about the system at hand which could make it challenging to apply the procedure for others. For most users it would be helpful to know how robust the procedure is to this step and also if there could be more stringent guidelines for how to decide which genes to include.
4. The comparison of the clusterings on p6 is not really fair is it? If I understand it correctly, the 3,012 genes identified by cESFW was used to define clusters in fig 3c through unsupervised clustering. The authors then use HVG methods to identify 3,012 genes and then carries out clustering based on those. To evaluate the methods the silhouette score is used, but the labels from the cESFW clustering is used as ground truth. This does not sound like a fair way to compare. Could the authors please clarify, and if needed come up with an approach where the three methods have a more level playing field if needed.
5. The main cESFW.py file in the github repository is clearly well structured and commented. However, I would like to see a much better documentation so that one does not have to go through the source code to understand what functions there are and what they do. In particular, I would like to see a vignette to make it easier for others to incorporate cESFW into their workflows.

Minor:

Why are the figures not always in order? For example, fig S10 is mentioned before fig S2 on p 6

I am not sure if the indexing in eq 1 (p 18) is correct. j is both on the LHS and it is also being summed over on the RHS. Should one of these be i instead?

Significance

The work presents a new method for feature selection in scRNAseq. Feature selection is a very important step and can have a big impact on findings. The method presented here is theoretically sound and it seems to provide interesting result when applied to early embryo development. However, as cESFW is only tested for one dataset it is unclear how well the method generalizes to other problems and datasets.

My expertise is in computational genomics.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this manuscript, Arthur Radley and Austin Smith designed a new feature selection method for scRNA-Seq, which is a successor to ESFW previously proposed by the same authors. As an evolution of this earlier framework, cESFW is also based on the idea that informative genes share information with other genes, whereas non-informative genes have a more random relative expression. The authors emphasize the key importance of feature selection in the scRNA-Seq workflow and assess the current state of the art for this step. They also propose that better feature selection leads to less data transformation. They show that cESFW outperforms Scran and Seurat feature selection in most cases of synthetic datasets. cESFW is then used in the context of early human development, re-analysing data from several published datasets where they show that they do not require batch correction. They also further strengthen the conclusion that a "2-step" model for TE-ICM and EPI-Hyp differentiation is also present in human embyros. Finally, they map several types of in vitro pluripotent stem cells, in particular primed and naive, to their manifold and study the evolution of the gene signatures during early human development. Overall, the manuscript is well written and presents a solid methodology. The re-analysis of human early development is convincing and justified. The main critic is that the quality of figures can be greatly improved: their resolution is too low and they are hard to read. For instance, more contrasted color schemes could be used to improve clarity, and given the high number of clusters for some UMAPs, indicating the name of some cluster near their centroids should improve clarity.

Comments:

Page 2 I think the criticism of PCA is unfair because it is not a true feature selection method, and it is mainly used for computational purposes. I believe that for most workflows, between 30 and 50 PCs are retained, which do not significantly change the results in the downstream analyses. The citation (Yeung and Ruzzo 2001) does not seem appropriate, as they examine cases where only a small number of PCs are retained, outside the context of scRNA-seq. "Furthermore, HVG selection has been found to be biased toward selecting highly expressed genes over low expressed genes." Could the author justify or remove this statement, as the Seurat and Scran methods are specifically designed to consider average expression to determine HVG? The cited article (Yip, Sham, and Wang 2019) raises this issue for methods other than Seurat and scran.

Page 6 I might have missed it, but I do not understand the number of cells in the early human development dataset also shown in Figure S2B. The Petropoulos et al. dataset alone is larger than the sum of cells from different cell types. Is there some filtering step that is not described? The unsupervised clustering used to annotate cell types is unconventional (especially with the high number of clusters chosen), which is not a problem, but should be clarified. Improving the figure 3D to make it clearer and providing a cell cluster correlation plot might help to better appreciate the relationship between cell types. It could be emphasized that the ICM/TE branch cell type is a major difference with the mouse topology, as the readers might not be aware that the ICM/TE is an unspecified blastocyst state that only exists in humans.

Page 9 To further substantiate the stepwise ICM/TE and EPI/PrE specification events, authors could project cells from each embryo on the UMAP, and analyze what are the co-occurrence of cells (as performed for instance in Meistermann et al 2021). This should show as reported (and cited by the authors) that some GATA3 positive cells (TE fated) start appearing from late morula stage and that ICM cells almost never co-exist with EPI nor Hyp in embryos.

Significance

The presented methodology shows significant value especially in the field of scRNA-Seq, where the critical step of feature selection is often inadequately addressed. Furthermore, this field is characterized by a limited set of feature selection methodologies. cESFW appears to be an important alternative to HVG methods that could improve scRNA-Seq analysis in certain contexts.

The new findings on early human development are somehow incremental, but a welcome addition to solidify the two-step model and refine the concept of reject cells. The audience for this early development context is specialized, but cESFW will most likely have an impact to the entire field of scRNA-Seq analysis.

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Reply to the reviewers

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

This is an excellent paper experimentally exploring variations in carboxylation rates of form I rubisco.

We thank the Reviewer for this positive feedback on our study.

I have three comments

Q. Did the authors also measure the oxygenate activity of the enzyme? This is relevant to the evolution of carboxysomes and CCMs in general.

We agree that this is relevant but there are technical limitations for achieving this with the current framework. This pipeline’s emphasis on the carboxylation rate allows for the screening of a high number of rubisco variants covering a wide genetic diversity. It provides a way to approach the complexity of the kinetic constraints of this enzyme with a realizable and reproducible method. However, we agree that the measurements of oxygenase activity, as well as affinities to CO2 and O2 , would enrich our understanding of the evolution of rubiscos in the context of CCMs, and thus expanding our pipeline in the future to cover the other kinetic dimension would be worthwhile but cannot be achieved currently due to various technical constraints (other dimensions to explore, like the temperature effect, could also be included). In line also with the comment of reviewer #3, we have expanded our discussion in the manuscript to clarify this matter more thoroughly:

“By centering our analysis on the carboxylation rate, this pipeline systematically shows the particularity of carboxysome-associated rubiscos which are characterized by a poor affinity to CO2 (Badger et al, 1998; Falkowski & Raven, 2007) alongside a relatively high carboxylation rate (our data). This likely reflects the aforementioned catalytic tradeoff, suggesting that higher local concentrations of CO2 within CCMs probably allowed rubiscos to evolve towards higher kcat and KM. High-throughput measurements of other kinetic parameters beyond what was achieved here, such as the KM for both gasses or the oxygenation rate, would be valuable. It could provide values of the carboxylation efficiency, or even the enzyme specificity, which would enrich our understanding of this enzyme and of its adaptation to the atmospheric composition over geological timescales.”

1. How do predicted structures (e.g., using Alpha fold) vary with catalytic efficient?

We generated Alpha Fold structures of the 98 active variants revealed in this study and performed preliminary structural analysis of the active site. There was no strong correlation between measured rates and the active site structure. The RMSD of generated structures has a median RMSD of 2.7 Å for the large and small subunit together, and 1.3 Å for the active site, suggesting high conservation of the structure of rubisco, and probably explaining the difficulty to associate rate variation with any clear structural feature (especially coming from prediction algorithm already showing uncertainties on the order of magnitude of an angstrom (Jumper et al, 2021; Terwilliger et al, 2024)).

We added a paragraph about this new analysis in the Results and in the Materials and Methods sections of the manuscript, and we present the results in new Supplementary Fig. 12. We made these structures available on the gitlab folder associated with this paper.

1. The authors should note the paper by Tortell (not this reviewer) https://aslopubs.onlinelibrary.wiley.com/doi/pdfdirect/10.4319/lo.2000.45.3.0744

Thank you. We added a reference to this paper in the following sentence: “Another strategy consists of the evolution of rubisco towards stronger affinity for CO2 (Tortell 2000).”

Reviewer #1 (Significance (Required)):

This is an excellent paper experimentally exploring variations in carboxylation rates of form I rubisco.

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

I very much enjoyed reviewing this manuscript. de Pins et al provide a timely report on the catalytic turnover rate of a large number of Rubisco enzymes within the FormI group. These data provide novel insights into generalities of Rubisco function, specifically within certain phylogenies, and extend our understanding of carbon acquisition in these systems. In particular, the data presented by de Pins et al provide new insights into the relative carbon fixation rates of alpha-cyanobacteria, for which there are very few studies reporting catalytic turnover. It is apparent that the CO2 concentrating mechanisms (CCM) of cyanobacteria, especially the alpha-cyanobacteria (containing FormIA Rubisco) are a globally important contributor to CO2 capture into the biosphere via their carboxysomal Rubisco enzymes. This report provides then first broad selection of FormI Rubiscos to enable comparisons of catalytic turnover across this dominant enzyme family and shows that FormIA Rubiscos from phototrophic systems, and encapsulated in carboxysomes, are on average the fastest enzymes.

We thank the Reviewer for the positive remark on the novelty of the study.

de Pins et al use a high throughput screening technique that provides a highly correlative estimate of Rubisco turnover compared with traditional assays. This screen is based upon bulk expression of enzymes within E. coli from synthesised genes, and in some cases the co-expression of chaperonin factors to boost expression and solubility of holoenzymes. The assay process is sound and of high quality and the interpretations clear and uncomplicated.

The conclusions are sound and I only have a number of minor issues for consideration.

Minor comments: Temperature effects on 'true' Rubisco turnover rates. The authors quite reasonably note that a single measurement temperature was used in the assay and that this may not necessarily reflect the catalytic turnover of Rubiscos from thermophiles. Suppl. Fig 5b indicates a relatively large number of 'hot spring' species that have, generally, a low median kcat compared with, for example, both cyanobacterial classes. Can the authors comment on whether or not the thermophile set is not highly represented by one group (e.g. phototrophic alpha-cyanobacteria). Does this thermophile dataset have the potential to influence the generalities presented? Fig 2 would suggest this is not the case but it is not possible for the reader to know if all or any thermophiles are represented in Fig2 (as opposed to Suppl. Fig 4).

We indeed identify 3 groups of rubiscos that are either expressed by thermophilic bacteria (Supplementary Figure 10), and/or are associated with hot environments (hot spring and hydrothermal vent; see Supplementary Figure 5). These rubiscos show relatively lower rates. We grouped them together and reproduced our main analysis (from Figure 2) with and without rubiscos from this group to create a new Figure (Supplementary Fig. 11). Interestingly, alpha-cyanobacteria had no representatives among this group of thermophilic and hot-environments-associated rubsicos. However, this is unlikely to explain the result observed as removing them does not influence the obtained tendencies. We add the following sentences in the Results section:

“Additionally, the slightly lower carboxylation rate of rubiscos originating from thermophilic bacteria and isolated from hot environments (Supplementary Fig. 5 and 10) aligns with expectations, considering that these rubiscos naturally work at higher temperatures than in our in vitro assay (30°C). However, this is unlikely to explain the observed trends as the main results of this study are not affected by the removal of these rubiscos (Supplementary Fig. 11).”

We also noticed, while reviewing the study, that the code generating Supplementary Fig. 8 and 10 incorrectly duplicated some dots for a few rubiscos (less than 5), although this did not affect the overall results. We have fixed this issue and have now updated the figures accordingly.

Line 98: "in spite of" should be "despite"

Done.

Lines 171-173: There is an additional alpha carboxysomal Rubisco for which there are catalytic parameters described (Chapter 11 Engineering Photosynthetic CO2 Assimilation to Develop New Crop Varieties to Cope with Future Climates. RE Sharwood, BM Long - Photosynthesis, respiration, and climate change, 2021). This book chapter reports a kcat of 11.9 s-1 for the alpha carboxysomal Rubisco from Synechococcus WH8102, very much in line with the authors conclusions.

We added this rubisco to the list of previously characterized rubisco and updated Figure 1 accordingly. We also updated the following sentence:

“However, such statements were made based on scarce measurements, with only three kcat,C values currently available for both rubisco groups (Shih et al, 2016; Long et al, 2018; Sharwood & Long, 2021; Wilson et al, 2018; Aguiló-Nicolau et al, 2023).”

Lines 232-234: I note that ref 30 posits that low CO2 was the more likely driver of carboxysome evolution than high O2.

We agree that our phrasing did not point clearly enough that CO2 was more likely the driver of carboxysome evolution, rather than high O2. We rephrase the sentence to: “Carboxysomes likely evolved during the Proterozoic eon - in the context of the continuous decrease of carbon dioxide in Earth’s atmosphere (Flamholz & Shih, 2020)”

Line 235: The preferred term is either "CO2 concentrating mechanism" or "inorganic carbon concentrating mechanism"

We rephrased into “CO2 concentrating mechanisms”.

Lines 254-256: The relative saturation of carboxysomes with Rubisco is still somewhat undecided, although relatively new datasets enable more accurate comparisons. A number of papers from the Liu Lab (Liverpool) enable estimates of Rubisco active site concentrations for alpha and beta carboxysomes in the range of 2-6 mM. It appears at this stage that Rubisco active site concentrations may be highest in alpha-carboxysomes.

We thank the reviewer for drawing our attention to the work of the Liu lab which, while acknowledging potential inaccuracies in the estimates, tends to show a higher concentration of rubiscos in alpha-carboxysomes than in beta-carboxysomes (Sun et al, 2019; Sun et al, 2022). We removed this statement from the text.

Lines 312-318: That genes were codon optimized for E. coli expression raises an interesting question about the effect of Raf1 on Rubisco solubility. Assuming expression rates were not constrained, can any conclusions be made as to the amino acid sequence differences that led to lower solubility? One assumes that the Rubisco sequences had a high degree of identity?

We indeed note that the fact that every rubisco gene from this study was codon optimized for E. coli expression suggests that the solubility issues met here were post-translational. This suggests a post-translational role for Raf1 in rubisco folding/assembly that is in line with the mechanism proposed by Xia et al. of an interaction of Raf1 with rubisco large subunits dimer, further mediating the assembly of an octameric core and the recruitment of rubisco small subunits (Xia et al, 2020). We also note that insoluble rubiscos were met in all form I clades, suggesting that this property was not linked to a specific group of rubiscos sequences with a high identity degree.

We add that we also tested the effect of not performing codon optimization on 8 rubiscos that were insoluble following codon optimization (to assess whether the codon optimization could negatively affect the folding, for instance by making the translation too fast). This did not yield any improvement in solubility.

Lines 333-344: Was there an attempt to use acRAF (Raf2?) for FormIA Rubiscos that did not fold successfully in E. coli?

While only 33% of β-carboxysome-associated (IB) rubiscos were originally soluble (i. e. without the coexpression of Raf1 from E. natronophila), 85% of the tested α-carboxysome-associated (IAc) rubiscos were soluble in our experimental conditions. We therefore decided that testing for the effect of co-expressing them with the chaperone acRAF would be less cost-effective.

Reviewer #2 (Significance (Required)):

This manuscript presents a significant advance in our broader understanding of the major enzyme involved in carbon input into the biosphere, Rubisco. It will be of key interest to those studying carbon biogeochemistry, global CO2 modelling, cyanobacterial and proteobacterial CCMs, and those interested in using these systems to improve plant-based carbon capture for food security and global carbon abatement systems. It provides, for the first time, a large dataset of hitherto unknown Rubisco kinetics in a globally important group of organisms. The study is extremely well carried out and will likely form the basis of future Rubisco screens to provide greater clarity to our knowledge base of this globally important enzyme.

My expertise is in the study and application of CCMs as CO2 acquisition systems that can be used for Synbio applications.

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

Summary: The authors have presented a tremendous study into the diversity of carboxylation speed (kcatc) from bacterial Form I Rubisco enzymes. The authors identified some nice diversity in kcatc which resulted in the finding that Rubisco's originating from within a CCM were faster, which confirms what has been previously observed in the literature. The authors provided information on a pipeline to screen large numbers of Rubisco variants. In this manuscript, the authors tested 144 different enzymes with 112 of these successfully expressed in E.coli and of these 98 showed substantial catalytic activity. The authors showed that alpha cyanobacterial Rubisco possessed the fastest kcatc when compared to beta cyanobacterial counterparts which is contrary to that published in the literature so far. The authors have provided some nice insight into how they improved expression of soluble Rubisco with expressing bacterial chaperonin and Rubisco assembly factors such as Raf1 and rbcX. All which have been previously discovered plant and cyanobacteria. The authors also presented some nice correlations as shown in figure 2 and some weaker and non-correlations to various environmental parameters in the supplementary data.

Overall, the field will learn something from this large body of work that has characterized only one Rubisco catalytic parameter.

We thank the Reviewer for these positive comments.

Major points: 1) The authors only measured carboxylation speed using a spec assay. The Michaelis constant for CO2 measured in N2 and 21% Oxygen is also valuable to understand the diversity in Rubisco catalysis. The authors should perhaps mention this and that the carboxylation efficiency is also an important measure for comparing Rubisco enzymes.

In line with this and with the comment of reviewer #1, we have expanded the Discussion to include the following:

“By centering our analysis on the carboxylation rate, this pipeline systematically shows the particularity of carboxysome-associated rubiscos which are characterized by a poor affinity to CO2 (Badger et al, 1998; Falkowski & Raven, 2007) alongside a relatively high carboxylation rate (our data). This likely reflects the aforementioned catalytic tradeoff, suggesting that higher local concentrations of CO2 within CCMs probably allowed rubiscos to evolve towards higher kcat and KM. High-throughput measurements of other kinetic parameters beyond what was achieved here, such as the KM for both gasses or the oxygenation rate, would be valuable. It could provide values of the carboxylation efficiency, or even the enzyme specificity, which would enrich our understanding of this enzyme and of its adaptation to the atmospheric composition over geological timescales.”

2) The authors mentioned that they used E.coli lysates. Did the authors test for background activity due NADH dehydrogenases which are present in bacterial lysates? This could impact the catalytic rates measured.

The background activity due to dehydrogenases from the lysate is negligible compared to the measured reaction (see as an example, in Supplementary Fig. 16A, the gray curve, corresponding to a CABP concentration of 90 nM, fully inhibiting rubisco in the reaction). Moreover, the use of CABP in the spectroscopic assay allows to take into account any “background activity” that would come from an element independent of rubisco because this background would be identical at every CABP concentration. We modified Supplementary Note 1 to make this point clearer:

“We note that any NADH dehydrogenation due to other native E. coli proteins, while low (see the [CABP] = 90 nM gray curve of Supplementary Fig. 16A), is not influencing the measurement of the carboxylation rate which relies on the differential Vmax values at changing CABP concentrations (which should not affect the rates of these dehydrogenases).”

3) For the microtitre plate assay, did the authors correct for the different pathlength? This is crucial for the Beer-Lambert law which is used to calculate the consumption of NADH.

Because our assay is performed in a microwell plate instead of a standard 1 cm quartz cuvette, we indeed calibrated the assay to empirically determine the optical path length in our conditions. We add the following sentence in the Material and Methods section to better explain the measurement of NADH concentration in our assay:

“Knowing the NADH extinction coefficient at 340 nm (ε340 = 6220 M-1cm-1), and after measuring the optical path length (𝑙 = 0.26 cm) with an NADH calibration curve in our setting, we used Beer-Lambert law (𝐴340 = ε340 . 𝑙 . 𝑐) to measure the NADH concentration 𝑐.”

4) Did the authors consider studying the temperature response of kcatc for these enzymes? This could also reveal some interesting insight into their data.

We indeed considered this. With a high-throughput pipeline involving >100 enzymes to express and test in parallel, we had to limit the experimental testing conditions to be realistic both in terms of time and budget. However, the finding that rubisco variants from thermophiles tend to have lower carboxylation rates in our standardized conditions (30°C) suggest that they will probably show faster rates at temperatures closer to their optimal growth temperature. We therefore agree that the study of the temperature response of the carboxylation rate in further works could validate these hypotheses and bring more insight into the catalytic characteristics of rubisco. We further emphasize this point in the following modified sentence:

“Investigating the temperature response of rubisco carboxylation rate in further work could shed light on the importance of this parameter, especially among thermophilic or psychrophilic associated enzymes.”

5) With this new catalytic knowledge, what can the field now do with this data to inform new research directions?

We believe this new knowledge can inform new research directions in the field of microbial ecology, metabolic engineering, and machine learning in the context of kinetic parameters prediction. We modified a paragraph in the discussion to elaborate on this point:

“This study provides a systematic exploration of bacterial form I rubisco maximal rates and its relationship with various contextual factors that could have shaped the evolution of this most abundant enzyme on Earth. It holds potential for future metabolic and ecological studies about specific bacterial species – for instance among cyanobacteria for which 40 rubiscos have been characterized here. By enriching our knowledge on carboxylation rates and their connection to environmental factors, it can also contribute to more accurately modeling global carbon fluxes. Additionally, this dataset of rubisco sequences and their associated rates can facilitate linking sequence motifs to catalytic function. Ultimately, it can improve our understanding, and possible harnessing, of bacterial CCMs for the potential development of plant-based carbon capture strategies, the increase of agricultural yields and the support of sustainable food production in the face of a changing climate.”

Minor comments: The figures are of outstanding quality and easy to follow. This will set the bar high in the literature. I have no other minor comments.

We thank the Reviewer for noting the care taken in the graphic presentation of our results.

Reviewer #3 (Significance (Required)):

Overall, the authors have presented an excellent study into bacterial Form I Rubisco's that will further enhance our understanding of Rubisco evolution. The pipeline for expression of bacterial Rubisco's in E.coli is developed nicely by the authors and the next step will be to determine how other important catalytic parameters can be determined to have more detailed understanding of Rubisco catalysis.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors have presented a tremendous study into the diversity of carboxylation speed (kcatc) from bacterial Form I Rubisco enzymes. The authors identified some nice diversity in kcatc which resulted in the finding that Rubisco's originating from within a CCM were faster, which confirms what has been previously observed in the literature. The authors provided information on a pipeline to screen large numbers of Rubisco variants. In this manuscript, the authors tested 144 different enzymes with 112 of these successfully expressed in E.coli and of these 98 showed substantial catalytic activity. The authors showed that alpha cyanobacterial Rubisco possessed the fastest kcatc when compared to beta cyanobacterial counterparts which is contrary to that published in the literature so far. The authors have provided some nice insight into how they improved expression of soluble Rubisco with expressing bacterial chaperonin and Rubisco assembly factors such as Raf1 and rbcX. All which have been previously discovered plant and cyanobacteria. The authors also presented some nice correlations as shown in figure 2 and some weaker and non-correlations to various environmental parameters in the supplementary data. Overall, the field will learn something from this large body of work that has characterized only one Rubisco catalytic parameter.

Major points:

1) The authors only measured carboxylation speed using a spec assay. The Michaelis constant for CO2 measured in N2 and 21% Oxygen is also valuable to understand the diversity in Rubisco catalysis. The authors should perhaps mention this and that the carboxylation efficiency is also an important measure for comparing Rubisco enzymes.

2) The authors mentioned that they used E.coli lysates. Did the authors test for background activity due NADH dehydrogenases which are present in bacterial lysates? This could impact the catalytic rates measured.

3) For the microtitre plate assay, did the authors correct for the different pathlength? This is crucial for the Beer-Lambert law which is used to calculate the consumption of NADH.

4) Did the authors consider studying the temperature response of kcatc for these enzymes? This could also reveal some interesting insight into their data.

5) With this new catalytic knowledge, what can the field now do with this data to inform new research directions?

Minor comments:

The figures are of outstanding quality and easy to follow. This will set the bar high in the literature. I have no other minor comments.

Significance

Overall, the authors have presented an excellent study into bacterial Form I Rubisco's that will further enhance our understanding of Rubisco evolution. The pipeline for expression of bacterial Rubisco's in E.coli is developed nicely by the authors and the next step will be to determine how other important catalytic parameters can be determined to have more detailed understanding of Rubisco catalysis.

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

• I very much enjoyed reviewing this manuscript. de Pins et al provide a timely report on the catalytic turnover rate of a large number of Rubisco enzymes within the FormI group. These data provide novel insights into generalities of Rubisco function, specifically within certain phylogenies, and extend our understanding of carbon acquisition in these systems. In particular, the data presented by de Pins et al provide new insights into the relative carbon fixation rates of alpha-cyanobacteria, for which there are very few studies reporting catalytic turnover. It is apparent that the CO2 concentrating mechanisms (CCM) of cyanobacteria, especially the alpha-cyanobacteria (containing FormIA Rubisco) are a globally important contributor to CO2 capture into the biosphere via their carboxysomal Rubisco enzymes. This report provides then first broad selection of FormI Rubiscos to enable comparisons of catalytic turnover across this dominant enzyme family and shows that FormIA Rubiscos from phototrophic systems, and encapsulated in carboxysomes, are on average the fastest enzymes.

• de Pins et al use a high throughput screening technique that provides a highly correlative estimate of Rubisco turnover compared with traditional assays. This screen is based upon bulk expression of enzymes within E. coli from synthesised genes, and in some cases the co-expression of chaperonin factors to boost expression and solubility of holoenzymes. The assay process is sound and of high quality and the interpretations clear and uncomplicated.

• The conclusions are sound and I only have a number of minor issues for consideration.

Minor comments:

• Temperature effects on 'true' Rubisco turnover rates. The authors quite reasonably note that a single measurement temperature was used in the assay and that this may not necessarily reflect the catalytic turnover of Rubiscos from thermophiles. Suppl. Fig 5b indicates a relatively large number of 'hot spring' species that have, generally, a low median kcat compared with, for example, both cyanobacterial classes. Can the authors comment on whether or not the thermophile set is not highly represented by one group (e.g. phototrophic alpha-cyanobacteria). Does this thermophile dataset have the potential to influence the generalities presented? Fig 2 would suggest this is not the case but it is not possible for the reader to know if all or any thermophiles are represented in Fig2 (as opposed to Suppl. Fig 4).

• Line 98: "in spite of" should be "despite"

• Lines 171-173: There is an additional alpha carboxysomal Rubisco for which there are catalytic parameters described (Chapter 11 Engineering Photosynthetic CO2 Assimilation to Develop New Crop Varieties to Cope with Future Climates. RE Sharwood, BM Long - Photosynthesis, respiration, and climate change, 2021). This book chapter reports a kcat of 11.9 s-1 for the alpha carboxysomal Rubisco from Synechococcus WH8102, very much in line with the authors conclusions.

• Lines 232-234: I note that ref 30 posits that low CO2 was the more likely driver of carboxysome evolution than high O2.

• Line 235: The preferred term is either "CO2 concentrating mechanism" or "inorganic carbon concentrating mechanism"

• Lines 254-256: The relative saturation of carboxysomes with Rubisco is still somewhat undecided, although relatively new datasets enable more accurate comparisons. A number of papers from the Liu Lab (Liverpool) enable estimates of Rubisco active site concentrations for alpha and beta carboxysomes in the range of 2-6 mM. It appears at this stage that Rubisco active site concentrations may be highest in alpha-carboxysomes.

• Lines 312-318: That genes were codon optimized for E. coli expression raises an interesting question about the effect of Raf1 on Rubisco solubility. Assuming expression rates were not constrained, can any conclusions be made as to the amino acid sequence differences that led to lower solubility? One assumes that the Rubisco sequences had a high degree of identity?

• Lines 333-344: Was there an attempt to use acRAF (Raf2?) for FormIA Rubiscos that did not fold successfully in E. coli?

Significance

This manuscript presents a significant advance in our broader understanding of the major enzyme involved in carbon input into the biosphere, Rubisco. It will be of key interest to those studying carbon biogeochemistry, global CO2 modelling, cyanobacterial and proteobacterial CCMs, and those interested in using these systems to improve plant-based carbon capture for food security and global carbon abatement systems. It provides, for the first time, a large dataset of hitherto unknown Rubisco kinetics in a globally important group of organisms. The study is extremely well carried out and will likely form the basis of future Rubisco screens to provide greater clarity to our knowledge base of this globally important enzyme.

My expertise is in the study and application of CCMs as CO2 acquisition systems that can be used for Synbio applications.

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

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Referee #1

Evidence, reproducibility and clarity

This is an excellent paper experimentally exploring variations in carboxylation rates of form I rubisco.

I have three comments

1. Q. Did the authors also measure the oxygenate activity of the enzyme? This is relevant to the evolution of carboxysomes and CCMs in general.

2. How do predicted structures (e.g., using Alpha fold) vary with catalytic efficient?

3. The authors should note the paper by Tortell (not this reviewer) https://aslopubs.onlinelibrary.wiley.com/doi/pdfdirect/10.4319/lo.2000.45.3.0744

Significance

This is an excellent paper experimentally exploring variations in carboxylation rates of form I rubisco.

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Reply to the reviewers

We thank the three reviewers for their thoughtful and constructive comments. The changes to the text and figures made in response to the questions raised have made this a clearer and stronger manuscript. The additional citations suggested by the reviewers helped to further anchor our study within the growing literature on facultative parthenogenesis. Below we have responded to each comment in blue. We have added new data to the manuscript (Fig. 4C, Fig. S10B and Fig. S10D).

Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

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

1. Summary: Here Ho et al. provide strong molecular evidence for the production of facultatively parthenogenetic whiptail lizards, through a gametic duplication. As evidenced through multiple routes, including microsatellites, WGS, RADseq, and RBC ploidy, and lines of evidence from multiple specimens, this study is timely in furthering our understanding of the mechanisms underlying FP. The findings are conclusive.

That said, I have several comments that should be addressed prior to publication. The introduction which addresses FP in other systems fails to cite several key studies that provide strongly molecular support for terminal fusion automixis. Similarly, the study pushes the idea that this is an adaptive trait, however without proving that the parthenogens can themselves reproduce, this is a moot point at this stage.

That said, my comments are minor. I found this to be an excellent study, well written, comprehensive in methodology, and one that I strongly advocate for publication.

We thank reviewer 1 for referring to our manuscript as an excellent study and strongly advocating for its publication. We concur with his/her points that evidence for automixis in other systems was not sufficiently referenced and that the adaptive trait hypothesis for FP is somewhat speculative. The text has been modified accordingly (see below).

Major comments - None.

Minor Comments: Should be addressed.

Line 36 - However, data that supports terminal fusion are no longer restricted to microsat data. Studies utilizing RADseq and whole-genome sequencing in snakes and crocodiles have now provided further evidence supporting terminal fusion.

See: Booth et al. 2023. Discovery of facultative parthenogenesis in a new world crocodile. Biology Letters. 19, 20230129.

Card et al. 2021. Genome-wide data implicate terminal fusion automixis in king cobra facultative parthenogenesis. Scientific Reports. 11, 1-9

Allen et al. 2018. Molecular evidence for the first records of facultative parthenogenesis in elapid snakes. R. Soc. Open. Sci. 5, 171901.

We have now included that automixis in other systems is supported by both microsatellite and NGS data in the abstract of our manuscript. The references have been included in the main text.

Ln 42 - Evidence suggesting that isolation from males was not a pre-requisite for FP has previously been reported in snakes.

See: Booth et al. 2011. Evidence for viable, non-clonal but fatherless Boa constrictors. Biology Letters. 7, 253-256.

Booth et al. Facultative parthenogenesis discovered in wild vertebrates. Biology Letters. 8, 983-985.

Booth et al. 2014. New insights on facultative parthenogenesis in pythons. Biol J Linn Soc. 112, 461-468.

Despite the prior evidence to the contrary cited by the reviewer, it is still a commonly held belief among scientists and science journalists that isolation from males promotes or triggers FP. We have placed our findings in the context of other studies, including those mentioned above, that came to the same conclusion that isolation from mating partners is not a requirement for FP. We thank the reviewer for the additional citations, which are now included in the discussion section.

Ln 48 - Is this really an argument. While an immediate transition to homozygosity will purge some deleterious alleles, given the genome-wide nature of this, there will also conversely have been strong selection for mildly deleterious alleles.

Even though many FP animals have congenital defects, our data, combined with that of others, show that seemingly healthy animals arise as well. Even if these healthy animals harbor slightly deleterious alleles, the most detrimental alleles would have therefore been purged especially for subsequent generations. We have modified the abstract to be clearer: “Conversely, for animals that develop normally, FP exerts strong purifying selection as all lethal recessive alleles are purged in one generation.”

Ln 56 - I would recommend the inclusion of both Allen et al. 2018. R. Soc. Open Sci, and Card et al. 2021. Sci Reports, here, as they are members of the elapids, not represented in the other examples.

These two citations have been added.

Ln 60 - Recent studies have highlighted the significance of sperm storage in reptiles. For example, Levine et al. 2021. Exceptional long-term sperm storage by a female vertebrate. PLos ONE. 16(6).e0252049, describe the storage of sperm by a female rattlesnake for ~70 months, with two instances of its utilization to produce healthy offspring during that period. Clearly, molecular tools are providing both support for long-term sperm storage, and an understanding of its utilization.

Recent work has indeed provided new evidence for instances of long-term sperm storage and the two mechanisms are no longer competing hypotheses, but it is clear that both mechanisms exist in nature. We have modified the text accordingly to include “Nevertheless, clear examples of long-term sperm storage have also been documented in the recent literature (29), underscoring the need for molecular methods such as MS analysis or sequencing data to elucidate the underlying mechanisms.”

Ln 68 - American Crocodile would also be suitable to include here.

This has now been included in the list of examples of endangered species.

Ln71 - The problem with this hypothesis is that parthenogens produced through FP tend to have very low viability. For example, Adams et al. 2023. Endangered Species Research, follow a cohort of sharks produced through FP and all survive. Similarly low levels of survival are reported across other systems for which FP was reported. More likely, FP is simply a neutral trait. The mother is not negatively impacted through producing parthenogens and can go on to produce sexual offspring. Few instances report successful reproduction of a parthenogen. See pers. Comm in Card et al. 2021. And Straube et al. 2016.

We thank the reviewer for the comment and agree that more data on the successful reproduction of parthenotes are needed to claim that FP is an adaptive trait. We have modified the text to include that studies on “the successful reproduction by FP offspring” are needed to support this hypothesis and have included the Straube et al. 2016 citation. We decided to omit the Card et al. 2021 citation as the reports of second-generation FP was through personal communication mentioned in this study and the results themselves have not yet been published.

Ln 79 - I doubt that there is a desperate need for this for conservation. However, I think there is a need to simply further our understanding of basic biological function, given that it is not uncommon, and is phylogenetically widespread in species lacking genomic imprinting.

We agree that understanding FP as a basic biological function is important in light of the realization that it occurs more commonly than previously thought. We have added this aspect to the text: “A better understanding of the triggers and molecular mechanisms underlying FP and the fitness of the resulting offspring are therefore needed in a variety of contexts. These include: to understand a fundamental biological mechanism and its significance in vertebrate evolution, to aid in conservation efforts including captive breeding programs, and to possibly harness FP in an agricultural context (28).”

Ln 85 - It would be worth citing Card et al. 2021., here given that they used genome-wide ddRAD markers to show support for terminal fusion.

The citation has been added.

Ln 91 - Better citations here are Card et al. 2021. Allen et al. 2018, and Booth et al. 2023, which all utilize either RADseq or WGS.

These citations have been added.

Ln 95 - The conclusion of genome duplication here was supported only by a small number of microsatellite loci. As such, given that terminal fusion has been supported through genome-wide markers in other species of snakes and crocodiles, the conclusion of genome duplication is likely incorrect.

In light of the other examples that show terminal fusion in snakes, we have removed this sentence.

Ln 96 - I would strongly disagree with this statement. Allen et al. 2018, Card et al. 2021, Booth et al. 2023, all provide evidence of heterozygous loci and thus support terminal fusion. While no species-specific chromosome level reference genome is available for any of these species, the fact that levels of heterozygosity are below 33% percent supports terminal fusion. Rates over 33% support central fusion, but have not been reported in any vertebrate to date. AS such, I would recommend the removal of this statement.

We agree that the studies listed by the reviewer all support terminal fusion in snakes and crocodiles and therefore, we have removed the statement.

Ln 121 - Recent work in Drosophila mercatorum and D. melanogaster suggest that three genes play a role in the activation of FP in unfertilized eggs. In this case, through the fusion of meiotic products. That said, it is plausible to assume that FP in these lizards has an underlying genomic mechanism that is not related to isolation from males. See Sperling et al. 2023. Current Biology. 33, P3545-P3560.E13.

Clearly isolation from males is not a key trigger in FP in whiptail lizards and other vertebrate species. With recent work from Sperling et al. 2023 and the fact that selection has led to increases in parthenogenesis in birds, an underlying genetic mechanism may well be at play. We have cited and addressed this in the discussion and propose identifying the genetic basis for FP in whiptail lizards in future studies.

“Recent work identifying key cell cycle genes inducing FP in two species of Drosophila (71) and selection resulting in higher incidences of parthenogenesis in birds (24, 33) suggest a genetic basis for the initiation of FP. [...] Additional whole-genome sequencing data for species with documented FP will aid in the understanding the genetic basis, propensity, and evolutionary significance of FP.”

Ln 126 - While these data strongly support FP of the two unusual A. marmoratus appearing offspring, can long term sperm storage be ruled out. Either through captive history or allelic exclusion of other males in the group?

We have added the following sentence to the text: “Given that all of these offspring are female, inherited only maternal alleles, and animal 122 had no history of being housed with a conspecific male during its lifetime, both interspecific hybridization and long-term sperm storage are all but ruled out and FP is strongly supported.”

Ln 171 - 191 - Given that the topic of this manuscript is the genomic mechanism underlying FP in this species, are these data necessary? These are not discussed later and as such I would recommend that they are moved supplemental material. Otherwise, they simply clutter that manuscript and detract from the key question. Indeed, they are important to show that the genome constructed is of high quality, but online Supp Mat is the place for that here.

We chose to keep this section in the main text for the following reasons: There is still a lack of published reference quality genomes for many reptile species and therefore we want to highlight that this A. marmoratus reference adds not only to the understanding of FP, but also expands the small list of reptile genomes and makes the first Aspidoscelis genome available to the community. The high quality and contiguity of the genome (as indicated by the high N50 value and BUSCO score) is important to emphasize in the main text because the absence of any heterozygous regions in FP animals supports a mechanism of post-meiotic genome duplication. We would not want to bury these key points in the supplement.

Ln 296 - Comparable estimates were made for parthenogenetic production in wild populations of two North American pitviper species. See Booth et al. 2012. Biology Letters.

In Booth et al. 2012, 2 out of 59 litters of the two pitvipers (3.39%) were identified to contain FP offspring and these results are very similar to our reported rate of FP in whiptail lizards. We have now included this similarity in our discussion. “Interestingly, these rates are similar to what has been reported for wild populations of two North American pitviper species (10)”.

Ln 312 - Again, can this really be suggested? Above, the authors state that most FP animals that hatched had congenital defects, and a large number failed to hatch. This does not sound like strong support for generating individuals that counter the effects of population bottlenecks and inbreeding depression. The authors need to take this study further and monitor the long-term viability of the FP individuals that survive.

We agree with the reviewer that the adaptive advantages of FP reproduction are dependent on the fitness and reproductive potential of FP offspring and present data is insufficient to clearly support this notion. We have modified the text to include that long-term studies are needed to support or refute this hypothesis: “However, support for this hypothesis is predicated on the fitness and reproduction of FP offspring and therefore more long-term studies on seemingly healthy individuals of FP origin are needed.”

Ln 348 - To be able to provide support for this, you need to track animals long term to understand their reproductive competence, and that of their offspring.

We have added the text: “To assess whether the co-occurrence of sexual and FP reproduction in vertebrates can indeed be considered a reproductive strategy rather than biological noise will require further studies to assess the reproductive competence and fecundity of offspring produced by either mode of reproduction.”

Ln 358 - But, the caveat is that the parthenogens must themselves reproduce. This must me stated.

The statement that parthenogens must be able to reproduce to support a hypothesis of FP as an adaptive trait has been added: “One must now consider the possibility that FP is an adaptive trait and that low rates of successful FP could contribute significantly to genome purification. Such a role for FP hinges on further studies demonstrating the ability of parthenogens to reproduce themselves either through further FP or sexually.”

Ln 359 - Note that FP can also fix mildly deleterious alleles. Only if it is strongly deleterious will it be lost.

We now make it clearer that selection only applies to strongly deleterious alleles.

Ln 361 - See above comments.

We have modified the text to include that “FP offspring will have low genetic load and only pass on neutral and mildly-deleterious alleles to the next generation.”

Reviewer #1 (Significance (Required)):

1. Significance:

While reports of parthenogenesis have been reported as far back as the early 1900's, it has only been over the last decade that reports are become common. Such that facultative parthenogenesis is no longer considered a rarity, but is recognized now as being relatively common and phylogenetically widespread in species that lack genomic imprinting - particularly reptiles, birds, and sharks. Reasons for this are both an increased understanding that the trait can occur, hence recognizing it as an alternative mechanism to long-term sperm storage, and the ease of using molecular approaches.

The fundamental questions of recent times have been understanding the mechanisms driving FP. Recent papers utilizing whole genome sequencing and ddRADseq have provided support for terminal fusion automixis in snakes and sharks. Here, this study provides evidence of gametic duplication in whiptails, a mechanism with an alternative outcome in regards to the levels of retained heterozygosity. As such, this study compares to the recent work of Card et al. 2021 (Scientific Reports), and Booth et al. 2023 (Biology Letters), in providing substantive advances in the field.

The audience for this will be broad. Parthenogenesis is a fascinating topic that attracts significant media attention. See the Altmetric score of recent papers on the topic, particularly Booth et al. 2023 (Altmetric score - ~3100). As such, the study will be of interest to both a broad readership, but will also be of great significance to a specialized group working on parthenogenesis. All round, an excellent paper that has promise to advance the field.

We thank reviewer 1 for this positive assessment and for putting our work into context.

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

Summary: The researchers bring together microsatellite and whole-genome sequencing data from long-term laboratory cultures of lizards to discover occasional production of parthenogenetic offspring by several species of otherwise sexually producing whiptail lizards ("facultative parthenogenesis, "FP") and to show that these FP-produced lizards have patterns of genomic homozygosity that are incompatible with currently held assumptions about mechanisms of FP. Instead, the FP lizards seem to have been produced by a mechanism that results in almost complete homozygosity, likely a consequence of post-meiotic duplication of genomes from haploid unfertilized oocytes. They also show that FP offspring were produced by females housed with males and along with sexually produced offspring, counter to prevailing assumptions that FP offspring are only produced in situations where mates are not available. Many of the FP-produced offspring did not survive to hatching or had major abnormalities, consistent with a situation where this high homozygosity exposes harmful alleles. Finally, the authors used reduced-representation sequencing (RAD-seq) to survey heterozygosity in 321 wild-collected whiptail lizards from 15 species, showing evidence for strikingly low homozygosity in at least one individual and perhaps up to 5, consistent with the potential for FP in nature. These data are of broad interest in demonstrating several exciting new possibilities. Most importantly, the data hint at a different mechanism of FP than previously assumed, and one that causes immediate near-complete homozygosity. This scenario would likely lead to immediate purging of harmful recessive alleles. If the selective load of this purging wasn't insurmountably high, a lineage with a history of purging could produce FP offspring of relatively high fitness. Other exciting possibilities suggested by the data include the existence of FP even in a setting where mating occurs and in natural populations, versus just captivity.

Major Comments:

I found it difficult to impossible to sort out exactly what the researchers did and with what lizards. For example, in line 107, they refer to a "systematic MS analysis" for all individuals of gonochoristic species in their laboratory, but where are these data? Indeed, at this early spot in the paper, the introduction from here on out suddenly reads like a discussion. What would be better here would be to summarize what was known and wasn't known about the system and questions involved, why gaps in knowledge were important, and what the researchers actually did for this paper. In my opinion, the paper would be a much easier read if the researchers left the results and interpretation for later in the paper.

As a consequence of the reviewers’ comments, the text of the manuscript has undergone major revision, and we trust that reviewer 2 will find this new version far more accessible. The MS data collection of more than 1000 individuals is the subject of another ongoing study and was only mentioned peripherally here to put the identification of FP into context. As most of the MS data relates to gonochoristic reproduction and interspecific hybridization, we are only presenting the data that are directly relevant to this manuscript as part of this study. To our knowledge, there is no common repository to upload raw MS data, but we have provided the data for the FP animals and controls discussed in this paper in the Github repository (see section “Data availability”).

Even with this suggested fix, however, the data are still too inaccessible and analyses too opaque. For example, in line 202, a critical definition is laid out regarding heterozygous sites as those having "equal support" for two alleles. What do the researchers mean by "equal support"? My presumption is that this is something about equal or close to equal numbers of reads, but this definition needs to be spelled out and justified because it underpins much of the downstream analyses. A similar problem occurs in line 208-209, where the authors make a statement about limiting further analysis to positions in the genome where the coverage is "equal" to the mean sequencing depth.

We have changed the text to “we defined heterozygous sites as those having two alleles supported by an equal number of reads. This stringent requirement was chosen to limit the search to apparent heterozygous sites with strong support, decreasing the chance of false positives.”. We further look at only sites where the coverage is equal to the average sequencing depth to exclude regions where over-assembly and collapse of repetitive elements would artificially increase the coverage.

Another data/analysis issue emerges with the components of the manuscript that deal with mixoploidy. As far as I can tell, these data come from one sexually produced lizard, one FP A. marmoratus, and one FP A. arizonae. While the reports of bimodality of nuclear size are certainly interesting, the data and discussion are no more than an anecdotal case study in the absence of careful replication across multiple FP lizards and comparison to sexually produced lizards. Without these data, the conclusion that “Animals produced by facultative parthenogenesis are characterized by mixoploidy” (Figure 4 caption; also see lines 324-331) is far too strong.

We have added animal IDs to figure legends 4 and S10 to clarify that these erythrocyte staining come from two FP A. marmoratus, and one FP A. arizonae. In addition, imaging from two sexually produced control animals (1 A. marmoratus and 1 A. arizonae) have now been included in S10 (as S10B and S10D). We also have included an extra panel of flow cytometry data (new Figure 4C) as a complementary methodology for ploidy determination. Both imaging and flow cytometry support similar amounts of haploid cells. With the additional data and clarification, we hope that the reviewer agrees that the observations of mixoploidy are well beyond “anecdotal”. Nevertheless, we have changed the title for Figure 4 to “Detection of mixoploidy associated with facultative parthenogenesis.” We hope that our observations here will indeed inspire future studies to see if mixoploidy is a widespread phenomenon in FP outside of whiptails as indicated by earlier work in birds.

I had a similar reaction to the discussion of developmental abnormalities and embryonic lethality of embryos of FP origin presented in lines 263-281 (also lines 307-309). What is the baseline level of such abnormalities and the frequency of lethality in sexually produced eggs/embryos/hatchlings, and especially those produced via inbreeding? These comparisons are needed to interpret the significance of the patterns observed in the FP eggs/embryos/hatchings. Analogously, the comparison of the ovaries and germinal vesicles from one FP individual relative to one sexual individual do not tell us anything nearly so definitive as the text in lines 279-281 (also see Fig. S12 title, which is too broad of a conclusion for N = 1). This overly ambitious conclusion also underpins the discussion regarding the potentially adaptive nature of FP with respect to genome purification (lines 341-363; also see lines 47-50). If FP does not actually increase the rate of purging in FP lizards relative to inbred sexual counterparts (sounds like inbreeding is common from line 339), it seems less likely that we can view FP as adaptive at least from this perspective.

We have now included a comparison between defects seen in sexually produced animals vs FP animals: “six out of 16 FP animals (37.5%) hatched with no discernable developmental defects (Fig. S11A-B). This is in stark contrast to sexually produced animals, where over 98% of hatchlings showed no abnormalities. Additionally, most of the defects noted in sexually produced animals were less severe than in FP animals including bulges in tails or truncated digits.”

We agree that our statement on the lack of differences between sexually produced and FP animals was too general. We have modified the title of Fig. S12 from “No differences between ovaries and germinal vesicles of Aspidoscelis marmoratus produced by facultative parthenogenesis or fertilization” to "Ovaries of Aspidoscelis marmoratus FP animal 8450 and germinal vesicles of FP sister 8449 revealed no differences in structure and anatomy compared to fertile sexually reproducing animals.” Due to instant complete homozygosity, FP would indeed have a higher rate of purging than inbreeding. While one hypothesis is that FP is adaptive (in large enough populations), our intentions were to highlight the alternative that FP could be detrimental in smaller populations (that already would likely experience high inbreeding rates). We would expect inbreeding to not be common in whiptails relative to other lizards given that they tend to have large population sizes and actively range across generalist habitats.

A final data concern is with the use of liver tissue for whole-genome sequencing and reference genome assembly (lines 389-390) and then using these data and the reference genome to make conclusions about ploidy/coverage. Liver tissue is very commonly endopolyploid, meaning that coverage could be artificially high for animals for which liver (vs. tail) tissue was used for DNA extraction. In particular, it would be helpful if the researchers consider whether endopolyploidy could have affected their ability to make accurate estimation of coverage and thus, heterozygosity, when libraries generated from diploid (tail) tissues are aligned to a reference genome generated from a polyploid tissue as was done here.

This is an interesting point and indeed hepatic cells in various organisms have been documented to be polyploid. The proportion of polyploid cells though vary and as far as we are aware, all published studies on polyploid hepatocytes are in mammals (DOI: 10.1016/j.tcb.2013.06.002). Reference genomes have been generated from a variety of tissue sources and liver is commonly used. As most assemblies are for haploid genomes, polyploidy (unlike aneuploidy) does not impact the assembly quality. The reference genome was also from an animal of FP origin and therefore has genome-wide homozygosity that aids in a more contiguous genome assembly by eliminating the phasing problem. For the 10 animals sequenced, genomic DNA was derived from liver for three animals and the rest from tail tissue. The sequencing data generated from either liver or tail resulted in similar coverage levels (Figure S6) and similar levels of heterozygosity (Figure 2A). Minor Comments:

Line 410: Please explain why the BLAST cutoff was changed from the default.

The BLAST cutoff was changed from the default 1e-03 to 1e-06 to be more stringent and thereby increase confidence in the BUSCO results.

Lines 441-443: Please explain why this dataset was seemingly larger than expected.

Animal 122 was sequenced on one flow cell without any multiplexing with other samples and therefore yielded more reads than other animals sequenced. We subsampled the reads from this animal for analysis, so it is directly comparable with the other WGS data.

Line 510: The link to the Github repository was broken, so I was unable to access the code and data denoted as available here.

We apologize for the unavailability of the link at the time of review. Review Commons did not request a reviewer token. The repository will be made public upon journal acceptance. We would be happy to provide a reviewer token in the meantime upon request by Review Commons.

Figure 1, and other figures featuring comparisons of MS data across parents and offspring: The authors need to engage here with the alleles that do not match either parent here (e.g., allele 282 at MS7), explaining the likelihood that these alleles indeed represent a binning error (or, perhaps, stepwise mutation from parental allele), and these alleles should be flagged. Instead, they bin these unique alleles with the most similar parental allele without any explanation or flagged. The authors do bring this point up in Figure S1, but this issue needs to be addressed in the main text (related point: the mix of red/green in MS16 offspring appear more green than red. Is this meant to denote a probability different than 50:50? If not, the authors should adjust the shading so that this shape is half green, half red).

We have added to the figure legend that single nucleotide differences are most likely binning errors and are therefore not considered “de novo” alleles. Instead, they are assigned it to the most similar parental allele, consistent with Figure S1. The shading at MS16 has been removed so that it is consistent with Figure 3.

Figure 3: Indicate that white background for alleles means that allelic inheritance is not determinable, or use the mix of colors applied in Fig. 1 to indicate as such. Unique offspring alleles should be flagged rather than just automatically assigned to the most similar parental allele. Finally, it would be helpful if the alleles were presented within loci from the shorter to the longer alleles.

We have included in the figure legend that non-shaded alleles are those for which multiple potential parents share the same allele and the inheritance therefore remains ambiguous for this locus. Single nucleotide differences are also now addressed, and sizes are ordered from smallest to largest.

Figure S7. Indicate visually which panels indicate FP animals.

We have now indicated which animals are FP and included this in Figure S6 as well.

Fig. S13. The 5 animals that had especially low heterozygosity should be flagged. The title of this figure should be toned down in light of the tentative nature of the conclusions regarding FP in nature: low heterozygosity could instead reflect, for example, a long history of inbreeding. My reaction to the data is also that the % heterozygosity distribution for many of the species looks continuous rather than the bimodality one might expect under FP vs. sexual reproduction.

Since FP has not been further confirmed in these animals, unlike those examples from our captive colony, there could indeed be other reasons for low heterozygosity. We have changed the title of the figure from “Facultative parthenogenesis in whiptail lizards collected in nature” to the more neutral “Heterozygosity estimates of whiptail lizards collected in nature.” Since there are so relatively few animals, one would not necessarily expect a bimodal distribution to be apparent in the current data. We did show that the animal with the lowest calculated level of heterozygosity (deppii LDOR30) was a statistical outlier when compared to other individuals of the same species though. Since these animals were sampled across different locations and habitats, the effective population sizes would be assumed to be different as well, reflecting the range of heterozygosity estimates seen here. This has been made clear in the text.

Reviewer #2 (Significance (Required)):

General assessment: strengths and limitations. The paper's strengths include the combination of data from lab and natural populations, the characterization of an unexpected means of achieving FP, with dramatic genetic consequences, and the data suggesting that this type of FP is fairly common and occurs even in the context of mating.

Audience: The biological questions of relevance to these discoveries are of broad interest, and the paper is likely to garner some attention from the life sciences community as whole and the popular press.

Advance: These data fill an important knowledge gap regarding the mechanisms potentially driving FP in vertebrates, how often FP is likely to occur, and its genetic consequences. The discoveries are potentially conceptual/fundamental, though the extent to which they are ground breaking is not clear in the absence of functional characterization of how FP occurs as well as the need for more rigorous comparisons and replication that I outlined above.

We thank reviewer 2 for summarizing the strengths of this manuscript, pointing out the broad interest and stating that this work fills an important knowledge gap.

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

Summary: The occurrence of facultative parthenogenesis has been described in a number of vertebrate lineages but the underlying cytological mechanism(s) have remained largely speculative due to sparsity of data. Here, Ho & Tormey et al. provide a detailed analysis of facultative parthenogenesis in gonochoristic species of the lizard genus Aspidoscelis. They show that parthenogenesis leads to a complete loss of heterozygosity (LOH) within a single generation. They attribute the LOH to diploidization through duplication of the oocytes haploid genome after completion of meiosis. This mechanism is consistent with their finding of mixoploidy in erythrocytes of asexually produced offspring. Based on LOH the authors additionally show that facultative parthenogenesis in Aspidoscelis is not condition dependent (no developmental switch): it can occur in the presence of males, alongside with sexual reproduction in the same clutch, and both in captivity and the wild. Finally, the authors show that facultative parthenogenesis is associated with developmental aberrations, likely caused by expression of homozygous recessive deleterious mutations.

Major comments: In my opinion, this study presents a very comprehensive, careful documentation of mechanistic aspects and consequences of facultative parthenogenesis in a vertebrate. The genomic and microsatellite results leave little to no doubt that facultative parthenogenesis has led to complete LOH in Aspidoscelis. I am particularly impressed by the meticulous analysis of genomic coverage to exclude e.g. false positive heterozygosity due to merged paralogs in the assembly. I also follow the authors conclusion that a post-meiotic "gamete duplication"-like mechanism is likely causative for the LOH (and the mixoploidy of erythrocytes; but I am no expert on that). I was wondering if terminal fusion automixis together with a complete absence of recombination would be worth mentioning as an (probably very unlikely) alternative in the discussion. It would be exciting to corroborate the conclusion of diploidization by genome duplication in the future, e.g. via early embryonic DNA stainings to show the duplication "in action" (if that is practically possible)...? As for this manuscript, I suggest emphasizing the indirect nature of the evidence for the mechanism of parthenogenesis a little bit more.

We thank the reviewer for highlighting the effort that went into the genomic analysis that led us to our conclusions. In terms of terminal fusion without recombination, we argue that this is not an obvious alternative explanation as a large body of work has established that at least one crossover per homologous chromosome pair is required to advance into meiosis I in many organisms (e.g. see https://doi.org/10.3389/fcell.2021.681123) and therefore the absence of recombination would likely not produce the polar bodies necessary for automixis.

We have added to the text: “In whiptail lizards, we have not been able to examine post-meiotic oocytes as locating the post-meiotic nucleus within a large yolked egg is inherently difficult. The difficulty is compounded by the unpredictability of which eggs will undergo FP development and the need to sacrifice animals to remove eggs.”

While the genome duplication mechanism we propose is indeed indirect because we are unable to visualize developing FP embryos, the most parsimonious explanation from the whole-genome sequencing analysis is genome duplication because of the lack of heterozygous regions associated with automixis. In the text, we have made sure to state genome-wide homozygosity as the basis for our conclusion.

I agree that facultative parthenogenesis in the presence of males hints at a baseline rate of parthenogenesis without requiring a developmental switch. However, this makes it difficult to rule out that sperm played a role in activation of embryonal development (gynogenesis; however I am only aware of gynogenesis in fishes and amphibians)... maybe, the authors want to take this up in the discussion. Were the five parthenogenetic individuals for whole genome sequencing actually produced in the presence of males, too?

FP has been reported to occur in isolated females for other reptile and bird species, suggesting that sperm activation is at least not a general requirement in FP of amniotes. (Watts, et al. 2006, W. W. Olsen, S. J. Marsden 1954). In all cases in this study, the female mothers were housed with conspecific or heterospecific males. While we cannot completely rule out a non-genetic contribution of sperm in these cases, it would seem to be an unlikely explanation in light of the sperm-independent reproduction by obligate parthenogenesis in other species of whiptail lizards (unlike the sperm-dependence of all unisexual reproduction in amphibians and fish). We decided to not include speculation on sperm-dependence in this manuscript as we have no evidence in favor of it, nor is there any evidence for this in the literature relating to other amniotes. In fact, most examples of FP were reported from isolated females, most likely because offspring were not expected in those cases and prompted further analysis as to their origin.

I agree with the interpretation of the LOH in the RADseq data as a likely case of facultative parthenogenesis in the wild. However, when looking at figure S13 I noticed some bimodal looking distributions (e.g. in A. guttatus). It may be interesting for future studies to look into what factors influence heterozygosity in natural populations of Aspidoscelis (e.g. inbreeding vs parthenogenesis). Could there be different mechanisms of facultative parthenogenesis in different Aspidoscelis species explaining different LOH intensities?

The continuous nature of the data may reflect natural variation between individuals and collection at various locations with possibly different effective population sizes and levels of hybridization. Low levels of heterozygosity could be indicative of inbreeding or FP in some cases. This is important to note in future studies and we have added this to the manuscript (“Further fieldwork and analysis will be required to assess the level of FP in natural populations of gonochoristic Aspidoscelis species (and other factors that could influence the observed heterozygosity such as population size, levels of hybridization, and inbreeding) …”). While there are different mechanisms of FP in other vertebrate groups, the most parsimonious hypothesis is that within a genus, the mechanism would be the same.

The manuscript is well written, the introduction nicely explains the significance of the study, the methods are fully appropriate and the results (and supplementary results) displayed comprehensibly and in great detail. The discussion might benefit from going a bit more generally into the occurrence and mechanism of obligate asexuality in Aspidoscelis. One might e.g. speculate on whether the ability for facultative parthenogenesis in gonochoristic species has facilitated the transitions to obligate parthenogenesis in the hybrid lineages and what peculiarities might predispose Aspidoscelis to parthenogenesis (e.g. are centrioles contributed by sperm required?). In addition, I think the occurrence of LOH due to gamete duplication (facultative and obligate) in invertebrates (e.g. due to Wolbachia) is worth mentioning in the discussion: e.g. there is a similar case in facultative asexual Bacillus rossius stick insects, where the early dividing cells are haploid. Some of them diploidize via duplication later and form the embryo.

Thank you for complimenting each section of the manuscript and referring to it as well-written. Our lab has a long-standing interest in obligate parthenogenesis. While it is interesting that both obligate and facultative parthenogenesis occur alongside each other in this genus, the mechanisms appear to be fundamentally different, and we would like to focus the discussion on FP in a variety of systems and its potential implications in conservation and evolution. Parthenogenesis in general is a fascinating topic for a broad audience and not discussing another form of parthenogenesis (obligate in this case), the focus remains on FP and keeps the manuscript more accessible for non-specialists. We have included the stick insect as another example of diploid restoration through genome duplication in the discussion.

Minor comments:

39-41: I am a bit puzzled by the usage of the term "post-meiotic" to contrast the diploidization through duplication with automixis. Wouldn't one consider polar body fusion after completion of meiosis II also post-meiotic? Maybe I am just not aware of how the term is usually used in this context here...

We use the term “post-meiotic” because the restoration of an entirely homozygous diploid cell can only occur after the completion of both meiotic divisions. It is our understanding that polar body fusion and meiotic restitution after meiosis I or meiosis II are generally considered meiotic mechanisms in the specialized literature, even though polar body fusion would also occur after the meiotic divisions.

65: isn't that gynogenesis (sperm-dependent parthenogenesis) in the amazon molly?

While sperm is required for parthenogenesis in the Amazon Molly, it is an all-female species that exclusively reproduces through gynogenesis. In this case, it is considered an example of obligate parthenogenesis rather than FP.

78: the term "economically viable" may be a bit puzzling for a biologist's audience. "Economically sustainable" could be an alternative.

This has been changed.

129: the Arizona male was referred to as ID 4272 above. Here it is ID 4238?

This has been corrected. The correct ID is 4272.

218: please define over-assembly (see line 207)

The definition of “over-assembly” is collapsing paralogous loci into a single representative sequence. This is now explained in the text.

263-281: please, indicate a hatching rate/ rate of malformations of sexually produced offspring for comparison.

A comparison has been added: “This is in stark contrast to sexually produced animals, where over 98% of hatchlings had no abnormalities noted.”

333: in the haploid cells recessive deleterious mutations would be exposed in the hemizygous state but in the diploid cells in the homozygous state.

The text has been modified to reflect the difference between haploid and diploid cells.

470: please, provide more detail for the RADseq analyses (variant calling, calculation of heterozygosity etc.)

We have elaborated on the analysis in the methods.

Figure 1B: please, mention in the legend that the shown mechanisms are not exhaustive, e.g. first polar body fusion could occur right after meiosis 1 or polar body formation could be skipped completely.

This has been added.

Figure 1C: it may be interesting for non-specialists to name the distinctive morphological characters setting apart the three species in the figure legend and highlight them e.g. with arrows in the figure.

We have now included in the figure legend characteristic color patterns for each species: “(C) Photographs of Aspidoscelis arizonae with characteristic blue ventral coloration (top), A. gularis with light spots in dark fields that separate light stripes on dorsum (middle), and A. marmoratus with light and dark reticulated pattern on dorsum (bottom).” Since the descriptions are specific and apparent, we did not add arrows to the pictures.

Reviewer #3 (Significance (Required)):

Significance: The study by Ho & Tormey et al. substantially enhances the understanding of (facultative) asexuality in vertebrates. In particular, while most reports of facultative parthenogenesis in vertebrates have been attributed to a form of automixis, the authors conclusively show an instance of diploidization through genome duplication, a mechanism functionally similar to "gamete duplication". The study is novel, very comprehensive and of interest for a general audience within the field of evolutionary biology.

We thank reviewer 3 for pointing out that our study substantially enhances the understanding of asexuality in vertebrates, is very comprehensive and of interest for a general audience within

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

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Referee #3

Evidence, reproducibility and clarity

Summary:

The occurrence of facultative parthenogenesis has been described in a number of vertebrate lineages but the underlying cytological mechanism(s) have remained largely speculative due to sparsity of data. Here, Ho & Tormey et al. provide a detailed analysis of facultative parthenogenesis in gonochoristic species of the lizard genus Aspidoscelis. They show that parthenogenesis leads to a complete loss of heterozygosity (LOH) within a single generation. They attribute the LOH to diploidization through duplication of the oocytes haploid genome after completion of meiosis. This mechanism is consistent with their finding of mixoploidy in erythrocytes of asexually produced offspring. Based on LOH the authors additionally show that facultative parthenogenesis in Aspidoscelis is not condition dependent (no developmental switch): it can occur in the presence of males, alongside with sexual reproduction in the same clutch, and both in captivity and the wild. Finally, the authors show that facultative parthenogenesis is associated with developmental aberrations, likely caused by expression of homozygous recessive deleterious mutations.

Major comments:

• In my opinion, this study presents a very comprehensive, careful documentation of mechanistic aspects and consequences of facultative parthenogenesis in a vertebrate. The genomic and microsatellite results leave little to no doubt that facultative parthenogenesis has led to complete LOH in Aspidoscelis. I am particularly impressed by the meticulous analysis of genomic coverage to exclude e.g. false positive heterozygosity due to merged paralogs in the assembly. I also follow the authors conclusion that a post-meiotic "gamete duplication"-like mechanism is likely causative for the LOH (and the mixoploidy of erythrocytes; but I am no expert on that). I was wondering if terminal fusion automixis together with a complete absence of recombination would be worth mentioning as an (probably very unlikely) alternative in the discussion. It would be exciting to corroborate the conclusion of diploidization by genome duplication in the future, e.g. via early embryonic DNA stainings to show the duplication "in action" (if that is practically possible)...? As for this manuscript, I suggest emphasizing the indirect nature of the evidence for the mechanism of parthenogenesis a little bit more.

• I agree that facultative parthenogenesis in the presence of males hints at a baseline rate of parthenogenesis without requiring a developmental switch. However, this makes it difficult to rule out that sperm played a role in activation of embryonal development (gynogenesis; however I am only aware of gynogenesis in fishes and amphibians)... maybe, the authors want to take this up in the discussion. Were the five parthenogenetic individuals for whole genome sequencing actually produced in the presence of males, too?

• I agree with the interpretation of the LOH in the RADseq data as a likely case of facultative parthenogenesis in the wild. However, when looking at figure S13 I noticed some bimodal looking distributions (e.g. in A. guttatus). It may be interesting for future studies to look into what factors influence heterozygosity in natural populations of Aspidoscelis (e.g. inbreeding vs parthenogenesis). Could there be different mechanisms of facultative parthenogenesis in different Aspidoscelis species explaining different LOH intensities?

• The manuscript is well written, the introduction nicely explains the significance of the study, the methods are fully appropriate and the results (and supplementary results) displayed comprehensibly and in great detail. The discussion might benefit from going a bit more generally into the occurrence and mechanism of obligate asexuality in Aspidoscelis. One might e.g. speculate on whether the ability for facultative parthenogenesis in gonochoristic species has facilitated the transitions to obligate parthenogenesis in the hybrid lineages and what peculiarities might predispose Aspidoscelis to parthenogenesis (e.g. are centrioles contributed by sperm required?). In addition, I think the occurrence of LOH due to gamete duplication (facultative and obligate) in invertebrates (e.g. due to Wolbachia) is worth mentioning in the discussion: e.g. there is a similar case in facultative asexual Bacillus rossius stick insects, where the early dividing cells are haploid. Some of them diploidize via duplication later and form the embryo.

Minor comments:

• 39-41: I am a bit puzzled by the usage of the term "post-meiotic" to contrast the diploidization through duplication with automixis. Wouldn't one consider polar body fusion after completion of meiosis II also post-meiotic? Maybe I am just not aware of how the term is usually used in this context here...

• 65: isn't that gynogenesis (sperm-dependent parthenogenesis) in the amazon molly?

• 78: the term "economically viable" may be a bit puzzling for a biologist's audience. "Economically sustainable" could be an alternative.

• 129: the Arizona male was referred to as ID 4272 above. Here it is ID 4238?

• 218: please define over-assembly (see line 207)

• 263-281: please, indicate a hatching rate/ rate of malformations of sexually produced offspring for comparison.

• 333: in the haploid cells recessive deleterious mutations would be exposed in the hemizygous state but in the diploid cells in the homozygous state.

• 470: please, provide more detail for the RADseq analyses (variant calling, calculation of heterozygosity etc.)

• Figure 1B: please, mention in the legend that the shown mechanisms are not exhaustive, e.g. first polar body fusion could occur right after meiosis 1 or polar body formation could be skipped completely.

• Figure 1C: it may be interesting for non-specialists to name the distinctive morphological characters setting apart the three species in the figure legend and highlight them e.g. with arrows in the figure.

Significance

Significance: The study by Ho & Tormey et al. substantially enhances the understanding of (facultative) asexuality in vertebrates. In particular, while most reports of facultative parthenogenesis in vertebrates have been attributed to a form of automixis, the authors conclusively show an instance of diploidization through genome duplication, a mechanism functionally similar to "gamete duplication". The study is novel, very comprehensive and of interest for a general audience within the field of evolutionary biology.

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

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

The researchers bring together microsatellite and whole-genome sequencing data from long-term laboratory cultures of lizards to discover occasional production of parthenogenetic offspring by several species of otherwise sexually producing whiptail lizards ("facultative parthenogenesis, "FP") and to show that these FP-produced lizards have patterns of genomic homozygosity that are incompatible with currently held assumptions about mechanisms of FP. Instead, the FP lizards seem to have been produced by a mechanism that results in almost complete homozygosity, likely a consequence of post-meiotic duplication of genomes from haploid unfertilized oocytes. They also show that FP offspring were produced by females housed with males and along with sexually produced offspring, counter to prevailing assumptions that FP offspring are only produced in situations where mates are not available. Many of the FP-produced offspring did not survive to hatching or had major abnormalities, consistent with a situation where this high homozygosity exposes harmful alleles. Finally, the authors used reduced-representation sequencing (RAD-seq) to survey heterozygosity in 321 wild-collected whiptail lizards from 15 species, showing evidence for strikingly low homozygosity in at least one individual and perhaps up to 5, consistent with the potential for FP in nature. These data are of broad interest in demonstrating several exciting new possibilities. Most importantly, the data hint at a different mechanism of FP than previously assumed, and one that causes immediate near-complete homozygosity. This scenario would likely lead to immediate purging of harmful recessive alleles. If the selective load of this purging wasn't insurmountably high, a lineage with a history of purging could produce FP offspring of relatively high fitness. Other exciting possibilities suggested by the data include the existence of FP even in a setting where mating occurs and in natural populations, versus just captivity.

Major Comments:

• I found it difficult to impossible to sort out exactly what the researchers did and with what lizards. For example, in line 107, they refer to a "systematic MS analysis" for all individuals of gonochoristic species in their laboratory, but where are these data? Indeed, at this early spot in the paper, the introduction from here on out suddenly reads like a discussion. What would be better here would be to summarize what was known and wasn't known about the system and questions involved, why gaps in knowledge were important, and what the researchers actually did for this paper. In my opinion, the paper would be a much easier read if the researchers left the results and interpretation for later in the paper.

• Even with this suggested fix, however, the data are still too inaccessible and analyses too opaque. For example, in line 202, a critical definition is laid out regarding heterozygous sites as those having "equal support" for two alleles. What do the researchers mean by "equal support"? My presumption is that this is something about equal or close to equal numbers of reads, but this definition needs to be spelled out and justified because it underpins much of the downstream analyses. A similar problem occurs in line 208-209, where the authors make a statement about limiting further analysis to positions in the genome where the coverage is "equal" to the mean sequencing depth.

• Another data/analysis issue emerges with the components of the manuscript that deal with mixoploidy. As far as I can tell, these data come from one sexually produced lizard, one FP A. marmoratus, and one FP A. arizonae. While the reports of bimodality of nuclear size are certainly interesting, the data and discussion are no more than an anecdotal case study in the absence of careful replication across multiple FP lizards and comparison to sexually produced lizards. Without these data, the conclusion that "Animals produced by facultative parthenogenesis are characterized by mixoploidy" (Figure 4 caption; also see lines 324-331) is far too strong.

• I had a similar reaction to the discussion of developmental abnormalities and embryonic lethality of embryos of FP origin presented in lines 263-281 (also lines 307-309). What is the baseline level of such abnormalities and the frequency of lethality in sexually produced eggs/embryos/hatchlings, and especially those produced via inbreeding? These comparisons are needed to interpret the significance of the patterns observed in the FP eggs/embryos/hatchings. Analogously, the comparison of the ovaries and germinal vesicles from one FP individual relative to one sexual individual do not tell us anything nearly so definitive as the text in lines 279-281 (also see Fig. S12 title, which is too broad of a conclusion for N = 1). This overly ambitious conclusion also underpins the discussion regarding the potentially adaptive nature of FP with respect to genome purification (lines 341-363; also see lines 47-50). If FP does not actually increase the rate of purging in FP lizards relative to inbred sexual counterparts (sounds like inbreeding is common from line 339), it seems less likely that we can view FP as adaptive at least from this perspective.

• A final data concern is with the use of liver tissue for whole-genome sequencing and reference genome assembly (lines 389-390) and then using these data and the reference genome to make conclusions about ploidy/coverage. Liver tissue is very commonly endopolyploid, meaning that coverage could be artificially high for animals for which liver (vs. tail) tissue was used for DNA extraction. In particular, it would be helpful if the researchers consider whether endopolyploidy could have affected their ability to make accurate estimation of coverage and thus, heterozygosity, when libraries generated from diploid (tail) tissues are aligned to a reference genome generated from a polyploid tissue as was done here.

Minor Comments:

• Line 410: Please explain why the BLAST cutoff was changed from the default.

• Lines 441-443: Please explain why this dataset was seemingly larger than expected.

• Line 510: The link to the Github repository was broken, so I was unable to access the code and data denoted as available here.

• Figure 1, and other figures featuring comparisons of MS data across parents and offspring: The authors need to engage here with the alleles that do not match either parent here (e.g., allele 282 at MS7), explaining the likelihood that these alleles indeed represent a binning error (or, perhaps, stepwise mutation from parental allele), and these alleles should be flagged. Instead, they bin these unique alleles with the most similar parental allele without any explanation or flagged. The authors do bring this point up in Figure S1, but this issue needs to be addressed in the main text (related point: the mix of red/green in MS16 offspring appear more green than red. Is this meant to denote a probability different than 50:50? If not, the authors should adjust the shading so that this shape is half green, half red).

• Figure 3: Indicate that white background for alleles means that allelic inheritance is not determinable, or use the mix of colors applied in Fig. 1 to indicate as such. Unique offspring alleles should be flagged rather than just automatically assigned to the most similar parental allele. Finally, it would be helpful if the alleles were presented within loci from the shorter to the longer alleles.

• Figure S7. Indicate visually which panels indicate FP animals.

• Fig. S13. The 5 animals that had especially low heterozygosity should be flagged. The title of this figure should be toned down in light of the tentative nature of the conclusions regarding FP in nature: low heterozygosity could instead reflect, for example, a long history of inbreeding. My reaction to the data is also that the % heterozygosity distribution for many of the species looks continuous rather than the bimodality one might expect under FP vs. sexual reproduction.

Significance

General assessment: strengths and limitations. The paper's strengths include the combination of data from lab and natural populations, the characterization of an unexpected means of achieving FP, with dramatic genetic consequences, and the data suggesting that this type of FP is fairly common and occurs even in the context of mating.

Audience: The biological questions of relevance to these discoveries are of broad interest, and the paper is likely to garner some attention from the life sciences community as whole and the popular press.

Advance: These data fill an important knowledge gap regarding the mechanisms potentially driving FP in vertebrates, how often FP is likely to occur, and its genetic consequences. The discoveries are potentially conceptual/fundamental, though the extent to which they are ground breaking is not clear in the absence of functional characterization of how FP occurs as well as the need for more rigorous comparisons and replication that I outlined above.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Here Ho et al. provide strong molecular evidence for the production of facultatively parthenogenetic whiptail lizards, through a gametic duplication. As evidenced through multiple routes, including microsatellites, WGS, RADseq, and RBC ploidy, and lines of evidence from multiple specimens, this study is timely in furthering our understanding of the mechanisms underlying FP. The fundings are conclusive.

That said, I have several comments that should be addressed prior to publication. The introduction which addresses FP in other systems fails to cite several key studies that provide strongly molecular support for terminal fusion automixis. Similarly, the study pushes the idea that this is an adaptive trait, however without proving that the parthenogens can themselves reproduce, this isa moot point at this stage.

That said, my comments are minor. I found this to be an excellent study, well written, comprehensive in methodology, and one that I strongly advocate for publication.

Major comments: None.

Minor Comments: Should be addressed.

• Line 36 - However, data that supports terminal fusion are no longer restricted to microsat data. Studies utilizing RADseq and whole-genome sequencing in snakes and crocodiles have now provided further evidence supporting terminal fusion.

See: Booth et al. 2023. Discovery of facultative parthenogenesis in a new world crocodile. Biology Letters. 19, 20230129.

Card et al. 2021. Genome-wide data implicate terminal fusion automixis in king cobra facultative parthenogenesis. Scientific Reports. 11, 1-9

Allen et al. 2018. Molecular evidence for the first records of facultative parthenogenesis in elapid snakes. R. Soc. Open. Sci. 5, 171901.

• Ln 42 - Evidence suggesting that isolation from males was not a pre-requisite for FP has previously been reported in snakes.

See: Booth et al. 2011. Evidence for viable, non-clonal but fatherless Boa constrictors. Biology Letters. 7, 253-256.

Booth et al. Facultative parthenogenesis discovered in wild vertebrates. Biology Letters. 8, 983-985.

Booth et al. 2014. New insights on facultative parthenogenesis in pythons. Biol J Linn Soc. 112, 461-468.

• Ln 48 - Is this really an argument. While an immediate transition to homozygosity will purge some deleterious alleles, given the genome-wide nature of this, there will also conversely have been strong selection for mildly deleterious alleles.

• Ln 56 - I would recommend the inclusion of both Allen et al. 2018. R. Soc. Open Sci, and Card et al. 2021. Sci Reports, here, as they are members of the elapids, not represented in the other examples.

• Ln 60 - Recent studies have highlighted the significance of sperm storage in reptiles. For example, Levine et al. 2021. Exceptional long-term sperm storage by a female vertebrate. PLos ONE. 16(6).e0252049, describe the storage of sperm by a female rattlesnake for ~70 months, with two instances of its utilization to produce healthy offspring during that period. Clearly, molecular tools are providing both support for long-term sperm storage, and an understanding of its utilization.

• Ln 68 - American Crocodile would also be suitable to include here.

• Ln71 - The problem with this hypothesis is that parthenogens produced through FP tend to have very low viability. For example, Adams et al. 2023. Endangered Species Research, follow a cohort of sharks produced through FP and all survive. Similarly low levels of survival are reported across other systems for which FP was reported. More likely, FP is simply a neutral trait. The mother is not negatively impacted through producing parthenogens and can go on to produce sexual offspring. Few instances report successful reproduction of a parthenogen. See pers. Comm in Card et al. 2021. And Straube et al. 2016.

• Ln 79 - I doubt that there is a desperate need for this for conservation. However, I think there is a need to simply further our understanding of basic biological function, given that it is not uncommon, and is phylogenetically widespread in species lacking genomic imprinting.

• Ln 85 - It would be worth citing Card et al. 2021., here given that they used genome-wide ddRAD markers to show support for terminal fusion.

• Ln 91 - Better citations here are Card et al. 2021. Allen et al. 2018, and Booth et al. 2023, which all utilize either RADseq or WGS.

• Ln 95 - The conclusion of genome duplication here was supported only by a small number of microsatellite loci. As such, given that terminal fusion has been supported through genome-wide markers in other species of snakes and crocodiles, the conclusion of genome duplication is likely incorrect.

• Ln 96 - I would strongly disagree with this statement. Allen et al. 2018, Card et al. 2021, Booth et al. 2023, all provide evidence of heterozygous loci and thus support terminal fusion. While no species-specific chromosome level reference genome is available for any of these species, the fact that levels of heterozygosity are below 33% percent supports terminal fusion. Rates over 33% support central fusion, but have not been reported in any vertebrate to date. AS such, I would recommend the removal of this statement.

• Ln 121 - Recent work in Drosophila mercatorum and D. melanogaster suggest that three genes play a role in the activation of FP in unfertilized eggs. In this case, through the fusion of meiotic products. That said, it is plausible to assume that FP in these lizards has an underlying genomic mechanism that is not related to isolation from males. See Sperling et al. 2023. Current Biology. 33, P3545-P3560.E13.

• Ln 126 - While these data strongly support FP of the two unusual A. marmoratus appearing offspring, can long term sperm storage be ruled out. Either through captive history or allelic exclusion of other males in the group?

• Ln 171 - 191 - Given that the topic of this manuscript is the genomic mechanism underlying FP in this species, are these data necessary? These are not discussed later and as such I would recommend that they are moved supplemental material. Otherwise, they simply clutter that manuscript and detract from the key question. Indeed, they are important to show that the genome constructed is of high quality, but online Supp Mat is the place for that here.

• Ln 296 - Comparable estimates were made for parthenogenetic production in wild populations of two North American pitviper species. See Booth et al. 2012. Biology Letters.

• Ln 312 - Again, can this really be suggested? Above, the authors state that most FP animals that hatched had congenital defects, and a large number failed to hatch. This does not sound like strong support for generating individuals that counter the effects of population bottlenecks and inbreeding depression. The authors need to take this study further and monitor the long-term viability of the FP individuals that survive.

• Ln 348 - To be able to provide support for this, you need to track animals long term to understand their reproductive competence, and that of their offspring.

• Ln 358 - But, the caveat is that the parthenogens must themselves reproduce. This must me stated.

• Ln 359 - Note that FP can also fix mildly deleterious alleles. Only if it is strongly deleterious will it be lost.

• Ln 361 - See above comments.

Significance

Significance:

• While reports of parthenogenesis have been reported as far back as the early 1900's, it has only been over the last decade that reports are become common. Such that facultative parthenogenesis is no longer considered a rarity, but is recognized now as being relatively common and phylogenetically widespread in species that lack genomic imprinting - particularly reptiles, birds, and sharks. Reasons for this are both an increased understanding that the trait can occur, hence recognizing it as an alternative mechanism to long-term sperm storage, and the ease of using molecular approaches.

• The fundamental questions of recent times have been understanding the mechanisms driving FP. Recent papers utilizing whole genome sequencing and ddRADseq have provided support for terminal fusion automixis in snakes and sharks. Here, this study provides evidence of gametic duplication in whiptails, a mechanism with an alternative outcome in regards to the levels of retained heterozygosity. As such, this study compares to the recent work of Card et al. 2021 (Scientific Reports), and Booth et al. 2023 (Biology Letters), in providing substantive advances in the field.

• The audience for this will be broad. Parthenogenesis is a fascinating topic that attracts significant media attention. See the Altmetric score of recent papers on the topic, particularly Booth et al. 2023 (Altmetric score - ~3100). As such, the study will be of interest to both a broad readership, but will also be of great significance to a specialized group working on parthenogenesis. All round, an excellent paper that has promise to advance the field.

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Reply to the reviewers

We appreciate the thoughtful comments of the reviewers. We have revised the manuscript according to these comments as detailed below.

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

Efficient proteostasis in cells demands efficient clearing of damaged or misfolded proteins, and an important pathway involved in such clearance is the ubiquitin-proteasome pathway. In this system, proteins are tagged with ubiquitin to target them for degradation by the 26S proteasome complex. The conventional 26S proteasome complex consists of a core particle (CP or 20S proteasome) and one or two regulatory particles (RP, or 19S proteasome) to form the singly or doubly-capped proteasome, respectively. Proteasome assembly is a well-orchestrated process that requires proper stoichiometry of proteasome subunits and dedicated proteasome assembly chaperones. This is maintained by fine-tuning their transcriptional and translational regulation.

This manuscript elucidates an important aspect of how the different proteasome components are transcriptionally regulated upon denervation in mouse muscles for timely and efficiently assembling 26S proteasome. The authors present data that point out towards the model whereby a two-phase transcriptional program (early: day 3-7 and late: day 10-14) activates genes encoding proteasome subunits and assembly chaperones to boost an increase in proteasome content. This involves the coordinated functions of two transcription factors, PAX4 and alpha-PAL(Nrf1) which were important for both early and late phase of the transcriptional program. Their roles were not redundant as loss of one transcription factor was sufficient to prevent induction of various proteasome genes in muscle after denervation.

In summary, the authors report a novel bi-phasic mechanism elevating proteasome production in vivo, which involves the coordinated functions of two transcription factors, PAX4 and alpha-PAL(Nrf1).

Major points: 1) It is not clear why PAX4 and alpha-PAL(Nrf1) are both fully required for the transcriptional induction of some proteasome genes upon denervation (with good overlap), while only PAX4 is important for increased proteasome assembly. The authors speculate that this could be due to a stoichiometry problem but an alternative scenario where translation is increased upon alpha-PAL(Nrf1) inhibition would also be possible. This would explain why, for example, the induction of PSMC1 gene expression upon denervation is abolished upon alpha-PAL(Nrf1) inhibition (Fig. 5C) while the protein level is still increased (Fig. 6H). Is that also true for PSMD5 and Rpn9? Could it also be that the loss of function of alpha-PAL(Nrf1) is too detrimental for the muscle so that they induce an alternative stress response pathway increasing proteasome subunit translation?

We thank the reviewer for this comment. To better clarify this important point, we conducted further experiments to examine the differential effects between PAX4 vs. α-PALNRF1 on proteasome assembly chaperons (Fig. S4b). Our new data show that PAX4 promotes the induction of the assembly chaperone, PSMD5 (S5b) at 3 days after denervation (Fig. S4B). This induction is critical for the increase in PSMD5 protein levels because PAX4 knockout results in decreased PSMD5 protein levels at both 3 and 10 days after denervation (Fig. 4K). α-PALNRF1, however, does not affect the mRNA levels of this chaperone (Fig. S4A). This new result strengthens our conclusion that induced expression of assembly chaperones by PAX4 is key to raising proteasome levels after denervation.

We cannot rule out an indirect effect of α-PALNRF1 knock-down on protein synthesis, and therefore this potential alternative mechanism is now discussed in the text. It appears unlikely, however, that α-PALNRF1 knock-down is too detrimental to muscle as we do not find any evidence phenotypically for any type of stress or abnormalities.

2) Pax4 controls Rpt1-2 transcription and these two Rpt proteins form a pair. As Rpt4 is also regulated by Pax4, is Rpt5 also controlled by Pax4?

We believe the reviewer meant to request the data for Rpt4, because the data for Rpt5 was already included in original Fig. 4G-H. Therefore, we repeated the RT-PCR analysis of PAX4 KO mouse muscles for Rpt4 and now show that its induction requires PAX4 at 10 d after denervation, just when proteasome content is increased (Fig. 4G). At 3 d after denervation, Rpt4 induction is probably regulated by other transcription factors because its mRNA levels at this early phase were similar in muscles from WT and PAX4 KO mice (Fig. 4H). These data, strengthen our conclusions that coordinated functions of multiple transcription factors control proteasome gene expression in vivo. In future studies, we will investigate the specific mode of cooperation and mechanisms by which various transcription factors and co-factors collaborate to enhance the expression of proteasome genes in the early and delayed stages of gene expression within a living organism.

What about the assembly chaperone for these two pairs: PSMD5 and p27? It would be very interesting to know if there is a transcriptional coregulation based on proteasome assembly intermediates.

The referee raises an important point, which we also discuss in the text. We now present data showing that PAX4 promotes the induction of the assembly chaperon PSMD5 at 3 d after denervation (Fig. S4B), correlating nicely with the observed changes in protein levels of this chaperon (Fig. 4K). The expression of PSMD9 (p27) however, does not require neither PAX4 nor α-PALNRF1 (Fig. S4). Consequently, we conclude that PAX4 promotes proteasome biogenesis by promoting PSMD5 induction, and in the absence of α-PALNRF1 proteasome subunits can still efficiently assemble into the proteasomes (even though their expression is reduced), due to the induced expression and increased action of the assembly chaperone PSMD5. Our data highlight the intricacy in controlling proteasome levels, through transcriptional regulation of proteasome genes and assembly chaperones during muscle atrophy. We now further document and discuss the regulation of proteasome biogenesis by these two transcription factors in the text and Discussion (p.28).

3) Fig. 4J: PSMD5 and PSMD13 are not tested in Fig. 4A, G and H. This needs to be done if the authors want to draw the parallel mRNA-protein levels, as in their conclusion. Moreover, the protein levels seem to be much more induced than the mRNA levels, could that be due to increased translation? This could be discussed.

We accepted this thoughtful suggestion and now present the mRNA levels for PSMD5 and PSMD13 in Figs. 4A, G and H and Fig. S4. The new data does not change our conclusion that protein abundance largely correlate with the transcript levels (Figs. 2 and 4K).

The reviewer raises an important question that we hope to resolve in the future. As we point out in the revised Discussion section, “the substantial rise in protein levels compared to mRNA levels after denervation suggests potential increased protein translation due to PAX4 loss. Whether PAX4 regulates protein synthesis and thus can affect protein levels beyond gene expression are intriguing questions for future research”.

4) The conclusion is not correct in this sentence: "Moreover, analysis of innervated and 10 d denervated muscle homogenates from WT, alpha-PAL(Nrf1) KD or PAX4/alpha-PAL(Nrf1) KD mice by native gels and immunoblotting or LLVY-cleavage indicated that loss of both transcription factors is necessary to effectively block accumulation of active assembled proteasomes on denervation (Fig. 6H)". This is not correct, as the loss of PAX4 is sufficient to block accumulation of active assembled proteasomes on denervation (Fig. 4K). So, it could just be that alpha-PAL(Nrf1) KD has no effect on the induction of proteasome assembly after denervation and that all the effect of the double mutant is due to PAX4 loss. This needs to be corrected.

We thank the reviewer for this thoughtful comment. The text has been revised accordingly.

Minor points:

1) I would rephrase the sentence "baseline at 14 d after denervation and showed a sustained low mRNA levels until 28 d (Fig. 2A-F).", as the mRNA levels are still significantly higher that the basal levels for most proteasome genes. Same for the sentence: "RNA sequencing (RNA-Seq) analysis of TA muscles at 14 d after denervation indicated that expression of most proteasome genes is low at 14 d (Fig. S1)". Expression is low compared to what and not being induced doesn't mean they are low. This needs to be rephrased.

We revised the text accordingly and thank the reviewer for these suggestions.

2) Microscopy images need more explanation: define the green and red channel and what they are used for in the legend.

The legends have been updated as requested.

3) Columns have moved from the Table 2.

The tables have now been submitted as separate files.

4) Fig. S3: RT-PCR on NRF-1(NFE2L1) need to be performed to see the extent of inhibition by shRNA.

We thank the reviewer for this important comment. The data, which was added as new Fig. S3A, shows an efficient knockdown of NRF-1NFE2L1 with shNFE2L1.

5) In the sentence: "PAX4 maintaining subunit stoichiometry for increased proteasome assembly.", could it be due to the much higher levels of PSMB8, 9 and 10 immunoproteasome subunits upon alpha-PAL(Nrf1) KD (Fig. 6F)?

We addressed this aspect in Major Point #1, regarding the difference between PAX4 and α-PALNRF1; please see our response. As for the Reviewer’s comment concerning Fig. 6F, we think that the increased expression of PSMB 8, 9, and 10 in α-PALNRF1-KD compared to the double KD or PAX4 KO further suggests a distinct cooperative interaction between these transcription factors in promoting proteasome expression, assembly, and function, which we plan to thoroughly investigate in future separate studies. However, the increased expression of PSMB 8, 9, and 10 can affect the composition of the CP (by replacing their normal ounterpart), but not the RP assembly. CP and RP are known to assemble separately with their own dedicated chaperones; RP and CP then associate to complete the assembly of proteasome holoenzyme (RP-CP complex). Thus, it is unlikely that increased CP assembly alone would increase overall RP-CP assembly.

**Referees cross-commenting**

All other comments are relevant.

Reviewer #1 (Significance (Required)):

Overall, the work is impactful and timely, reporting the participation of a novel transcription factor, alpha-PAL(Nrf1), along with PAX4, in regulating the transcription of proteasome genes and the subsequent assembly of conventional proteasomes in mouse muscle upon denervation. One limitation is that alpha-PAL(Nrf1) kockdown is only inhibiting proteasome genes expression but proteasome assembly, the reason being still unknown. Most of the conclusions drawn in the manuscript are supported by the experimental data. Better understanding how proteasome homeostasis is regulated upon stressful conditions is an important fundamental aspect of proteasome biology. I would support publication of this manuscript providing the more specific concerns listed are addressed.

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

The main limitation of this study is that is based on a single model of muscle atrophy: that induced by cut of the sciatic nerve. Another one will nicely complement the findings as fasting atrophy or cancer cachexia model, to see if the two phase is recapitulated with regard to proteasome modulation.

The referee raises an interesting point, but as we explained throughout the manuscript, we did not use denervation in this study as a model for atrophy but rather as an in vivo model system to investigate mechanisms of protein degradation and proteasome homeostasis in a whole organism in vivo. The reason we selected denervation as an in vivo model for accelerated proteolysis is due to the gradual nature of muscle loss, which allows us to dissect the various phases of proteasome homeostasis effectively. Fasting, as an alternative model, is too rapid for addressing the specific questions that we asked in this study. In addition, in the rapid atrophy induced by fasting the primary physiological mechanism to increase protein degradation in vivo is believed to be through post-synthetic modification of proteasomes, rather than the production of new proteasomes (VerPlank et al., 2019). In future separate studies, we will thoroughly investigate whether the mechanisms discovered here are applicable to other types of atrophy (e.g. diabetes, aging, cancer). The obtained results will be published and fully discussed separately, in part because covering all types of atrophy within a single paper is impractical and goes beyond the scope of the current manuscript.

Another major concern is that the author do not measure over time during denervation atrophy the mRNA and protein content expression of the two transcription factors that they found crucial in the proteasome induction and assembly.

We agree with the reviewer that time course would strengthen our conclusions that the two transcription factors are important for proteasome gene induction and assembly. We have added these data showing that PAX4 (Fig. 4I) and α-PALNRF-1 (Fig. 6E) both accumulate in the nucleus at 7 d after denervation, just when proteasome content is maximal (Fig. 3A) and protein breakdown is accelerated (Cohen 2009; Volodin 2017; Aweida 2021). The mRNA levels of PAX4 were presented as original Fig. 4F and indicate that PAX4 is induced already at 3 d after denervation. We have added new RT-PCR data for α-PALNRF-1 showing that α-PALNRF-1 is induced at 7 d and 10 d after denervation (Fig. 6D).

Major and minor concerns are as follows:

Typos now and then are present all over the text, as holoemzyme shall be replaced with holoenzyme on page 9, on page 12 proteasome is misspelled on mid page, as well as cellls. By cotrast shall be corrected on page 19. References on page 22 shall be formatted.

We have corrected the typographical errors.

• reference 29 on page 7 seems out of context together with the sentences it is coupled with.

The reference is appropriately located within the text in terms of context, and precisely aligns with the sentence to which it is associated. Reference 29 (Boos 2019) describes a cellular state in which all proteasome genes rise simultaneously.

• muscle electroporation of plasmid shall be replaced by AAV9 injection that causes less inflammation and more expressing fibers

We do not understand and see no basis for the referee’s assertion that the “muscle electroporation of plasmid shall be replaced by AAV9 injection”. On the contrary, the electroporation methodology is widely used by many labs because of its many advantages. This in vivo gene transfection approach is extremely useful to study transient gene (or shRNA) effects in adult muscles, while avoiding the developmental effects of genes (or shRNA) that are often seen in transgenic or knockout animals (e.g., the inducible knockout of α-PALNRF-1 caused lethality, see Fig. 6B-C).

In addition, the electroporation technique offers great advantages from its speed and major cost savings. We have been using it routinely in our lab for in vivo studies, and articles using it from many laboratories worldwide have appeared in all major journals, e.g. see our papers in Nature Communications, J Cell Biol, PNAS, EMBO rep, and papers from late Alfred Goldberg (Harvard), Marco Sandri (Padova, Italy), Jeff Brault (Indiana Univ.) and others. In all studies included in this manuscript that involve electroporation, contrary to the reviewer’s impression, there was no damage or inflammation to the muscles, and we routinely examined histological sections. Finally, for our studies, we always use muscles that are at least ~70% transfected, which has proven adequate for observing gene effects in mouse muscle. In each experiment, transfected muscles are always compared and analyzed in parallel to control muscles (transfected with scrambled shLacz control). In fact, the validity of the in vivo electroporation technique is further confirmed herein by our investigations of transgenic inducible knock-down mice, showing similar effects on proteasome gene expression.

• the shGankyrin data shall be complemented with overexpression of the same chaperone to see the effects of proteasome expression and assembly.

We understand the reviewer’s concern but do not believe that such an experiment is necessary since it is well known and there is already extensive evidence in the literature showing that the chaperon Gankyrin is essential for proteasome assembly (Kaneko et al. Cell 137, 914–925, May 29, 2009 (DOI 10.1016/j.cell.2009.05.008). Thus, various Gankyrin mutants have often been used as an inactive control for proteasome assembly in vitro and in vivo (Kaneko et al. Cell 137, 914–925, May 29, 2009 (DOI 10.1016/j.cell.2009.05.008). In fact, Gankyrin’s known function in ensuring not only the proper subunit composition, but also proper conformation of the proteasome holoenzyme (Lu et al., Mol Cell. 2017 Jul 20;67(2):322-333.e6).

• another important transcription factor driving MuRF1 expression is Twist and it is totally ignored in the discussion, please add it.

We regret this oversight. We did not mean to slight any authors, although our major new discoveries and focus is on proteasome genes and not MuRF1. However, to satisfy the reviewer, we now discuss in the text Twist and other transcription factors (including SMAD2/3, glucocorticoid receptors and NFkB) capable of inducing the major atrophy-related genes (among them MuRF1).

• WB in Fig 2 shall be complemented by one in the Supp with more replicates per timepoint

We accepted this thoughtful suggestion and now present blots from additional normal and atrophying denervated mouse muscle samples as new Fig. S1B. This approach, however, does not change any of our conclusions.

• please justify why only PSMD10 (gankyrin) has been silenced and not any of the others (POMP, PSMD5, PSMD9)

We silenced PSMD10 (Gankyrin) as a representative RP assembly chaperone, since it is better characterized than the other RP assembly chaperones (PSMD5 and PSMD9). We kept POMP (a CP assembly chaperone) intact. Since the formation of one proteasome holoenzyme (RP2-CP) requires two RPs and one CP, increasing proteasome assembly is expected to be more demanding for RP assembly than CP. This led us to predict that disrupting RP assembly should be sufficient to block the induced proteasome assembly. This prediction is supported by our data (Fig. 3), and this justification was also added to the revised text to enhance clarity.

The originality is limited by the fact that Pax4 was already shown to have a role in muscle atrophy and drives the expression of p97 by the same authors. I would be curious to see if treatments in vitro know to induce the proteasome as starvation etc acts through the biphase mechanism showed in this paper, to understand how extendable to other kinds of atrophy is.

We respectfully disagree that the originally of the present findings is limited, because previously we validated a single proteasome subunit (Rpt1) as a target gene for PAX4 (Volodin 2017), and here we discover novel global coordination of proteasome gene expression by multiple transcription factors.

As we mention above, muscle denervation was used here as an in vivo model system of catabolic conditions. Unlike prior reports that were limited to cultured cells, our studies focus on the physiological setting in vivo to reveal mechanisms of proteasome homeostasis. In any case, regulation of proteasome gene expression by multiple transcription factors in other types of atrophy has not been investigated but is possible because common transcriptional adaptations activate protein breakdown in different types of muscle atrophy, including a coordinated induction of numerous components of the ubiquitin proteasome system (Jagoe 2002; Lecker 2004; Gomes 2001). In future independent research, we intend to investigate if the two-phase mechanism reported here can in fact be generalized to other atrophy (or stress) conditions.

Reviewer #2 (Significance (Required)):

The authors Gilda and co-workers made a great attempt to dissect the induction of proteasome activity during denervation muscle atrophy and discovered a two-phase process which involves two transcription factors Pax4 and NRF1. The manuscript is clearly written and the experiments fully delineated.

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

Using denervated mouse muscle as a model, Gilda et al. demonstrated that a two-step transcriptional program operates in the process of muscle atrophy after denervation and that proteasome expression-induced enhancement of protein degradation is important. Gilda et al. clarified that the transcription factors PAX4 and PAL/NRF-1 act on this proteasome expression induction and that the induction of these transcription factors and the expression induction of the proteasome gene cluster after denervation are necessary for muscle atrophy using an in vivo mouse model. The experiments were logically designed, and the results presented are considered clear and reliable. However, some of the descriptions in the text lack accuracy and courtesy, and some experiments require additional data to support and strengthen the author's claims. In particular, it is unclear whether PAX4, FOXO3, and NRF-1 work together or whether they have distinct functions. Although the authors claim that there are two stages of proteasome expression induction after denervation, this remains unclear. The authors should clarify the differences in target sequence or target genes and the substitutability of each transcription factor.

Major comments: 1: In Figure 3A, the results of the immunoblot of SDS-PAGE against 20S proteasome subunits should also be shown to confirm the increase in proteasome activity and amount.

We would like to clarify this aspect. We show the increased levels of proteasome holoenzyme complex (RP2-CP) by immunoblotting of the native gel, rather than SDS-PAGE gel. This is because the blots of the native gel can assess the levels of the actual proteasome complex, not simply subunit levels in their denatured state as in SDS-PAGE; SDS-PAGE cannot distinguish between free subunits and ones that are incorporated into the proteasome.

If proteasome activity was increased due to some other mechanisms, proteasome levels would remain relatively constant, while proteasome activity would have increased. However, this is not the case here since our data demonstrates that both RP2-CP activities and levels peak at day 7. Furthermore, the in-gel peptidase assay (Fig. 3A panel b) directly tests the 20S CP activity within the proteasome holoenzyme (RP2-CP complex) using the fluorogenic model substrate, LLVY-AMC. The 20S CP is activated for substrate degradation, only upon its association with RP (RP2-CP complex), since RP opens the substrate entry gate of the 20S. Free 20S itself is inactive, as its gate for substrate entry is closed; for this reason, free 20S can be detected, only after its substrate entry gate is artificially opened by SDS (see free 20S in panel b, but not in panel a).

2: In Figure 3, the reviewer assumed the conflict between the results of peptidase activity and SDS-PAGE in 14d. Therefore, quantification and statistical analysis should be performed on the results of proteasome peptidase activity and immunoblots to clarify the relationships between proteasome activity and amounts. Immunoblotting against ubiquitin is also needed to confirm the requirement and efficiency of proteasome induction.

As the reviewer pointed out, it might seem discrepant that peptidase activity at 14 d denervation is lower than its peak at 7d (Fig. 3A, panel a), but SDS-PAGE signal for proteasome subunits seems still high (Fig. 3A, panel d, Rpn2). SDS-PAGE detects total cellular content of proteasome subunits (free subunits as well as ones assembled within proteasomes). However, at any given moment, these subunits are not only in the proteasome holoenzyme complex, but also in different assembly intermediates. When proteasome subunits are transcriptionally induced as in this study, proteasome assembly process is also increased. However, proteasome assembly is a multi-step process, and the fold-induction for each specific subunit is different (Fig. 2A-B). This means that the rate of a certain assembly step would be differently affected for a given subunit, depending on their fold-induction. For this reason, some subunits seem to exist at a high level at 14d (e.g. Fig. 3A, panel d, Rpn2), but they are not yet incorporated into the proteasome complex, because they might be still undergoing assembly process.

As for the ubiquitin blot, it can be a good indicator for proteasome activity, when proteasome activity is decreased than normal. In such situations, ubiquitinated proteins accumulate (i.e. their signals increase as compared to control), due to their deficient degradation. However, our present study pertains to the opposite situation, where proteasome activity is increased in degrading ubiquitinated proteins. In normal cells, ubiquitinated proteins are hardly detectable due to their rapid degradation. Thus, when proteasome activity is greater than normal, ubiquitinated protein levels will be further decreased than normal. Data become unreliable when the signals are below the detection threshold. For this reason, we provided functional readouts involving the number of muscle fibers (for example, Fig. 3D).

3: In Figure 3C, the sample labels of shGankyrin and shLacZ are repeated. Would it be mislabeled?　In addition, NATIVE PAGE immunoblot analysis against Gankyrin and proteasome subunits are needed to prove the knockdown efficiency and to reveal the assembly defect of proteasome by Gankyrin knockdown.

To present our findings more clearly, we show one of each sample in the revised figure, rather than the duplicates as in the previous figure (Fig. 3C). We also included the immunoblot data to show that Gankyrin knockdown disrupts proteasome assembly, as seen by the reduced proteasome complex activity and level (Fig. 3C, panels a, b, c, lane 3, see RP2-CP). In Gankyrin knockdown samples, proteasome holoenzyme complex exhibited smeary appearance (Fig. 3C, panel c, see bracketed region in lane 3), as opposed to a discrete band in the controls (lanes 1, 2). This smeary appearance reflects more heterogeneous proteasome populations, due to defects in their composition and/or conformation. This is in line with Gankyrin’s known function in ensuring not only the proper subunit composition, but also proper conformation of the proteasome holoenzyme (Lu et al., Mol Cell. 2017 Jul 20;67(2):322-333.e6).

4: In Figures 4A, 4G, 4H, 4J, and 4K, the results of shPAX4 against innervated muscle should be shown to estimate the contribution of PAX4 in steady-state conditions. To clarify the innervated muscle-specific function of PAX4, histological analysis and quantification of proteasome gene expression in multiple organs in PAX4 KO mice are needed.

The reviewer raises an interesting point, but as we explained above, we concentrate here on the major new discovery that multiple transcription factors increase proteasome content in a catabolic condition in vivo, correlating directly with the accelerated protein loss. Regulation of the basal levels of proteasome in normal conditions in various types of cells and tissues is certainly an important issue meriting in depth study and will be the subject for future studies, but it is beyond the scope of this lengthy paper. This point is now discussed in the revised text.

The tissue distribution of PAX4 and the detailed description of the phenotype of KO mice are also needed to understand and evaluate the role of PAX4 in muscle.

We added the requested data about PAX4 distribution as Fig. 4I. These data shows that PAX4 accumulates in the nucleus already at 3 d after denervation. Furthermore, we are happy to add further information about the knock-out mouse model. The requested information and a detailed description of how PAX4 KO mice were generated were added to the text. The PAX4 KO mice showed no abnormalities and did not appear in any way different from the wild type littermates.

5: In Figure 4C, immunoblot analysis against PAX4 is essential to confirm the PAX4 protein knockout.

We agree and representative blots were added to Fig. 4C.

6: In Figure 5, peptidase activity and immunoblotting in NATIVE PAGE are needed to reveal the contribution of FOXO3 and NRF-1 in denervated muscle as shown in Figure 4.

The requested data for FOXO3 using FOXO3 dominant negative (as in Fig. 5A-B) were added as new Fig. 5C-D, showing no effect on proteasome content by FOXO3 inhibition. These new data are consistent with our findings that the expression of only two proteasome subunit genes was affected by FOXO3 inhibition at 10 d after denervation (Fig. 5B). The data for α-PALNRF-1 and the effects of its knockdown on proteasome content and activity were shown as original Fig. 6H (now Fig. 6J).

The expression of FOXO3 and NRF-1 should also be shown by RT-PCR and immunoblotting as shown in Figure 4.

We thank the reviewer for this thoughtful suggestion, and as requested, we now show representative blots of transfected muscles to support the graphical data (Figs. 5C-F). These data confirm the efficient expression of HA-FOXO3ΔC or FLAG-α-PALNRF-1 dominant negative inhibitors in transfected muscles. It is important to note that these inhibitors are mutant forms designed to interfere with the normal function of the wild-type endogenous FOXO3 or α-PALNRF-1 proteins, without affecting their transcript levels. Given this mechanism, we believe that Western blotting is a more appropriate technique for assessing their impact, as it provides direct insights into protein expression. In the revised main text and methods, we have now clarified this point.

Similar to previous comments, the expression of the dominant negative form of Foxo3 and NRF-1 should be performed in innervated muscles to reveal the significance and specificity of Foxo3 and NRF-1 function in denervated muscles.

As mentioned above, regulation of the normal basal levels of proteasomes is certainly an important issue meriting in depth study and will be the subject for future studies, but it is beyond the scope of this lengthy paper, which focuses on the mechanisms increasing protein content in catabolic conditions in vivo. With respect to FOXOs, there is a large literature on its regulation and roles in normal muscle (please see papers by late Alfred L Goldberg, Marco Sandri and others). Under normal conditions FOXO3 is largely inactive via phosphorylation by insulin-PI3K-AKT signaling (Stitt 2004; Latres 2005; Zhao 2007).

7: In Figure 6D, the list of genes should be served especially about 27 genes and 69 genes that show common features between NRF-1 KD and PAX4 KO.

The requested data is now presented as new Table 4.

8: In Figure 6F, the list of genes that change expression in PAX4 and NRF-1 KD mice is needed.

We agree and the requested data has now been added to table 5.

9: In Figure 6H, immunoblotting against ubiquitin is needed to evaluate the contribution of proteasome induction to protein degradation.

We clarified this aspect in the Major Point #2. Please see our response.

10: This study lacks the detailed mechanisms by which PAX4, Foxo3, and NRF-1 regulate the expression of proteasome genes. The contribution of these transcription factors is revealed by experiments, but the specific sequence that these transcription factors bind and how transcription factors are induced in denervated muscles is not clarified. As shown in the figures, the ChIP assay provides convincing results, but the detailed sequence or map of the promoter region of proteasome genes must be shown in the figures to clarify the target sequences of NFE2L1 and PAX4, FOXO3, and NRF-1. In addition, the luciferase assay would support the results of the ChIP assay.

Again, the reviewer raises an important question that we plan to resolve in the future. As mentioned, our findings strongly suggest a novel coordinated mechanism involving multiple transcription factors that control proteasome content in catabolic states in vivo. The enclosed revised manuscript primarily focuses on elucidating the contributions of individual transcription factors (α-PALNRF-1, PAX4, NRF-1NFE2L1 and FOXO3) to the induction of proteasome genes, revealing a significant overlap in genes regulated by multiple transcription factors. The specific mode of cooperation among these and other transcription factors and cofactors is certainly an important question for future studies, but it is beyond the scope of this lengthy paper. In the revised text we have now clarified this point (page 27). In addition, we agree that clarifying how the transcription factors are induced in denervated muscles merits some considerations and a paragraph was added to the Discussion (page 26) concerning possible mechanisms. For example, it is possible that the transcription factor STAT3 is involved in PAX4 induction because, based on previous microarray and ChIP data in cultured NIH3T3 cells, PAX4 was identified as a target gene of STAT3 (Snyder et al., 2008), and STAT3 becomes activated after denervation (Madaro et al., 2018).

We are delighted that the reviewer found the results obtained through the ChIP assay convincing. Given the extensive scope of our investigation and rigorous analyses of dozens of genes, it is not feasible to generate luciferase-encoding plasmids for all of them. However, in response to the reviewer's request, we have carried out predictions of the binding sites of the 4 transcription factors within the minimal promoter regions (300 up- and 1000 down-stream to TSS) of the 64 proteasome sequences. The predicted binding sites are now listed in Table 2A-D. These new data further support our key findings that multiple transcription factors control proteasome gene expression in a catabolic physiological state in vivo.

11: The results of the loss of transcription factors are well done, but the authors should also try to estimate the effect of overexpression of transcription factors in muscle. If the overexpressed transcription factors cause proteasome induction and muscle fiber mass reduction, these results strongly support the importance of transcription factor-mediated proteasome enhancement.

We understand the reviewer’s comment but do not believe that such an experiment is necessary to support our key findings about proteasome gene induction by multiple transcription factors in vivo. In fact, we have specifically refrained from pursuing overexpression studies in this context due to the apparent coordination and some potential interdependence between the functions of PAX4 and α-PALNRF-1 transcription factors in inducing proteasome genes. Manipulating one specific gene through overexpression could potentially disrupt this delicate coordination and yield misleading results.

In addition, there are several limitations of gene overexpression in mouse muscle, as it may not be as efficient and does not represent physiological conditions. Therefore, to validate gene functions in a physiological setting in vivo, we generated transgenic animals with the gene of interest specifically knocked-out or knocked-down. Utilizing transgenic mice lacking the gene of interest, though time-consuming, is a widely accepted and common approach that proves to be the most suitable method for specifically demonstrating the involvement of a particular gene in a physiological process, enabling a targeted and controlled investigation of its role and providing valuable insights into its contribution to the observed effects.

Minor comments:

12: The authors should describe the inducible KO mice more carefully and correctly. In the Results section on P12, the description of "whole body Cre+ mice" confuses the readers in understanding the mechanism of inducible Cre-mediated KO.

We agree and have added the information requested about the KO mice to the main text and a detailed description in the methods section.

13: In Figures 6B and 6C, the number of mice and the meaning of the asterisk should be described correctly. Is it statistically significant?

We agree. By accident the number of mice and sign for statistical significance were omitted during processing. The correct sign was added to Fig. 6B-C, and the number of mice used, and the meaning of asterisks were added to the corresponding legend. N=10 mice per condition. **, P

14: There is no description of Figure 6E in the manuscript. The authors should include it.

In the original version of this paper, we refer to Fig. 6E in the text on pages 21 and 25. Also, the presented illustration is fully described in the corresponding legend.

Reviewer #3 (Significance (Required)):

This paper clarified a novel mechanism of proteasome induction by transcription factors in denervated muscles other than Nrf1 (NFE2L1), which has been shown to contribute to the induction of proteasome gene expression in cultured cells. This is an important paper for expanding the understanding of the field. It is also important because it has demonstrated the potential for new therapeutic targets in diseases such as type 2 diabetes and cancer.

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Referee #3

Evidence, reproducibility and clarity

Using denervated mouse muscle as a model, Gilda et al. demonstrated that a two-step transcriptional program operates in the process of muscle atrophy after denervation and that proteasome expression-induced enhancement of protein degradation is important. Gilda et al. clarified that the transcription factors PAX4 and PAL/NRF-1 act on this proteasome expression induction and that the induction of these transcription factors and the expression induction of the proteasome gene cluster after denervation are necessary for muscle atrophy using an in vivo mouse model. The experiments were logically designed, and the results presented are considered clear and reliable. However, some of the descriptions in the text lack accuracy and courtesy, and some experiments require additional data to support and strengthen the author's claims. In particular, it is unclear whether PAX4, FOXO3, and NRF-1 work together or whether they have distinct functions. Although the authors claim that there are two stages of proteasome expression induction after denervation, this remains unclear. The authors should clarify the differences in target sequence or target genes and the substitutability of each transcription factor.

Major comments:

1. In Figure 3A, the results of the immunoblot of SDS-PAGE against 20S proteasome subunits should also be shown to confirm the increase in proteasome activity and amount.
2. In Figure 3, the reviewer assumed the conflict between the results of peptidase activity and SDS-PAGE in 14d. Therefore, quantification and statistical analysis should be performed on the results of proteasome peptidase activity and immunoblots to clarify the relationships between proteasome activity and amounts. Immunoblotting against ubiquitin is also needed to confirm the requirement and efficiency of proteasome induction.
3. In Figure 3C, the sample labels of shGankyrin and shLacZ are repeated. Would it be mislabeled?　In addition, NATIVE PAGE immunoblot analysis against Gankyrin and proteasome subunits are needed to prove the knockdown efficiency and to reveal the assembly defect of proteasome by Gankyrin knockdown.
4. In Figures 4A, 4G, 4H, 4J, and 4K, the results of shPAX4 against innervated muscle should be shown to estimate the contribution of PAX4 in steady-state conditions. To clarify the innervated muscle-specific function of PAX4, histological analysis and quantification of proteasome gene expression in multiple organs in PAX4 KO mice are needed. The tissue distribution of PAX4 and the detailed description of the phenotype of KO mice are also needed to understand and evaluate the role of PAX4 in muscle.
5. In Figure 4C, immunoblot analysis against PAX4 is essential to confirm the PAX4 protein knockout.
6. In Figure 5, peptidase activity and immunoblotting in NATIVE PAGE are needed to reveal the contribution of FOXO3 and NRF-1 in denervated muscle as shown in Figure 4. The expression of FOXO3 and NRF-1 should also be shown by RT-PCR and immunoblotting as shown in Figure 4. Similar to previous comments, the expression of the dominant negative form of Foxo3 and NRF-1 should be performed in innervated muscles to reveal the significance and specificity of Foxo3 and NRF-1 function in denervated muscles.
7. In Figure 6D, the list of genes should be served especially about 27 genes and 69 genes that show common features between NRF-1 KD and PAX4 KO.
8. In Figure 6F, the list of genes that change expression in PAX4 and NRF-1 KD mice is needed.
9. In Figure 6H, immunoblotting against ubiquitin is needed to evaluate the contribution of proteasome induction to protein degradation.
10. This study lacks the detailed mechanisms by which PAX4, Foxo3, and NRF-1 regulate the expression of proteasome genes. The contribution of these transcription factors is revealed by experiments, but the specific sequence that these transcription factors bind and how transcription factors are induced in denervated muscles is not clarified. As shown in the figures, the ChIP assay provides convincing results, but the detailed sequence or map of the promoter region of proteasome genes must be shown in the figures to clarify the target sequences of NFE2L1 and PAX4, FOXO3, and NRF-1. In addition, the luciferase assay would support the results of the ChIP assay.
11. The results of the loss of transcription factors are well done, but the authors should also try to estimate the effect of overexpression of transcription factors in muscle. If the overexpressed transcription factors cause proteasome induction and muscle fiber mass reduction, these results strongly support the importance of transcription factor-mediated proteasome enhancement.

Minor comments:

1. The authors should describe the inducible KO mice more carefully and correctly. In the Results section on P12, the description of "whole body Cre+ mice" confuses the readers in understanding the mechanism of inducible Cre-mediated KO.
2. In Figures 6B and 6C, the number of mice and the meaning of the asterisk should be described correctly. Is it statistically significant?
3. There is no description of Figure 6E in the manuscript. The authors should include it.

Significance

This paper clarified a novel mechanism of proteasome induction by transcription factors in denervated muscles other than Nrf1 (NFE2L1), which has been shown to contribute to the induction of proteasome gene expression in cultured cells. This is an important paper for expanding the understanding of the field. It is also important because it has demonstrated the potential for new therapeutic targets in diseases such as type 2 diabetes and cancer.

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Referee #2

Evidence, reproducibility and clarity

The main limitation of this study is that is based on a single model of muscle atrophy: that induced by cut of the sciatic nerve. Another one will nicely complement the findings as fasting atrophy or cancer cachexia model, to see if the two phase is recapitulated with regard to proteasome modulation.

Another major concern is that the author do not measure over time during denervation atrophy the mRNA and protein content expression of the two transcription factors that they found crucial in the proteasome induction and assembly.

Major and minor concerns are as follows:

Typos now and then are present all over the text, as holoemzyme shall be replaced with holoenzyme on page 9, on page 12 proteasome is misspelled on mid page, as well as cellls. By cotrast shall be corrected on page 19. References on page 22 shall be formatted.

• reference 29 on page 7 seems out of context together with the sentences it is coupled with.
• muscle electroporation of plasmid shall be replaced by AAV9 injection that causes less inflammation and more expressing fibers
• the shGankyrin data shall be complemented with overexpression of the same chaperone to see the effects of proteasome expression and assembly
• another important transcription factor driving MuRF1 expression is Twist and it is totally ignored in the discussion, please add it.
• WB in Fig 2 shall be complemented by one in the Supp with more replicates per timepoint
• please justify why only PSMD10 (gankyrin) has been silenced and not any of the others (POMP, PSMD5, PSMD9)

The originality is limited by the fact that Pax4 was already shown to have a role in muscle atrophy and drives the expression of p97 by the same authors. I would be curious to see if treatments in vitro know to induce the proteasome as starvation etc acts through the biphase mechanism showed in this paper, to understand how extendable to other kinds of atrophy is.

Significance

The authors Gilda and co-workers made a great attempt to dissect the induction of proteasome activity during denervation muscle atrophy and discovered a two-phase process which involves two transcription factors Pax4 and NRF1. The manuscript is clearly written and the experiments fully delineated.

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Referee #1

Evidence, reproducibility and clarity

Efficient proteostasis in cells demands efficient clearing of damaged or misfolded proteins, and an important pathway involved in such clearance is the ubiquitin-proteasome pathway. In this system, proteins are tagged with ubiquitin to target them for degradation by the 26S proteasome complex. The conventional 26S proteasome complex consists of a core particle (CP or 20S proteasome) and one or two regulatory particles (RP, or 19S proteasome) to form the singly or doubly-capped proteasome, respectively. Proteasome assembly is a well-orchestrated process that requires proper stoichiometry of proteasome subunits and dedicated proteasome assembly chaperones. This is maintained by fine-tuning their transcriptional and translational regulation.

This manuscript elucidates an important aspect of how the different proteasome components are transcriptionally regulated upon denervation in mouse muscles for timely and efficiently assembling 26S proteasome. The authors present data that point out towards the model whereby a two-phase transcriptional program (early: day 3-7 and late: day 10-14) activates genes encoding proteasome subunits and assembly chaperones to boost an increase in proteasome content. This involves the coordinated functions of two transcription factors, PAX4 and alpha-PAL(Nrf1) which were important for both early and late phase of the transcriptional program. Their roles were not redundant as loss of one transcription factor was sufficient to prevent induction of various proteasome genes in muscle after denervation.

In summary, the authors report a novel bi-phasic mechanism elevating proteasome production in vivo, which involves the coordinated functions of two transcription factors, PAX4 and alpha-PAL(Nrf1).

Major points:

1. It is not clear why PAX4 and alpha-PAL(Nrf1) are both fully required for the transcriptional induction of some proteasome genes upon denervation (with good overlap), while only PAX4 is important for increased proteasome assembly. The authors speculate that this could be due to a stoichiometry problem but an alternative scenario where translation is increased upon alpha-PAL(Nrf1) inhibition would also be possible. This would explain why, for example, the induction of PSMC1 gene expression upon denervation is abolished upon alpha-PAL(Nrf1) inhibition (Fig. 5C) while the protein level is still increased (Fig. 6H). Is that also true for PSMD5 and Rpn9? Could it also be that the loss of function of alpha-PAL(Nrf1) is too detrimental for the muscle so that they induce an alternative stress response pathway increasing proteasome subunit translation?
2. Pax4 controls Rpt1-2 transcription and these two Rpt proteins form a pair. As Rpt4 is also regulated by Pax4, is Rpt5 also controlled by Pax4? What about the assembly chaperone for these two pairs: PSMD5 and p27? It would be very interesting to know if there is a transcriptional coregulation based on proteasome assembly intermediates.
3. Fig. 4J: PSMD5 and PSMD13 are not tested in Fig. 4A, G and H. This needs to be done if the authors want to draw the parallel mRNA-protein levels, as in their conclusion. Moreover, the protein levels seem to be much more induced than the mRNA levels, could that be due to increased translation? This could be discussed.
4. The conclusion is not correct in this sentence: "Moreover, analysis of innervated and 10 d denervated muscle homogenates from WT, alpha-PAL(Nrf1) KD or PAX4/alpha-PAL(Nrf1) KD mice by native gels and immunoblotting or LLVY-cleavage indicated that loss of both transcription factors is necessary to effectively block accumulation of active assembled proteasomes on denervation (Fig. 6H)". This is not correct, as the loss of PAX4 is sufficient to block accumulation of active assembled proteasomes on denervation (Fig. 4K). So, it could just be that alpha-PAL(Nrf1) KD has no effect on the induction of proteasome assembly after denervation and that all the effect of the double mutant is due to PAX4 loss. This needs to be corrected.

Minor points:

1. I would rephrase the sentence "baseline at 14 d after denervation and showed a sustained low mRNA levels until 28 d (Fig. 2A-F).", as the mRNA levels are still significantly higher that the basal levels for most proteasome genes. Same for the sentence: "RNA sequencing (RNA-Seq) analysis of TA muscles at 14 d after denervation indicated that expression of most proteasome genes is low at 14 d (Fig. S1)". Expression is low compared to what and not being induced doesn't mean they are low. This needs to be rephrased.
2. Microscopy images need more explanation: define the green and red channel and what they are used for in the legend.
3. Columns have moved from the Table 2.
4. Fig. S3: RT-PCR on NRF-1(NFE2L1) need to be performed to see the extent of inhibition by shRNA.
5. In the sentence: "PAX4 maintaining subunit stoichiometry for increased proteasome assembly.", could it be due to the much higher levels of PSMB8, 9 and 10 immunoproteasome subunits upon alpha-PAL(Nrf1) KD (Fig. 6F)?

Referees cross-commenting

All other comments are relevant.

Significance

Overall, the work is impactful and timely, reporting the participation of a novel transcription factor, alpha-PAL(Nrf1), along with PAX4, in regulating the transcription of proteasome genes and the subsequent assembly of conventional proteasomes in mouse muscle upon denervation. One limitation is that alpha-PAL(Nrf1) kockdown is only inhibiting proteasome genes expression but proteasome assembly, the reason being still unknown. Most of the conclusions drawn in the manuscript are supported by the experimental data. Better understanding how proteasome homeostasis is regulated upon stressful conditions is an important fundamental aspect of proteasome biology. I would support publication of this manuscript providing the more specific concerns listed are addressed.

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Reply to the reviewers

Manuscript number: RC-2023-02199 Corresponding author(s): Cornelis, Calkhoven

1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

• *

We would like to thank the reviewers for their comments that will help to improve the manuscript and the editor(s) for taking care of the process.

Text revisions and corrections in the manuscript are in red font.

To keep oversight, see below the distribution of the comments and our replies per category:

Reviewer 1

Major comment 1: see 2. planned revisions

Major comment 2: see 3. already incorporated

Major comment 3: see 2. planned revisions

Major comment 4: see 4. prefer not to carry out

Minor comment 1: see 3. already incorporated

Minor comment 2: see 4. prefer not to carry out

Reviewer 2

Major comment 1: see 4. prefer not to carry out

Major comment 2: see 4. prefer not to carry out

Major comment 3: see 3. already incorporated

Major comment 4: see 4. prefer not to carry out

Minor comment 1: see 3. already incorporated

Minor comment 2: see 3. already incorporated

Minor comment 3: see 3. already incorporated

Minor comment 4: see 3. already incorporated

Minor comment 5: see 3. already incorporated

Reviewer 3

Major comment 1: see 3. already incorporated

Major comment 2: see 3. already incorporated

Major comment 3: see 4. prefer not to carry out

Minor comment 1: see 4. prefer not to carry out

Minor comment 2: see 4. prefer not to carry out

Significance comments by the three reviewers

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

Reviewer #1

*Major comment 1: The reviewer is not convinced that FTO-CEBPB regulation is direct (data Figure 5). *

Reply: We offer to perform immunoprecipitation of FTO from wt cells to examine interaction with CEBPB mRNA to resolve this. HPRT mRNA will be used as negative control (like in the MeRIP-RT-qPCR experiments in the manuscript).

Major comment 3: FTO effect on proliferation and migration in less aggressive / normal breast epithelial cells (data Figure 1) (reviewer writes “cancer cells” and “MCF-10A”, but these are untransformed epithelial cells).

Reply: We offer to perform proliferation and migration assays in MCF-10A wt and FTO-knockdown cells.

Reviewer #2 – see below.

Reviewer #3 – see below.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

Reviewer 1

Major comment 2: The reviewer asks to discuss the relevance of the findings for m6Am biology.

Reply: We now discuss this in the discussion session at page 18.

Here we mention that Sun et al (https://doi.org/10.1038/s41467-021-25105-5) performed m6Am-seq in HEK293T cells and detected no m6Am for C/EBPβ (Supplementary Data 2). These experiments were well controlled using m6A-IP experiments with PCIF1-KO HEK293T cells and compared with m6Am-Exo-seq and miCLIP published data.

• *

Minor comment 1: Mistake in Figure 5 legend and beyond.

Reply: Legend of Figure 5 has been updated (text in red) and data for Supplementary Figure 5 has been added, together showing that FTO-CEBPB regulation takes place in MDA-MB-231, MCF-7 and MEFs.

Reviewer 2

Major comment 3: The reviewer noticed duplication of figures in Figure 6A and Supplementary Figure 6A.

Reply: The data presented in the bar graphs of Figure 6 and Supplementary Figure 6 are from two independent experiments. Unfortunately, the pictures of the cells at the bottom for supplementary Figure 6A were the wrong ones and now are replaced by the proper pictures belonging to this experiment.

*Minor comment 1: Statistic analysis in several panels is missing. *

Reply: All significant events are clearly marked by *: p0.05).

Minor comments 2 and 3: Issues in Figure 2E.

Reply: The “E” is removed. We have included the cell type information in the panels D (MDA-MB-231) and E (MDA-MB-231 – shFTO1).

Minor comment 4: Textual description belonging by Figure 2E.

Reply: We have re-written the text describing the data, at page 6.

Minor comment 5: Missing explanation about WTAP.

Reply: We have extended the explanation about WTAP function at page 13.

Minor comment 5: Layout of images needs improvement.

Reply: we have to guess here what the reviewer means, but we have included the requested information in panels 2E and D (see under Minor comments 2 and 3).

For Figure 4 we matched colours for bars representing shFTO1 and shFTO2 throughout the figure.

In Figure 1, panel D we now label the cells as MDA-MB-231 – shTFO (instead of FTO-kd), in line with labelling throughout the paper.

In Figures 1D and 2E we now use +FTO (instead on just FTO) for clearness.

Concerning the reviewers remark under “significance”:

*From a translational point of view, it is unclear if the study is significant for the future of therapeutic applications since no experiments have been performed on normal breast cancer cells. *

Reply: We do not understand what the reviewer means with “normal breast cancer cells”, maybe the reviewer means untransformed breast epithelial cells (MCF-10A), or really breast cancer cells derived from patients?

We now added supplementary data FTO knockdown decreases C/EBPβ-LIP levels in MCF-7 (luminal A type breast cancer) and in MEFs (Supplementary Figure 5A and B). This indicates that the FTO- C/EBPβ regulation is conserved in different cell lines of different origin. Still, FTO- C/EBPβ could play a more prominent role in breast cancer with high expression of FTO correlated with high C/EBPβ-LIP levels, and the possibility to suppress this.

Reviewer 3

Major comment 1: Disconnect between findings presented in Figure 1 and Figure 5.

Reply: We have improved the reasoning at page 12.

Major comment 2: In vivo phenotype of FTO deficiency.

Reply: We already discussed the paper by Niu et al (https://doi.org/10.1186/s12943-019-1004-4) in the discussion, page 18.

We have now added information about FTO knockout and overexpression mice and how the phenotypes of FTO knockout mice and CEBPB uORF deficient mice relate to each other at page 19.

4. Description of analyses that authors prefer not to carry out

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

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

Major comment 4: To support the data on the FTO and WTAP regulation of C/EBPβ isoform expression analysis of the correlation in expression between FTO/ C/EBPβ and WTAP/ C/EBPβ could be performed using the cancer cell encyclopedia (CCLE) dependency map portal.

Reply: The CCLE map uses transcript expression data. Our observation is that mRNA-stability is not affected, but the protein C/EBPβ-LIP/-LAP ratio is. Therefore, CCLE analysis is not informative since it does not provide information on C/EBPβ-LIP/LAP protein ratios.

*Minor comment 2: For the C/EBPβ-LIP overexpression-mediated rescue of the migration phenotype of figure 6 an additional replicate for shFTO1 may be helpful as only one of the two replicates presented is statistically significant. *

Reply: Taken together the results presented in the main and supplementary figure show:

• significant downregulation of migration for all shFTO1 and shFTO2 knockdowns (EV vs. EV-shFTO1 or EV-shFTO2).

• Significant upregulation of migration in FTO-knockdown cells by ectopic LIP expression in three of the four FTO knockdown samples (shFTO1/2-EV vs. LIP).

• Significant further upregulation of migration in one of the control (scr) cells by ectopic LIP expression (scr cells EV vs. LIP).

• Throughout the experiments the observed changes in migration are consistent with shFTO knockdown and LIP expression.

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

Major comment 1: 1. The authors focused on FTO and its function of RNA demethylation but the m6A-seq is not used at all. It is not likely to find the direct down stream effector of FTO without m6A-seq if you believe demethylation is the key function of FTO.

Reply: In Figure 5A we show collective m6A sites based on experiments of others by miCLIP, DART-seq, and SRAMP prediction software. In combination with MeRIP-RT-qPCR in response to FTO KD this shows regulation of CEBPB-mRNA m6A modification by FTO, but without knowledge of the exact m6A sites affected. This study aimed to examine the way FTO affects cell proliferation and migration in different breast cancer cell lines. We revealed the FTO-C/EBPβregulation and will further examine the FTO-C/EBPβ interaction as proposed under session 2, planned revisions. Determination of specific m6Am sites in relation to the translational mechanism involved would be subject of a future study.

*Major comment 2: Related to above concerns, the authors claimed that FTO regulated C/EBPβ-LIP. But how FTO regulated the protein expression is missing. As is known to all, FTO mainly affect RNA m6A. There is a gap between C/EBPβ-LIP protein and the RNA of this gene. *

Reply: It is true we do not understand the mechanism of how m6A modification affects the differential translation of the CEBPB mRNA in the different protein isoforms. Examining this is a major effort and would take considerable time, which is beyond this study, but would be subject of further study.

*Major comment 4: The authors claimed that EMT related genes are affected upon FTO knock down, but Figure 2C do not seem to align with the EMT process. Also, if the authors believe EMT process is regulated, another GSEA enrichment panel like Figure 2B should be included. *

Reply: we have difficulty in understanding this comment. Relevance of the EMT-process is clearly shown by GSEA in panel 2B. GSEA uses a ranked list of gene expression (including all genes in the RNA-seq data set, also the ones not significantly changed in expression) and is thereby a powerful and comprehensive technique to identify relevant pathways since all data in the dataset is used. The GO-term analysis in Figure 2C looks at significantly regulated genes and maps these to GO-terms for biological process (BP), molecular function (MF) or cellular component (CC). Here we used BP, and find many GO-terms involved in ECM/cell membrane/cell adhesion/cell migration (linked to cell migration and thereby EMT since the cells are of epithelial origin). GO-term analysis only requires a list of genes that were found to be significantly regulated (It doesn’t know where your list of genes has been derived from and does not take into account the p-value of a specific gene or the fold change in expression observed between SCR and shFTO cells, in contrast to GSEA). GSEA and GO-term analysis are therefore complementary analyses based on different principles to help indicate what biological processes are changed upon FTO knock-down; their results cannot be directly compared.

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

Major comment 3: The lack of clear impact of FTO KD on the translatome is surprising. Maybe the reverse experiment (over expression) would lead to more relevant findings. Likewise, use of the mutant FTO could differentiate between the demethylase function of FTO vs other non-enzymatic functions.

Reply: Although we agree the proposed experiments are interesting, we believe them to be beyond the scope and time of this manuscript – Major point 3.

Minor comment 1: baseline FTO level in MDA MB231 seems inconsistent (1A vs 1D--controls). It would be useful to see FTO expression across breast cancer cell lines and normal mammary cells to justify choice of cell lines in which experiments were carried out.

Reply: It is due to unfortunate choice of blots with different exposures: The immunoblot in Figure 1A shows wild-type MDA-MB-231 cells with scr-shRNA with expected expression of FTO, compared to shFTO knockdowns with low expression of FTO. Figure 1D are MDA-MB-231 cells with knockdown of FTO and therefore very low FTO expression, compared to FTO knockdown cells with re-expression of FTO. The exposure was a bit unnecessary low, and we changed the blot with a higher exposure blot.

Niu et all (https://doi.org/10.1186/s12943-019-1004-4) have analysed breast cancer samples form patients and breast cancer cell lines and showing a general upregulation of FTO in breast cancer compared to healthy tissue or other cancer cell lines, respectively.

Minor comment 2: lack of data from human specimens.

Reply: Not available. Very difficult to realize since immunostaining techniques cannot discriminate between C/EBPβ-LAP and -LIP isoforms because LIP shares all possible antibody epitopes with LAP. This means that one needs enough material for western blotting which is difficult to arrange.

Significance

Reviewer #1: Despite the interest in the finding that FTO knockdown influences cellular proliferation and migration, the authors do not have enough mechanistic insights on how FTO regulates this process, leaving uncertainty on the study's relevance.

Reply: We agree, but we feel that performing detailed mechanistic study would take considerable time and therefore should be part of future work.

*From a translational point of view, it is unclear if the study is significant for the future of therapeutic applications since no experiments have been performed on normal breast cancer cells. *

Reply same as under section 3: We do not understand what the reviewer means with “normal breast cancer cells”, maybe the reviewer means untransformed breast epithelial cells (MCF-10A), or really breast cancer cells derived from patients?

We now added supplementary data FTO knockdown decreases C/EBPβ-LIP levels in MCF-7 (luminal A type breast cancer) and in MEFs (Supplementary Figure 5A and B). This indicates that the FTO- C/EBPβ regulation is conserved in different cell lines of different origin. Still, FTO- C/EBPβ could play a more prominent role in breast cancer with high expression of FTO correlated with high C/EBPβ-LIP levels, and the possibility to suppress this.

*From a molecular point of view, FTO can influence m6A and m6Am. The authors do not mention the relevance of their findings in terms of m6Am biology. *

Reply: See above under 3. Description revisions already incorporated - Major comment 2.

*Reviewer #2: The study's significance is somewhat unclear. The initial sections in the main body present primarily negative or statistically insignificant results. While the explanations in later sections are insightful, they may give the impression of an attempt to justify these negative findings, leaving the study's significance somewhat ambiguous. *

Reply: This raises the issue whether we as a scientific community should present “negative” results. In our opinion this is important since it informs about what is probably not involved (regulation of translation efficiency by FTO) and it leads the way to other hypothesis and explanations of a biological phenomenon. How can – in the reviewers’ words - insightful explanations by labelled as just justifying? They are what they are; insightful and contributing to the topic. Currently the role of FTO in cancer and/or translation regulation is not clear and different views exist (see for example our review https://doi.org/10.1158/0008-5472.CAN-21-3710). In this manuscript we provide evidence that FTO might not be significantly involved in global regulation of mRNA translation efficiency in MDA-MB-231 cells, these results seem quite relevant to share. Furthermore, we provide a possible mechanism that could explain part of the effects observed, and already indicate ourselves future work is needed to further strengthen these findings.

Reviewer #3: * Well written report on the functions of FTO in breast cancer pointing to an oncogenic role and regulation of transcripts related to EMT. Data are well done and well presented, 2 shRNA transfected cell lines are included in the experiments; methodology is clear.*

Reply: we are grateful for this assessment and hope the reviewer will find the manuscript further improved after revision.

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Referee #3

Evidence, reproducibility and clarity

The strengths are the well written manuscript, robust and well presented data, study of the effects of FTO on both transcriptome and translatome.

Major weaknesses:

1. There is a big disconnect between the findings presented in Figures 1-3 and the focus on CEBP in Figure 5. This needs to be reconciled either by demonstrating a link between CEBP and the transcripts found to be dysregulated in Fig 2 or some other way.
2. There are no in vivo data. Does the phenotype caused by FTO KD lead to an in vivo phenotype?
3. The lack of clear impact of FTO KD on the translatome is surprising. Maybe the reverse experiment (over expression) would lead to more relevant findings.Likewise, use of the mutant FTO could differentiate between the demethylase function of FTO vs other non-enzymatic functions.

Minor weaknesses:

1. baseline FTO level in MDA MB231 seems inconsistent (1A vs 1D--controls). It would be useful to see FTO expression across breast cancer cell lines and normal mammary cells to justify choice of cell lines in which experiments were carried out.
2. lack of data from human specimens.

Significance

Well written report on the functions of FTO in breast cancer pointing to an oncogenic role and regulation of transcripts related to EMT. Data are well done and well presented, 2 shRNA transfected cell lines are included in the experiments; methodology is clear.

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Referee #2

Evidence, reproducibility and clarity

The authors are trying to demonstrate the oncogenic role of FTO in breast cancer. RNA-seq was used to explore the effect of FTO on gene transcription and translation. And it turned out that the protein expression ratio of LIP/LAP is the most prominent effect of FTO on breast cancer development. While the oncogenic roles of FTO in breast cancer cell lines look well supported, several key questions remain to be answered before it can be considered to publish.

major comment:

1. The authors focused on FTO and its function of RNA demethylation but the m6A-seq is not used at all. It is not likely to find the direct down stream effector of FTO without m6A-seq if you believe demethylation is the key function of FTO.
2. Related to above concerns, the authors claimed that FTO regulated C/EBPβ-LIP. But how FTO regulated the protein expression is missing. As is known to all, FTO mainly affect RNA m6A. There is a gap between C/EBPβ-LIP protein and the RNA of this gene.
3. Data quality is not convincing, the transwell migration assay image in figure 6 and Supplementary Figure 6 is identical, which is unacceptable.
4. The authors claimed that EMT related genes are affected upon FTO knock down, but Figure 2C do not seem to align with the EMT process. Also, if the authors believe EMT process is regulated, another GSEA enrichment panel like Figure 2B should be included.

Minor concerns

1. Statistic analysis in several panels is missing. Normally, every date should include statistic analysis, even its not significant.
2. Issues in Figure 2E, there is a "E" above the first column, which is not supposed to be there.
3. Also in Figure 2E, these results conducted in FTO-knocked down cells, but the panel did not show clearly.
4. In Figure 2E, the textual description does not entirely correspond with the image results, and there is a lack of information about the expression levels of COL12A1, FN1, MMP1, and TNC.
5. Furthermore, while the article conveys the meaning of WTAP, it lacks a thorough textual explanation. Additionally, the layout of the article's images needs improvement.

Significance

The study's significance is somewhat unclear. The initial sections in the main body present primarily negative or statistically insignificant results. While the explanations in later sections are insightful, they may give the impression of an attempt to justify these negative findings, leaving the study's significance somewhat ambiguous.

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Referee #1

Evidence, reproducibility and clarity

In this study, the authors investigated the effect of FTO knockdown in triple-negative breast cancer (TNBC) cells. They show that FTO knockdown reduces the proliferation and migration of two breast cancer cell lines using clonogenic and transwell migration assays. Through transcriptome analysis of FTO-depleted cells, they showed a negative enrichment of the epithelial-to-mesenchymal transition (EMT) signature and showed that this decrease is not mediated at a transcript stability level. Through ribosome profiling experiments they demonstrated that the translatome is only mildly affected by FTO depletion and using differential ribosomal codon reading (diricore) analysis showed that FTO knockdown does not cause specific tRNA or amino acid shortages. They show that FTO and WTAP knockdown reciprocally regulate the expression of C/EBPβ isoform. Finally, through rescue experiments, the authors showed that C/EBPβ-LIP overexpression rescues the decreased migration phenotype observed upon FTO knockdown.

Major comments:

The authors showed that upon FTO knockdown, the C/EBPβ-LIP protein levels decrease, and conversely, upon WTAP knockdown, the levels of C/EBPβ-LIP protein increase (figure 5b and 5d) and suggest that a reversible WTAP- and FTO-controlled m6A modification of CEBP mRNA alters its translation. Upon FTO knockdown, however, the stability of CEBP mRNA is not affected, and despite a clear trend in the increase of the CEBP transcript m6A levels from MeRIP-RT-qPCR (figure 5E), this is not statistically significant. It remains unclear whether the regulatory effect of FTO on the CEBP mRNA transcript is a direct, m6A-mediated effect or an indirect effect. For this reason, further experiments may help to strengthen this result. It would be helpful to clarify if m6A levels increase in the CEPB mRNA level with more replicates of the MeRIP-RT-qPCR or using other quantitative techniques. Moreover, to clarify whether this is directly mediated by FTO a RIP-qPCR for the FTO protein and CEPB mRNA in wild-type cells could be performed.

Additionally, the authors never consider the possibility that FTO could regulate CEBP because of a possible m6Am site. Does CEBP have an m6Am site? Would PCIF1 knockdown cause the same effect that FTO knockdown? Also, the authors should consider classifying mRNAs based on the number of m6A sites or m6Am sites and determine if mRNAs with an m6Am site or an m6A site show a difference in their translation or expression levels compared to non-methylated sites.

It would be interesting to see if the effect of FTO on proliferation and migration impact less aggressive form of cancer or normal breast cancer cells, such as MCF-10A.

To support the data on the FTO and WTAP regulation of C/EBPβ isoform expression analysis of the correlation in expression between FTO/ C/EBPβ and WTAP/ C/EBPβ could be performed using the cancer cell encyclopedia (CCLE) dependency map portal.

Minor comments:

The figure 5 legend is missing the description of the MeRIP-RT-qPCR experiment.

For the C/EBPβ-LIP overexpression-mediated rescue of the migration phenotype of figure 6 an additional replicate for shFTO1 may be helpful as only one of the two replicates presented is statistically significant.

Significance

Despite the interest in the finding that FTO knockdown influences cellular proliferation and migration, the authors do not have enough mechanistic insights on how FTO regulates this process, leaving uncertainty on the study's relevance.

From a translational point of view, it is unclear if the study is significant for the future of therapeutic applications since no experiments have been performed on normal breast cancer cells.

From a molecular point of view, FTO can influence m6A and m6Am. The authors do not mention the relevance of their findings in terms of m6Am biology.

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Reply to the reviewers

1. General Statements [optional]

We would like to thank all three reviewers for their careful and comprehensive reviews of our manuscript. We have taken on board all the comments and have made appropriate changes to improve the manuscript. The more substantive changes are to the structuring of the text in Introduction section, and to improving the clarity of Figure 2 after reviewers’ comments (we have added extra panels to A, F and G). Other minor changes are individually signposted in each paragraph of the point-by-point response attached below.

We performed a number of pieces of additional analysis to address reviewer comments. To be as transparent as possible we make these and all other data analyses available in the form of .html files exported by Rmarkdown, hosted at https://joebowness.github.io/YY1-XCI-analysis/.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

• *

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

Summary: This manuscript uses differentiation of the highly informative inter-specific hybrid mouse ESC to follow features of genes that inactivate slowly. Resistance to silencing is reflected in reduced change in chromatin accessibility and the authors identify YY1 and CTCF as enriched amongst these 'slow' genes. This finding is provocative as these factors have been reported to enrich at both human and mouse escape genes. The authors go on to demonstrate that eviction of YY1 is slowly evicted from the X, and that removal of YY1 increases silencing.

Minor Comments: Overall, the manuscript's conclusions are well supported; however, the brevity of the presentation in some places made it difficult to follow, and in other places seemed a missed opportunity to more fully examine or present their data.

1. Introduction is only 2 paragraphs and half of the last is their new findings. First part of results/discussion is then forced to be very introductory. In addition, some discussion of escapees, even if predominantly human, seems warranted in the introduction. There are multiple studies that have tried to identify features enriched at genes that escape inactivation that could be mentioned.

We have now written the introduction as 3 paragraphs instead of 2. In doing this, we have moved the sentence introducing chromatin accessibility from the results section to the introduction. Additionally, we now discuss the studies that focus on escapees (in mouse XCI) in the second introduction paragraph.

Variation in silencing rates. 'Comparable rankings' cites multiple studies (oddly previous sentence cites only two) - how concurrent are they? Developing this further (perhaps a supplementary table) would inform whether the genes assessed are ones that routinely behave similarly across different studies/lines; and also serve as a resource for future studies.

To avoid double-citing, we have made this one sentence and have cited at the end of the sentence 7 studies which describe gene-by-gene variability in rates of silencing. The majority of these studies include comparisons of their categories of fast and slow-silencing gene with previous classifications, and they all conclude that there is substantial concurrence. Some examples:

• Marks et al, 2015, Table S3,
• Loda et al, 2017, Figure 5,
• Barros de Andrade E Sousa et al. 2019, Figure 2
• Pacini et al. 2021, Figure 6e,i We believe this is sufficient evidence for our claim that these studies report “comparable categories” (“ranking” changed to “categories” as not all studies strictly rank). A comprehensive gene-by-gene comparison table would likely serve only to highlight differences due the various silencing assays/model systems/classification approaches used in the studies. If required, however, we would be willing to include a supplemental table which collates where gene silencing categories are discussed in each publication, and links to any supplemental files which provide full lists of X-linked genes.

It would be helpful to give insight into informativity of cross - what proportion of ATAC-seq peaks were informative with allelic information (and similarly, what proportion of genes expressed had allelic information?

Of the 2042 consensus ATAC-seq peaks we defined on ChrX via aggregating macs2 peaks over all time course samples, n = 821 passed our initial criteria for allelic analysis in the iXist-ChrX-Dom model line (ie they are proximal to the Xist locus in ChrX 0-103Mb, overlap SNPs, and contain sufficient allelic reads). A small number of peaks were additionally filtered out during fitting of the exponential decay model, leaving a final ATAC-seq peak set of n = 790 elements (38.6%) which we focus on in this study. We have added this information to the text (first Results paragraph).

Our collections of ChrX genes amenable to allelic analysis were not redefined for this study. We used lists of genes defined in our previous ChrRNA-seq study (10.1016/j.celrep.2022.110830). In general, allelic analysis of gene expression is not as limited by the frequency of SNPs, because the sequence length of transcripts (including introns, which are a significant fraction of the reads in ChrRNA-seq data) is much greater than for ATAC-seq peaks. Only a few very lowly expressed genes are not amenable to allelic ChrRNA-seq analysis.

P5: "can be influenced by Xist RNA via a variety of mechanisms" seems like it this sweeping statement could use expansion, or at least a reference. Authors could also clarify that 'distal elements assigned by linear genomic proximity is their definition of nearest gene.

The statement that “both [chromatin accessibility and gene expression] can be influenced by Xist RNA via a variety of mechanisms” is intentionally broad to support a negative argument that we do not wish to mechanistically over-interpret the observation that Xi chromatin accessibility loss occurs slower than gene silencing. Nonetheless, we have added two references to studies which report mechanisms for how Xist may influence chromatin accessibility; via recruiting PRC1 (Pintacuda et al 2017) or antagonising BRG1 (Jegu et al 2019). That multiple molecular pathways simultaneously contribute towards the effect of Xist RNA on gene silencing is well established in the field (see reviews such as Brockdorff et al 2020, Boeren et al 2021, Loda et al 2022).

We have clarified in the text that our definition of “distal” is all REs which do not overlap with promoter regions (TSS+/-500bp). We have also made it clearer that our definition of “nearest” gene refers to linear genomic proximity in both the Results and Methods sections.

Figure S1 - there are 6-8 other regions that fail to become monoallelic - what are they?

The regions which stand out most by the colour scheme of the heatmap in Figure S1 are those where accessibility increases on Xi, most notably the loci of Firre, Dxz4 and Xist, which are known to have unique features related to the 3D superstructure of the inactive X chromosome. A few other regions which do not become monoallelic harbour classic “escapee” genes. We have now labelled the locations of escapees Ddx3x, Slc25a5 and Eif2s3x in FigS1.

The other regions noticeable in the heatmap have no obvious features which explain why they fail to become monoallelic. We have highlighted a region containing intragenic peaks within Bcor (a gene which is silenced in iXist-ChrX mESCs), but many other regions are not in the vicinity of genes. Some of the persistently Xi-accessible peaks within these regions contain strong YY1 or CTCF sites, although many others do not.

It is also possible that some Xi-accessible peaks are artefacts of mismatches between the Castaneous or Domesticus/129Sv strain SNP databases and ground truth iXist-ChrX genome sequence. The number of these cases are small, and if a misannotated SNP is the only SNP present in a single peak, the peak is discarded by our allelic filtering criteria as it will appear monoallelic in uninduced mESCs.

Is there any correlation between silencing speed and expression (as previously reported)? If yes, then is there also a correlation with YY1 presence - and is this correlation greater than or less than seen on autosomes?

The data we present here pertaining to gene silencing kinetics is reused from our previous study. In that work we did indeed observe a significant association between silencing rate and initial gene expression levels (10.1016/j.celrep.2022.110830, Supplemental Information Figure S5F), which has also been reported by multiple groups previously.

To correlate YY1 binding with gene expression levels, we calculated transcripts per million (TPM) for all genes from our genome-wide mRNA-seq data of uninduced iXist-ChrX-Dom cells (GSE185869). It is indeed true that, on average, X-linked genes classified as “direct” YY1-targets in our analysis have higher levels of initial expression (median TPM 70.8, n=64) compared to non-target genes (median TPM 30.7, n=346). Autosomal YY1 targets are also relatively higher expressed (median TPM 29.6, n=1882) than non-YY1 genes (median TPM 8.0, n=9983). Within the list of YY1-targets, there is no additional correlation between quantitative levels of YY1 ChIP enrichment (calculated in this study using BAMscale (Pongor et al, 2020)) and gene expression (R=-0.05, Spearman correlation).

Therefore, we appreciate that this correlation between YY1-binding and gene expression levels may be a covariate in the correlation we report in this study between YY1-target genes and slow-silencing. This does not invalidate a potential functional role for YY1 in impeding silencing, as it could affect both variables via common or distinct mechanisms. Nevertheless, in an attempt to account for initial expression level as a covariate, we compared the silencing halftimes of YY1-targets versus non-targets within genes grouped by similar expression levels (low, medium and high-expressed genes). YY1-targets have slower halftimes in each comparison, and this difference is highly significant (p=1.9e-05, Wilcoxon test) for the “medium-expressed” gene group. This implies that YY1 contributes towards slower gene silencing kinetics independently of initial gene expression levels. We have added this panel to Fig2 with an associated sentence in the Results section.

These new analyses are also appended to the documentation of the R scripts used to generate the main figures in this study (Figure2_YY1association.Rmd), which will all be published to Github.

It is also important to note that this analysis approach is complicated by the methodology we use to classify YY1 target genes. In this study, we define YY1 targets based on the presence of ChIP-seq peaks overlapping the gene promoters, which is reasonable and widely accepted practice when defining targets of transcription factors. However, as briefly discussed in the Methods, in YY1 ChIP-seq data samples with very high signal:noise (eg Fig3), minor peaks of YY1 enrichment can be detected at almost every active promoter. As enrichment at these peaks is typically much less than at peaks with occurrences of the YY1 consensus DNA motif, we hypothesise that these small peaks result from secondary YY1 cofactors enriched at promoters (eg P300, BAF, Mediator) rather than direct sites of binding to DNA/chromatin. Therefore, for annotating genes as “direct” YY1 targets, we chose to use the YY1 peak set defined from lower signal:noise ChIP-seq data in iXist-ChrX produced with the endogenous YY1 Ab. Nevertheless, this behaviour is likely to confound any analysis correlating YY1 ChIP binding with gene expression.

Figure 2: Have the authors considered using quartiles rather than an arbitrary division into depleted and persistent?

We primarily chose this binary classification of REs as either Xi-“persistent” or Xi-“depleted” to maximise the numbers of sequences that could be used in each group as input for the HOMER motif enrichment software.

It is also not trivial to separate REs into quartiles because our “Xi-persistent” classification includes peaks defined as “biallelically accessible in NPCs”, as well as peaks with slow accessibility halftimes. This is explained in both the Results and Methods but we now have edited Fig2A to make it clearer. Instead of quartiles, we have performed an analysis which keeps “biallelically accessible REs” as a separate category and subdivides the remaining peaks into three groups by halftimes (slow, intermediate and fast accessibility loss). The same trends are evident with this four-category approach as with the two-category approach.

Importantly, our follow-up analyses which confirm the association between YY1 binding and slow Xi accessibility loss (Fig2E) and slow silencing (Fig 2F-H) are independent from categorisations of REs which rely on arbitrary thresholds.

1. Could simplify secondary labels to solely YY1 and CTCF. D & F do not print in black and white. Overall the mESC versus NPC can be confusing, perhaps mESC (no diff) would be helpful?

We have simplified the secondary labels in Fig2B and modified the colour scheme of FIg2D and Fig2F as suggested. “mESC” is now modified to “mESC no diff” in Fig2H, FigS2B, Fig3C and Fig3E to reduce the potential for confusion.

The numbers appear to suggest YY1 is generally enriched on X, but not at promoters?? Is this true?

The explanation for this is that clear peaks of YY1 ChIP are found at young LINE1 elements in iXist-ChrX mESCs (specifically over L1Md_T subfamilies). These elements are highly enriched (>2-fold) on the mouse X chromosome compared to autosomes (Waterston 2002), and the majority are not promoter-associated. We chose not to include a discussion of YY1 enrichment at repetitive LINE1 elements in this study primarily because of a) issues related to multiple-mapping reads, such as difficulties distinguishing ChrX vs autosomal reads, and b) the absence of strain-specific SNPs within annotated ChrX L1Md_Ts means that none of these elements are amenable to allelic analysis so we cannot compare Xi versus Xa. However, these LINE1 peaks are a significant fraction (262/521) of the numbers of YY1 ChIP-seq peaks in Fig2C.

For Figure 2f, it might be helpful to show autosomal genes - are Fast depleted or Slow enriched for YY1 relative to autosomes?

We have calculated these numbers as part of the analysis of gene expression on ChrX and autosomes above. Overall, the fraction of genes defined as YY1-targets is the same on ChrX as on autosomes (~0.16). Accordingly, fast-silencing genes are depleted for YY1 compared to autosomes, whereas slow-silencing genes are enriched for YY1 compared to autosomes. Fig2F is now redesigned to include the total numbers of YY1-target genes on ChrX and autosomes.

More generally, is YY1 binding on the X lost more slowly than YY1 binding on autosomes, or is the slow loss a feature of YY1. While I agree YY1 could have direct up or down-regulatory roles, Figure S3 could also be reflecting a secondary impact.

We agree that many of the differentially regulated genes after 52 hours of YY1 degradation could be secondary effects and have added a sentence on this to the relevant paragraph in the text.

Figure 3, 4 and supplementary - the chromosome cartoon introduces the LOH in iXist, but this needs to be described in text. Describing the reciprocal as a biological replicate seems challenging given this LOH.

It is true that the reciprocal lines iXist-ChrX-Dom and iXist-ChrX-Cast are not true biological replicates, and we try to avoid referring to them as such. Writing this in the legend of Fig3 was an error which we have corrected. We have now also mentioned the recombination event in the iXist-ChrX-Dom cell line at the point where data from this line is first discussed (paragraph 1 of Results section).

For the latter parts this work (Figs 3 and 4), we made the conscious decision to proceed with two YY1-FKP12F36V cell lines from different reciprocal iXist-ChrX backgrounds (aF1 in iXist-ChrX-Dom, cC3 in iXist-ChrX-Cast), rather than “biological replicate” clones from either iXist-ChrX-Dom or iXist-ChrX-Cast. Our reasoning was to control against potential confounding effects of strain background on our experiments related to the role of YY1. Although there were some minor differences between the clones, aF1 and cC3 demonstrated essentially equivalent phenotypes in all analyses we performed.

Could a panel of TFs be used rather than OCT4 which has its own unique properties to emphasize that YY1 is unique?

This would indeed be worthwhile, and we did consider attempting to perform ChIP-seq for additional TFs other than OCT4 in order to collect more points of comparison for the slow rate of loss of YY1 binding to Xi. However, it is admittedly hard to identify appropriate candidate TFs in mESCs which a) have similar numbers of discrete peaks of binding in promoters and distal elements on ChrX and b) it is possible to reliably perform ChIP-seq for at sufficiently high signal:noise to allow for quantitative allelic analysis.

We have changed the text to acknowledge that our comparison only to OCT4 limits the scope of the statements we can make about unique properties of YY1 binding.

Figure 4 - by examining 'late' genes, a change in allelic ratio is observed, but what about escape genes (e.g. Kdm5c, Kdm6a)? Do they now become silent? It would be helpful to have all this data as a supplementary table so people could query their 'favourite' gene.

YY1 degradation experiments performed for Figure 4 were performed on mESCs without cellular differentiation (YY1-ablated cells do not survive in our mESC to NPC differentiation protocol). In undifferentiated mESCs, silencing of the inactive X does not reach completion, and in fact all X-linked genes are residually expressed at a higher level than in equivalent timepoints of Xist induction with NPC differentiation (see Figure 4D, Bowness et al 2022). We write in the text “slow-silencing genes are residually expressed from Xi” because genes of this category account for the majority of expression under these conditions, and indeed almost all slow genes would all be classed as “escape genes” in this setting by a conventional definition of >10% residual expression from Xi (see also Figure 4D, Bowness et al 2022). Our analysis in Fig4D (of this study) includes all genes, and we share processed .txt files of allelic ratio and allelic fold changes in GEO, so querying the behaviour of a favourite gene would be easy (GSE240680).

Incidentally, when we do perform NPC differentiation of iXist-ChrX NPC, at late stages very few genes show any expression from Xi (Ddx3x, Slc25a5, Eif2s3x and Kdm5c clearly escape, but even Kdm6a is entirely silenced). Unfortunately, with such a small number of “super” escapees it is hard to make any general conclusions, so in this study we can only make inferences about escape via the transitive property that many “slow-silencing” genes are facultative escapees in other settings without induced Xist overexpression. We now write about this consideration in the introduction and final paragraph of the main text.

It seems surprising that loss of YY1 has no demonstrative impact on the Xa. Figure S3B suggests that over 1000 genes are significantly impacted - primarily down regulated. How many of those are X-linked? Perhaps they could be colored differently?

For the broad-brush differential expression testing in FigS3B, we use all the ChrRNA-seq samples (6 x untreated, 6 x dTAG) as “pseudo-replicates”, disregarding any confounding effects related to induced Xist-silencing as effecting untreated and dTAG sample groups equivalently. We did specifically investigate the behaviour of X-linked genes in this volcano plot, however only a very small number of genes were differentially expressed (n=22 X-linked genes appeared significantly downregulated compared to n=4 genes upregulated). This can be seen in our analysis records uploaded to Github.

Additionally, there is actually a minor effect of YY1 loss on expression of YY1-target genes on Xa. This can be seen in Fig4F, where the median lines of YY1-target boxes lie below the horizontal line of 0-fold change.

Since XIST+/undifferentiated cells retain YY1, is YY1 binding sensitive to DNAme? Indeed, are X chromosome bound sites in islands that become methylated? Figure S4 shows YY1-targetted X genes in SMCHD1 knockout; can CTCF targets also be shown? While identified in Figure 2, CTCF was not examined the way YY1 was, although it has also been identified in somatic studies of genes that escape X inactivation.

Binding of YY1 is indeed sensitive to DNA methylation; specifically it is reported to be blocked by CpG methylation (see refs (Kim et al, 2003; Makhlouf et al, 2014; Fang et al, 2019). Thus, crosstalk with the DNA methylation pathways, which deposit de novo CpG island methylation as a late event of XCI (Lock 1987, Gendrel 2012), did appeal to us as a potential mechanism of YY1 “eviction”. However, preliminary analysis we performed to investigate this revealed limited overlap between YY1 binding sites and de novo meythlated CpG islands in the iXist-ChrX model cell line.

FigS4 presents ATAC-seq data from two iXist-ChrX SmcHD1 KO clonal cell lines, comparing the accessibility loss kinetics between YY1-binding and non-YY1 REs in these cells.

Although FigS4 in this paper does not show genes, we have previously published ChrRNA-seq data from these SmcHD1 KO lines over a similar Xist induction + NPC differentiation time course (Figure 6, Bowness et al, 2022). A reanalysis of this ChrRNA-seq data by YY1-target vs non-target genes shows a similar trend to the accessibility data, although this is expected from the strong overlap of both “YY1-target” and “SmcHD1-dependent” genes with slow-silencing genes in our model.

With respect to CTCF, we have performed a similar analysis of this data separating ATAC-seq peaks by CTCF-binding rather than YY1-binding. This shows a similar trend to YY1, but is overall less pronounced, and is now included in our analysis records. We have reported previously that loss of CTCF from many binding sites on Xi requires SmcHD1 (Gdula et al, 2019).

When the authors use cf. do they simply mean see also, or as wikipedia suggests: "the cited source supports a different claim (proposition) than the one just made, that it is worthwhile to compare the two claims and assess the difference". Perhaps it would be worth spelling out to clarify for the audience.

We used “cf.” in the text to mean “compare with”, when referring to a plot/observation/piece of data outside of the figure being immediately discussed (either in another study or different section of the paper). We were not aware of the recommendation to only use the cf abbreviation when the two items are intended to be contrasted. We do not believe this to be a universal grammatical convention, but nevertheless have changed incidences of cf. to “see also”.

Reviewer #1 (Significance (Required)):

General assessment: An important question in human biology is how much the sex chromosome contributes to sex differences in disease frequency. Genes that escape X inactivation in humans seem to have considerable impact on gene expression genome-wide. While there are not as many genes in mouse that escape inactivation, the use of the mESC cell differentiation approach allows detailed assessment of the timing of silencing during inactivation. The authors utilize an inter-specific cross and it would be interesting to know the limitations of such a system (in terms of informative DHS/genes that are informative).

Advance: As the authors note, there are multiple studies of similar systems that have revealed differences in the speeds of silencing of genes. However, this is the first study to my knowledge that has then tried to assess timing with gene-specific factors. There are multiple studies in humans comparing escape and subject genes for TFs, but lacking the developmental timing that this study incorporates.

Audience: While generally applicable to a basic research audience interested in gene regulation, the applicability to human genes that escape inactivation may interest cancer researchers or clinical audiences interested in sex differences.

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

The authors studied the molecular basis of a variation in the rate of individual gene silencing on the X undergoing inactivation. They took advantage of ATAC-seq to observe the kinetics of chromatin accessibility along the inactive X upon induction of Xist expression in mESCs. They demonstrated a clear correspondence between the decrease in chromatin accessibility and the silencing of nearby genes. Furthermore, they found that persistently accessible regulatory elements and slow-silencing were associated with binding of YY1. YY1 tended to associate longer with genes that required more time to be silenced than those that became silenced fast on the inactive X during XCI. The acute loss of YY1 facilitated silencing of slow genes in a shorter period. They suggest that whether or not the transcription factors stay associated longer is another factor that impacts the variation in the rate of gene silencing on the Xi.

Reviewer #2 (Significance (Required)):

It has been suggested that the rate of gene silencing during XCI is varies depending on the distance of individual genes from the Xist locus or the entry site of Xist RNA on the X, as well as their initial expression levels before silencing. This study provides another perspective on this issue. The persistent association of transcription factors during XCI affects the rate of gene silencing. Although the issued addressed here might draw attention from only the limited fields of specialists, their finding advances our understanding of how the efficiency of silencing is controlled during the process of XCI. The experimental data essentially support their conclusion, and the manuscript was easy to follow. However, I still have some comments, which I would like the authors to consider before further consideration.

Major concerns 1. Based on the results shown in Figure 3E and F, the authors concluded that YY1 was more resistant than other TFs against the eviction from the X upon Xist induction. I am not still convinced with this. YY1 binds DNA via the zinc finger domain, while Oct4 binds DNA via the homeodomain. The difference in the binding module between them might affect their dissociation or the response to Xist RNA-mediated chromatin changes. In addition, given that YY1 has been reported to bind RNA, including Xist, as well, Oct4 might not be a good TF to compare.

We acknowledge and agree that our singular comparison between YY1 and OCT4 is insufficient to support a general conclusion that YY1 is unique with respect to its binding properties on Xi. This was also alluded to by Reviewer #1 (see 10.), where in response we write about the difficulties of selecting other appropriate/feasible candidate TFs for ChIP-seq in order to widen the comparison beyond OCT4. In consideration of this concern, we have re-phrased our conclusions regarding this point in the text, both at the point where it is first presented (Fig3F) and in the first discussion paragraph.

Furthermore, the difference in allelic ratio change between YY1 and OCT4 is admittedly not dramatic, and this metric can be influenced somewhat by the properties of the sets of peaks used (which is also why we have not tried to add statistical significance to this comparison in Fig3F). In order to make the comparison with OCT4 (a classic pluripotency factor), we were also limited to using mESC culture without differentiation conditions. It is possible that more pronounced differences between YY1 and other TFs would be observed under conditions where XCI is able to proceed further.

Even so, we contend that our observation that YY1 binding is lost from the Xi relatively slowly likely stands without a requirement for a comparison with OCT4 or other transcription factors. The decrease in allelic ratio for YY1 ChIP occurs more slowly than overall loss of chromatin accessibility from REs, which is arguably a more general proxy for TF binding, and much slower than kinetics of gene silencing (Fig3D and FigS2C). In addition, no other TF motifs (except CTCF, which has its own unique properties) were found significantly enriched within persistently-accessible REs, which would be an expectation if a different factor had similar properties of late-retained Xi binding as YY1.

Thus, overall we have tried to write the paper without overstating in isolation the importance of our claim that YY1 binding on Xi is relatively resistant to Xist-mediated inactivation, instead emphasising that it should be considered alongside the other pieces of data in the study.

I don't think that Kinetics of YY1 eviction upon Xist induction in SmcHD1 KO cells during NSC differentiation fit the phenotype of Smchd1mutant cells. Although their previous study by Bowness et al (2022) showed that Smchd1-KO cells fail to establish complete silencing of SmcHD1-dependnet genes, their silencing still reached rather appreciable levels according to Figure 6 of Bowness et al (2022). This is, in fact, consistent with the idea that XCI initially takes place in the mutant embryos, at least to an extent that does not compromise early postimplantation development. On the other hand, a significant portion of YY1 appears to remain associated with the target genes on both active and inactive X (Figure S4), which I think suggests that the presence of YY1 is compatible with silencing of SmdHD1-dependent genes. This is contradictory to the proposed role of YY1 that sustains the expression of X-linked genes in this context.

At any given timepoint of XCI, our data sets of gene silencing (ChrRNA-seq) consistently show a more pronounced allelic skew compared to chromatin accessibility (ATAC-seq). This behaviour is discussed in relation to Figure 1 in the text (see Results paragraph 2). We do not wish to overinterpret this quantitative difference because the assays are technically different and accessibility is not linearly correlated with gene expression. With this in consideration, we interpret the ATAC-seq data presented in Figure S4 to be fully consistent with the iXist-ChrX SmcHD1 KO ChrRNA-seq data in Figure 6 of our previous publication ie. a small increase in residual Xi gene expression from SmcHD1 KO NPCs is accompanied by a more appreciable increase in residual Xi chromatin accessibility. In line with this, it would not be contradictory for substantially increased Xi YY1 binding to sustain a quantitively small (but nonetheless meaningful) increase in residual gene expression from Xi.

Additionally, the context in which we include this SmcHD1 KO ATAC-seq data in the current paper is to hypothesise a potential role for SmcHD1 in contributing towards the eventual removal of YY1 binding from Xi. This hypothesis is essentially based on two observations; 1.) There is substantially more residual YY1 binding to Xi in mESC no diff conditions (Figure 3) and 2.) One difference between no diff and diff conditions is absence of SmcHD1 recruitment in the former (Figure 5 in our previous study). The new SmcHD1 KO ATAC-seq data adds a third observation which supports the hypothesis - that YY1-bound REs are appreciably more accessible from Xi in SmcHD1 KO. However, none of these observations are direct evidence of a link between SmcHD1 and YY1, and more experiments would be required to substantiate this potential mechanism. If confirmed, it would be logically reasonable to suggest a role for YY1 in contributing towards the residual expression of X-linked in the context of SmcHD1 KO, but we do not yet claim this, and a potential link with SmcHD1 KO is not the main focus of the paper.

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

In this manuscript, Bowness and colleagues describe the interesting finding that the transcription factor YY1 is associated with slow silencing genes in induced X-Chromosome Inactivation (XCI). The authors have conducted a comprehensive characterization of X-linked gene silencing and the loss of chromatin accessibility of regulatory elements in induced XCI in ESCs and during NPC differentiation. X-linked gene silencing was classified into four categories, ranging from fast-silenced genes to genes that escape silencing. Motif enrichment analysis of regulatory elements associated with slowly silenced genes identified YY1 as the transcription factor most significantly enriched. The separation of YY1-target and non-target genes confirmed that most genes bound by YY1 indeed exhibit slower silencing kinetics. A comparison of the binding kinetics of YY1 to another transcription factor, OCT4, during XCI revealed that YY1 is evicted more slowly compared to OCT4 on the inactive X, suggesting that slower eviction is a unique property of YY1. Conditional knock-outs of YY1 using protein degradation during induced XCI in mESCs demonstrated that the loss of YY1 at target genes enhances silencing. This supports the hypothesis that YY1 serves as a crucial barrier for slow-silenced genes during XCI. Finally, the authors propose a hypothesis regarding the mechanism of YY1 eviction, suggesting a potential connection to the role of SmcHD1 during XCI.

The authors provide an in-depth analysis of the role of YY1 in gene silencing kinetics during induced XCI and believe this manuscript should be published if our comments are addressed.

Major comment:

Based on the allelic ratio in figure 3C only minor loss of YY1 binding occurs in induced XCI in mESCs on the Xi, while silencing is established properly as shown in figure 4C (left panel, red boxplots). This suggests that YY1 eviction is not necessarily required for these genes to be effectively silenced. Could the authors explain this discrepancy in the data regarding their manuscript conclusions? It seems this is true for XCI happening during differentiation towards NPCs, but not if cells are stuck in the pluripotency stage?

Whilst indeed substantial, we do not consider the silencing seen for 6-day mESCs in Fig4C to be “established properly”. We refer to our previous publication (Figure 4 Bowness et al., 2022), which shows that silencing at equivalent timepoints under differentiation conditions (d5-d7) is significantly more pronounced (near-“complete”). Indeed, the level of silencing reached by YY1-FKBP mESCs (Xist induced but no dTAG treatment) aligns with the plateau of silencing in undifferentiated mESCs we describe in our previous study (median allelic ratio of approximately 0.1).

We conclude that YY1 contributes somewhat to sustaining this residual expression in mESCs, because a) substantial YY1 binding remains on Xi at these timepoints in mESCs and b) silencing increases with degradation of YY1 (the latter is more direct evidence). Notably, silencing does not progress to completion (allelic ratio of 0) in the absence of YY1, so we do not claim that YY1 is the only factor sustaining residual Xi gene expression in mESCs.

We interpret this comment to be a fundamentally similar concern to that raised by Reviewer #2 (2.), but in the context of undifferentiated mESCs rather than SmcHD1 KO. As stated above, we do not think it inherently contradictory for substantially increased Xi YY1 binding to sustain a quantitively small (but nonetheless meaningful) increase in residual gene expression from Xi.

Minor comments:

1. In the abstract lines 7-8, the authors state that the experiments were performed in mouse embryonic stem cell lines, but much of the data shown is acquired in NPC differentiations. Please adjust abstract.

We have adjusted this sentence in the abstract to include that many of the experiments in the paper involved differentiation of iXist-ChrX mESCs.

The last sentence of the abstract states that YY1 acts as a barrier to silencing but as stated in my major comment, that does seem to be the case in ESC differentiation towards NPCs, but not in ESCs themselves. Please tone down this sentence. Moreover, we do not fully understand where the 'is removed only at late stages' comes from? Is this because of the Smchd1 link? We find this link quite weak with the data presented. We would tone down that last abstract sentence.

We have toned down the final sentence of the abstract accordingly. We agree that “removed only at late stages” is unsubstantiated since YY1 binding on Xi decreases over the entire time course (albeit slowly). However, we maintain that a connection between YY1 and late stages of the XCI process is reasonable to infer from the various pieces of evidence we provide in the study (egs YY1 is persistently enriched in accessible REs, it is associated with slow-silencing genes, and it remains bound to Xi in undifferentiated mESCs).

Several comparisons to human XCI have been made in the article. We do agree that there are similarities between mouse and human XCI. However, there is insufficient data that substantiates that these genes are regulated in a similar manner in humans. We believe the comparisons should be removed altogether or attenuated.

We agree that there is nothing in our data that directly pertains to human XCI. Comparisons to human are only made twice in the paper: Initially in the introduction to make a broad statement that many mechanisms of Xist function are conserved between species, and finally as speculation in the last discussion paragraph. We think it is relevant to acknowledge the parallels between our study, which links YY1 binding with resistance to Xist-silencing in a mouse ESC model, and literature describing a similar association between YY1 and XCI escape in humans.

At bottom of page 4, the authors say that for any given gene, the allelic ration of accessibility at its promoter decreased more slowly than it silenced and then write Fig 1B. They probably mean S1C? Since 1B only shows 4 genes.

The phrase “any given” was used colloquially (ie imprecisely), so we have replaced it with “individual”.

Figure 1B shows the average allelic ratio of multiple clones for genes representing different silencing speeds. Each data point is the average of multiple clones for these representative genes, could the authors show the individual data points or the standard deviation?

Fig1B predominantly shows the averages of only two replicate time-courses of Xist induction with NPC differentiation using the same parental clonal cell line, iXist-ChrX-Dom, but performed on different dates and passages. We regenerated the panel without merging the replicate data points, but this has little effect on the plot (see the Rmarkdown html file of Figure 1 on Github).

Figure 1B. Loss of promoter accessibility lags behind loss of chromatin-associated RNA expression for these 4 genes. What about distal REs? Do the allelic ratios for the distal REs more closely follow chromatin-associated RNA expression? Could the authors show this in a supplemental figure?

We comment from FigS1C on the general trend that accessibility decrease from Xi occurs slower than gene silencing (measured by ChrRNA-seq). We then find in FigS1D that distal elements lose accessibility slightly faster than promoters. Although overall the allelic ratio decrease of distal (non-CTCF) RE accessibility is slightly closer to the trajectory to that of gene silencing, it remains substantially slower (see again the Rmarkdown .html file of Figure 1 on Github).

An equivalent plot to Fig1B showing distal REs would rely on our simplistic assignment of distal elements to their nearest genes. We believe this is reasonable generalisation for investigating chromosome-wide trends but unlikely to be sufficiently accurate at the level of specific genes.

Figure 1B: gene silencing trajectory is depicted left while the legend says right. Same for promoter accessibility.

The legend is now corrected.

Figure S1A shows only part of the X chromosome. The area downstream of Xist is missing. Is this because the iXist-ChrXDom cell line is missing allelic resolution as shown in figure S2A? Could the authors explain in the figure legend that part of the X-Chromosome is missing?

We have now included a reference to the recombination event in the iXist-ChrXDom cell line both when we present data from this background in the first paragraph of the Results section, and in the legend of FigS1A.

Figure 2C shows that 94 TSSs bear a YY1 peak, yet Fig 2F shows 62 are targets of YY1. Is this because the rest are not properly silenced or are escapees?

Fig2C shows the numbers of ChrX YY1 ATAC-seq peaks which overlap with “promoters” (ie regions +/- 500bp of a TSS). By contrast, Fig2F shows ChrX genes classified as direct YY1-targets for allelic silencing analysis. The discrepancy between these numbers is due to a number of reasons:

1. It is possible for multiple YY1 peaks to overlap the same promoter (eg one peak overlaps 500bp upstream, a separate peak overlaps 500bp downstream).
2. The count in Fig2C is not restrictive to one TSS per gene in cases where there are multiple transcript isoforms in the gene annotation, thus multiple YY1 peaks can overlap different promoters for the same gene.
3. A few genes do not pass our filters for allelic silencing analysis (eg they are too lowly expressed). Some YY1 peaks may overlap these genes. We hope the revised version of Fig2F, which includes numbers of direct YY1 target genes on autosomes and ChrX, makes the distinction between these two numbers clearer.

Moreover, YY1 has ~4-fold more peaks on the X chromosome on distal elements compared to promoters. Yet figure 2F exclusively shows the proportion of YY1 binding sites on TSSs. Would distal REs show similar proportions for the silencing categories? Could the authors show the differences in a Supplemental figure?

As discussed in the response to Reviewer #1 (point 8.), a large fraction of distal YY1 peaks on ChrX are at LINE1 elements, which are not amenable to allelic analysis. Excluding these peaks results in a smaller number of distal elements bound by YY1. The application of our filters for allelic analysis reduces the number of distal YY1-bound REs even more, and our assignment of distal REs to their nearest gene is imprecise. For these reasons, we do not think a comparison of genes classified by whether they are putative targets of distal YY1-bound enhancers is informative.

The authors switch between different model systems in the figures, which makes quite confusing which type of XCI is being discussed. We would like to see clearly stated above all panels which cell culture condition is being studied (mESCs or NPCs).

We have tried to improve this potential source of confusion by modifying “mESC” to “mESC no diff” in the relevant figure panels (see response to Reviewer #1 comment 7B), and adding “in mESCs without differentiation” to the title of Figure 4.

In Figure 3E and 3F the authors look at the binding retention of OCT4 during XCI in ESCs. However, it is not clear why the authors choose OCT4. Could the authors explain why specifically OCT4 was chosen for these analyses?

In our responses to the other reviewers, we discuss the limitations of only having one other TF to compare to YY1. The choice of OCT4 was primarily dictated by our experience and confidence in being able to generate high quality ChIP-seq data of this factor.

As it was essentially arbitrary for the purposes of this paper, we have added a comment to this effect in the text (“with that of a different arbitrary TF, OCT4”).

What is the expression level of YY1 in NPCs compared to mESCS? In Supplemental S2A, it seems that YY1 protein levels decrease over time during NPC differentiation. Is part of the increased eviction a result of lower protein levels of YY1? Probably not since you calculate ratios between Xi and Xa. Can you please comment on this?

We were similarly intrigued by this apparent decrease in YY1 protein levels in NPCs (there is no decrease on the RNA level) and initially considered if it could contribute to the relative.

In FigS2A specifically, the d18 NPC band is probably just a poor quality sample extraction. Our ChIP-seq data generated from the same sample is similar poor compared to the others (FigS2B). In other YY1-FKBP12F36V clones we derived and characterised by Western (not described further in this study, but will likely be published as raw source data for the cropped blots we show in FigS2A), the apparent difference in YY1 protein levels in NPCs is less pronounced. Although a minor decrease in YY1 protein in NPCs seems to be robust, we do not think it relevant in the context of our analysis of YY1 and XCI, as we almost always use Xa as internal comparison for any observations made about Xi.

On page 7 the authors state that degrading YY1 does not affect Xist spreading and/or localisation. Indeed, it has been previously shown by other groups that YY1 is required for Xist localisation during XCI. Could the authors elaborate further on the why their cells behave differently compared to the Jeon 2011 paper?

We are working with a mouse ESC model of inducible Xist from its endogenous locus on ChrX and using the dTAG system to degrade YY1 protein. By contrast, Jeon 2011 worked with an Xist transgene integrated at random in the genome of mouse embryonic fibroblasts (MEFs) and siRNA knockdown of YY1. The difference in our observations could be linked to any of these 4 differences (ie cellular context, Xist genomic location, Xist introns, knockdown strategy), but we cannot identify a specific explanation.

In figure 4G and figure S3D elevated levels of Xist are observed in the dTAG conditions. As the authors point out, this could then result in accelerated silencing of the X seen upon YY1 loss. Are these elevated Xist levels that result in enhanced silencing in figure 4 relevant for the kinetics of silencing? Moreover, YY1 could act as transcriptional regulator of those genes in the X and by removing YY1, one would expect decreased transcription, which would be read as accelerated silencing. The authors could see whether the genes that show accelerated silencing are regulated by YY1 in ESCs (+ dTAG, - Dox).

We agree that these points are important to consider when interpreting the results of the YY1-FKBP12F36V ChrRNA-seq we present in Figure 4. However, we believe they are covered in the text during our discussion of the data.

In relation to the final suggestion, the silencing of almost all X-linked genes is increased upon YY1 removal so separating a specific set of genes which show accelerated silencing would be difficult. Nevertheless, in Fig4F we report that the increases in Xi silencing are strongest for direct YY1 target genes. In fact, these genes also show a minor decrease in expression in the + dTAG - Dox condition (see response to Reviewer #1 point 12.). However, by-and-large the differences in Xa log2FCs between YY1-target and non-target genes are less statistically significant. Non-significant p-values are not shown on Fig4F, but can be found in our Rmarkdown analysis records.

Can the authors explain why they decided to put the Smchd1 part after the conclusion? Before the conclusion would have been better? The probable link between YY1 and SmcHD1 is definitely something important to investigate.

Supplemental FigS4 relating to SmcHD1 is more speculative and we lack direct mechanistic evidence linking YY1 and SmcHD1. It would require more experiments to substantiate this as a mechanism. We think these experiments could potentially be very interesting, but are beyond the scope of this study.

In the paper the authors cite Bowness et al., 2022. In it, Figure 5F studies silencing times with respect to silencing dependency on SmcHD1. What is the overlap between SmcHD1 target genes and YY1 target genes? This would provide more data about the correlation between YY1 and SmcHD1.

There is an association between YY1 target genes and our previous categories of genes based on SmcHD1 dependence (13/56 SmcHD1_dependent genes are YY1 targets compared to only 8/101 of SmchD1_not_dependent genes). However, this enrichment of YY1 targets in SmcHD1 dependent genes is not so striking to warrant inclusion into the (very short) discussion of SmcHD1 in this paper. This association is also expected from the fact that both YY1-target genes and SmcHD1-dependent genes associate with the set of slow-silencing genes.

Of note, our categories of SmcHD1 dependency were in fact defined in a previous study (Gdula et al., 2019) from a different cellular model (SmcHD1 KO MEFs).

The authors hypothesise that SmcHD1 might play a role in the eviction of YY1 in NPC differentiation. The current data shows impaired silencing of slow silencing genes and YY1-dependent genes in the SmcHD1 knock-out. However, it doesn't show SmcHD1 is required for YY1 eviction. Could the authors provide direct evidence for their hypothesis by performing NPC differentiation in wild type and SmcHD1 knock-out cells and investigate YY1 binding using ChIP-seq?

The data we show in FigS4 is ATAC-seq data. It shows that YY1 target REs are particularly more accessible from the Xi in SmcHD1 KO, which is not direct evidence but does align with a potential role for SmcHD1 in mediating removal of YY1 binding from Xi (see our response to Reviewer #2’s comment 2.). We agree that YY1 ChIP-seq over the same time course would be an interesting experiment, but arguably this would also only be indirect evidence (ie increased Xi YY1 enrichment may be due to a confounding consequence of SmcHD1 KO). We therefore believe the full suite of experiments needed to rigorously test the hypothesis are beyond the scope of this paper.

In figure S4A and S4B no significance is indicated among the different conditions across the different differentiation days. Could the authors add this?

At all timepoints, differences of Xi accessibility between YY1-binding vs non-YY1 REs are significant. P values are now added to FigS4 and the statistical test is described in the legend.

Finally, we would like the authors to elaborate in the conclusion about the order of events. As they correctly state at the top of page 5 (and we agree), delayed loss of promoter accessibility compared to gene silencing does not automatically mean that it is downstream of gene silencing. Can you elaborate on this? Also, in light of Fig S2C where loss of YY1 binding seems to happen after gene silencing.

We mention in the text and in the above response to Reviewer #2 (point 2.) that we do not wish to overinterpret this quantitative difference because the assays are technically different and accessibility is not linearly correlated with gene expression.

It is possible to speculate plausible biological explanations for this discrepancy in kinetics between accessibility loss, TF binding and gene silencing. For example, a change in the landscape of histone modifications at a promoter may have little effect on its accessibility to TFs but directly hinder RNA Polymerase II in initiation and/or elongation of transcription of the gene. However, we prefer to keep this speculation out of the main text of the paper.

Reviewer #3 (Significance (Required)):

This manuscript highlights a novel role for YY1 in XCI. The manuscript provides an analysis of the correlation and causation of YY1 in gene silencing during XCI. There is a clear correlation between YY1 and delayed silencing of genes on the Xi. To our knowledge, this is the first time such an analysis has been performed for YY1. It advances our conceptual and mechanistic understanding of gene silencing kinetics and what the factors involved in it are. We believe it is an important contribution to the XCI field and will be of great value to the XCI community.

Strength:

This study presents a comprehensive and in-depth characterization of X-linked gene silencing during XCI.

Two different types of inducible XCI are studied and compared (ESCs vs differentiation towards NPCs), which we are grateful for.

Systematic and stepwise analysis of the data is very strong.

Many data points have been collected which provide stronger conclusions.

Weakness:

Some sentences in the abstract should be toned down.

YY1 eviction on the inactive X doesn't seem crucial to establish X-linked gene silencing in mESCs.

The mechanistic approach at the end of the manuscript with relation to SmcHD1 could be studied further.

This paper will be suited for a specialised audience in XCI and transcription factor control of gene expression, i.e. basic research.

Field of expertise: XCI, epigenetics, Xist, gene silencing, X chromosome biology.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, Bowness and colleagues describe the interesting finding that the transcription factor YY1 is associated with slow silencing genes in induced X-Chromosome Inactivation (XCI). The authors have conducted a comprehensive characterization of X-linked gene silencing and the loss of chromatin accessibility of regulatory elements in induced XCI in ESCs and during NPC differentiation. X-linked gene silencing was classified into four categories, ranging from fast-silenced genes to genes that escape silencing. Motif enrichment analysis of regulatory elements associated with slowly silenced genes identified YY1 as the transcription factor most significantly enriched. The separation of YY1-target and non-target genes confirmed that most genes bound by YY1 indeed exhibit slower silencing kinetics. A comparison of the binding kinetics of YY1 to another transcription factor, OCT4, during XCI revealed that YY1 is evicted more slowly compared to OCT4 on the inactive X, suggesting that slower eviction is a unique property of YY1. Conditional knock-outs of YY1 using protein degradation during induced XCI in mESCs demonstrated that the loss of YY1 at target genes enhances silencing. This supports the hypothesis that YY1 serves as a crucial barrier for slow-silenced genes during XCI. Finally, the authors propose a hypothesis regarding the mechanism of YY1 eviction, suggesting a potential connection to the role of SmcHD1 during XCI.

The authors provide an in-depth analysis of the role of YY1 in gene silencing kinetics during induced XCI and believe this manuscript should be published if our comments are addressed.

Major comment:

Based on the allelic ratio in figure 3C only minor loss of YY1 binding occurs in induced XCI in mESCs on the Xi, while silencing is established properly as shown in figure 4C (left panel, red boxplots). This suggests that YY1 eviction is not necessarily required for these genes to be effectively silenced. Could the authors explain this discrepancy in the data regarding their manuscript conclusions? It seems this is true for XCI happening during differentiation towards NPCs, but not if cells are stuck in the pluripotency stage?

Minor comments:

In the abstract lines 7-8, the authors state that the experiments were performed in mouse embryonic stem cell lines, but much of the data shown is acquired in NPC differentiations. Please adjust abstract.

The last sentence of the abstract states that YY1 acts as a barrier to silencing but as stated in my major comment, that does seem to be the case in ESC differentiation towards NPCs, but not in ESCs themselves. Please tone down this sentence. Moreover, we do not fully understand where the 'is removed only at late stages' comes from? Is this because of the Smchd1 link? We find this link quite weak with the data presented. We would tone down that last abstract sentence.

Several comparisons to human XCI have been made in the article. We do agree that there are similarities between mouse and human XCI. However, there is insufficient data that substantiates that these genes are regulated in a similar manner in humans. We believe the comparisons should be removed altogether or attenuated.

At bottom of page 4, the authors say that for any given gene, the allelic ration of accessibility at its promoter decreased more slowly than it silenced and then write Fig 1B. They probably mean S1C? Since 1B only shows 4 genes.

Figure 1B shows the average allelic ratio of multiple clones for genes representing different silencing speeds. Each data point is the average of multiple clones for these representative genes, could the authors show the individual data points or the standard deviation?

Figure 1B. Loss of promoter accessibility lags behind loss of chromatin-associated RNA expression for these 4 genes. What about distal REs? Do the allelic ratios for the distal REs more closely follow chromatin-associated RNA expression? Could the authors show this in a supplemental figure?

Figure 1B: gene silencing trajectory is depicted left while the legend says right. Same for promoter accessibility.

Figure S1A shows only part of the X chromosome. The area downstream of Xist is missing. Is this because the iXist-ChrXDom cell line is missing allelic resolution as shown in figure S2A? Could the authors explain in the figure legend that part of the X-Chromosome is missing?

Figure 2C shows that 94 TSSs bear a YY1 peak, yet Fig 2F shows 62 are targets of YY1. Is this because the rest are not properly silenced or are escapees?

Moreover, YY1 has ~4-fold more peaks on the X chromosome on distal elements compared to promoters. Yet figure 2F exclusively shows the proportion of YY1 binding sites on TSSs. Would distal REs show similar proportions for the silencing categories? Could the authors show the differences in a Supplemental figure?

The authors switch between different model systems in the figures, which makes quite confusing which type of XCI is being discussed. We would like to see clearly stated above all panels which cell culture condition is being studied (mESCs or NPCs).

In Figure 3E and 3F the authors look at the binding retention of OCT4 during XCI in ESCs. However, it is not clear why the authors choose OCT4. Could the authors explain why specifically OCT4 was chosen for these analyses?

What is the expression level of YY1 in NPCs compared to mESCS? In Supplemental S2A, it seems that YY1 protein levels decrease over time during NPC differentiation. Is part of the increased eviction a result of lower protein levels of YY1? Probably not since you calculate ratios between Xi and Xa. Can you please comment on this?

On page 7 the authors state that degrading YY1 does not affect Xist spreading and/or localisation. Indeed, it has been previously shown by other groups that YY1 is required for Xist localisation during XCI. Could the authors elaborate further on the why their cells behave differently compared to the Jeon 2011 paper?

In figure 4G and figure S3D elevated levels of Xist are observed in the dTAG conditions. As the authors point out, this could then result in accelerated silencing of the X seen upon YY1 loss. Are these elevated Xist levels that result in enhanced silencing in figure 4 relevant for the kinetics of silencing? Moreover, YY1 could act as transcriptional regulator of those genes in the X and by removing YY1, one would expect decreased transcription, which would be read as accelerated silencing. The authors could see whether the genes that show accelerated silencing are regulated by YY1 in ESCs (+ dTAG, - Dox).

Can the authors explain why they decided to put the Smchd1 part after the conclusion? Before the conclusion would have been better? The probable link between YY1 and SmcHD1 is definitely something important to investigate.

In the paper the authors cite Bowness et al., 2022. In it, Figure 5F studies silencing times with respect to silencing dependency on SmcHD1. What is the overlap between SmcHD1 target genes and YY1 target genes? This would provide more data about the correlation between YY1 and SmcHD1.

The authors hypothesise that SmcHD1 might play a role in the eviction of YY1 in NPC differentiation. The current data shows impaired silencing of slow silencing genes and YY1-dependent genes in the SmcHD1 knock-out. However, it doesn't show SmcHD1 is required for YY1 eviction. Could the authors provide direct evidence for their hypothesis by performing NPC differentiation in wild type and SmcHD1 knock-out cells and investigate YY1 binding using ChIP-seq?

In figure S4A and S4B no significance is indicated among the different conditions across the different differentiation days. Could the authors add this?

Finally, we would like the authors to elaborate in the conclusion about the order of events. As they correctly state at the top of page 5 (and we agree), delayed loss of promoter accessibility compared to gene silencing does not automatically mean that it is downstream of gene silencing. Can you elaborate on this? Also, in light of Fig S2C where loss of YY1 binding seems to happen after gene silencing.

Significance

This manuscript highlights a novel role for YY1 in XCI. The manuscript provides an analysis of the correlation and causation of YY1 in gene silencing during XCI. There is a clear correlation between YY1 and delayed silencing of genes on the Xi. To our knowledge, this is the first time such an analysis has been performed for YY1. It advances our conceptual and mechanistic understanding of gene silencing kinetics and what the factors involved in it are. We believe it is an important contribution to the XCI field and will be of great value to the XCI community.

Strength:

This study presents a comprehensive and in-depth characterization of X-linked gene silencing during XCI.

Two different types of inducible XCI are studied and compared (ESCs vs differentiation towards NPCs), which we are grateful for.

Systematic and stepwise analysis of the data is very strong.

Many data points have been collected which provide stronger conclusions.

Weakness:

Some sentences in the abstract should be toned down.

YY1 eviction on the inactive X doesn't seem crucial to establish X-linked gene silencing in mESCs.

The mechanistic approach at the end of the manuscript with relation to SmcHD1 could be studied further.

This paper will be suited for a specialised audience in XCI and transcription factor control of gene expression, i.e. basic research.

Field of expertise: XCI, epigenetics, Xist, gene silencing, X chromosome biology.

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Referee #2

Evidence, reproducibility and clarity

The authors studied the molecular basis of a variation in the rate of individual gene silencing on the X undergoing inactivation. They took advantage of ATAC-seq to observe the kinetics of chromatin accessibility along the inactive X upon induction of Xist expression in mESCs. They demonstrated a clear correspondence between the decrease in chromatin accessibility and the silencing of nearby genes. Furthermore, they found that persistently accessible regulatory elements and slow-silencing were associated with binding of YY1. YY1 tended to associate longer with genes that required more time to be silenced than those that became silenced fast on the inactive X during XCI. The acute loss of YY1 facilitated silencing of slow genes in a shorter period. They suggest that whether or not the transcription factors stay associated longer is another factor that impacts the variation in the rate of gene silencing on the Xi.

Significance

It has been suggested that the rate of gene silencing during XCI is varies depending on the distance of individual genes from the Xist locus or the entry site of Xist RNA on the X, as well as their initial expression levels before silencing. This study provides another perspective on this issue. The persistent association of transcription factors during XCI affects the rate of gene silencing. Although the issued addressed here might draw attention from only the limited fields of specialists, their finding advances our understanding of how the efficiency of silencing is controlled during the process of XCI. The experimental data essentially support their conclusion, and the manuscript was easy to follow. However, I still have some comments, which I would like the authors to consider before further consideration.

Major concerns

Based on the results shown in Figure 3E and F, the authors concluded that YY1 was more resistant than other TFs against the eviction from the X upon Xist induction. I am not still convinced with this. YY1 binds DNA via the zinc finger domain, while Oct4 binds DNA via the homeodomain. The difference in the binding module between them might affect their dissociation or the response to Xist RNA-mediated chromatin changes. In addition, given that YY1 has been reported to bind RNA, including Xist, as well, Oct4 might not be a good TF to compare.

I don't think that Kinetics of YY1 eviction upon Xist induction in SmcHD1 KO cells during NSC differentiation fit the phenotype of Smchd1mutant cells. Although their previous study by Bowness et al (2022) showed that Smchd1-KO cells fail to establish complete silencing of SmcHD1-dependnet genes, their silencing still reached rather appreciable levels according to Figure 6 of Bowness et al (2022). This is, in fact, consistent with the idea that XCI initially takes place in the mutant embryos, at least to an extent that does not compromise early postimplantation development. On the other hand, a significant portion of YY1 appears to remain associated with the target genes on both active and inactive X (Figure S4), which I think suggests that the presence of YY1 is compatible with silencing of SmdHD1-dependent genes. This is contradictory to the proposed role of YY1 that sustains the expression of X-linked genes in this context.

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Referee #1

Evidence, reproducibility and clarity

Summary: This manuscript uses differentiation of the highly informative inter-specific hybrid mouse ESC to follow features of genes that inactivate slowly. Resistance to silencing is reflected in reduced change in chromatin accessibility and the authors identify YY1 and CTCF as enriched amongst these 'slow' genes. This finding is provocative as these factors have been reported to enrich at both human and mouse escape genes. The authors go on to demonstrate that eviction of YY1 is slowly evicted from the X, and that removal of YY1 increases silencing.

Minor Comments:

Overall, the manuscript's conclusions are well supported; however, the brevity of the presentation in some places made it difficult to follow, and in other places seemed a missed opportunity to more fully examine or present their data.

1. Introduction is only 2 paragraphs and half of the last is their new findings. First part of results/discussion is then forced to be very introductory. In addition, some discussion of escapees, even if predominantly human, seems warranted in the introduction. There are multiple studies that have tried to identify features enriched at genes that escape inactivation that could be mentioned.
2. Variation in silencing rates. 'Comparable rankings' cites multiple studies (oddly previous sentence cites only two) - how concurrent are they? Developing this further (perhaps a supplementary table) would inform whether the genes assessed are ones that routinely behave similarly across different studies/lines; and also serve as a resource for future studies.
3. It would be helpful to give insight into informativity of cross - what proportion of ATAC-seq peaks were informative with allelic information (and similarly, what proportion of genes expressed had allelic information?
4. P5: "can be influenced by Xist RNA via a variety of mechanisms" seems like it this sweeping statement could use expansion, or at least a reference. Authors could also clarify that 'distal elements assigned by linear genomic proximity is their definition of nearest gene.
5. Figure S1 - there are 6-8 other regions that fail to become monoallelic - what are they?
6. Is there any correlation between silencing speed and expression (as previously reported)? If yes, then is there also a correlation with YY1 presence - and is this correlation greater than or less than seen on autosomes?
7. Figure 2: Have the authors considered using quartiles rather than an arbitrary division into depleted and persistent? B. Could simplify secondary labels to solely YY1 and CTCF. D & F do not print in black and white. Overall the mESC versus NPC can be confusing, perhaps mESC (no diff) would be helpful?
8. The numbers appear to suggest YY1 is generally enriched on X, but not at promoters?? Is this true? For Figure 2f, it might be helpful to show autosomal genes - are Fast depleted or Slow enriched for YY1 relative to autosomes? More generally, is YY1 binding on the X lost more slowly than YY1 binding on autosomes, or is the slow loss a feature of YY1. While I agree YY1 could have direct up or down-regulatory roles, Figure S3 could also be reflecting a secondary impact.
9. Figure 3, 4 and supplementary - the chromosome cartoon introduces the LOH in iXist, but this needs to be described in text. Describing the reciprocal as a biological replicate seems challenging given this LOH.
10. Could a panel of TFs be used rather than OCT4 which has its own unique properties to emphasize that YY1 is unique?
11. Figure 4 - by examining 'late' genes, a change in allelic ratio is observed, but what about escape genes (e.g. Kdm5c, Kdm6a)? Do they now become silent? It would be helpful to have all this data as a supplementary table so people could query their 'favorite' gene.
12. It seems surprising that loss of YY1 has no demonstrative impact on the Xa. Figure S3B suggests that over 1000 genes are significantly impacted - primarily down regulated. How many of those are X-linked? Perhaps they could be colored differently?
13. Since XIST+/undifferentiated cells retain YY1, is YY1 binding sensitive to DNAme? Indeed, are X chromosome bound sites in islands that become methylated? Figure S4 shows YY1-targetted X genes in SMCHD1 knockout; can CTCF targets also be shown? While identified in Figure 2, CTCF was not examined the way YY1 was, although it has also been identified in somatic studies of genes that escape X inactivation.
14. When the authors use cf. do they simply mean see also, or as wikipedia suggests: "the cited source supports a different claim (proposition) than the one just made, that it is worthwhile to compare the two claims and assess the difference". Perhaps it would be worth spelling out to clarify for the audience.

Significance

General assessment: An important question in human biology is how much the sex chromosome contributes to sex differences in disease frequency. Genes that escape X inactivation in humans seem to have considerable impact on gene expression genome-wide. While there are not as many genes in mouse that escape inactivation, the use of the mESC cell differentiation approach allows detailed assessment of the timing of silencing during inactivation. The authors utilize an inter-specific cross and it would be interesting to know the limitations of such a system (in terms of informative DHS/genes that are informative).

Advance: As the authors note, there are multiple studies of similar systems that have revealed differences in the speeds of silencing of genes. However, this is the first study to my knowledge that has then tried to assess timing with gene-specific factors. There are multiple studies in humans comparing escape and subject genes for TFs, but lacking the developmental timing that this study incorporates.

Audience: While generally applicable to a basic research audience interested in gene regulation, the applicability to human genes that escape inactivation may interest cancer researchers or clinical audiences interested in sex differences.

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Reply to the reviewers

General Statement We very much appreciate the reviewers' thorough comments and are sincerely grateful for their kind remarks on the novelty and interest of our manuscript. We are confident to have addressed all the points that they have raised including new data, as well as revised figures and text.

Point-by-point description of revisions All the revisions have been already carried out and included in the transferred manuscript.

Reviewer #1

Major comments:

> The number of the replicates/animals for the experiments described in Figures 1 and 2 should be reported either in the figure legends or in the methods (statistical analysis). We have added the required numbers to the corresponding revised figures, as requested.

> A relevant part of the discussion repeats what the authors have already said in the results. I would recommend to reorganize this section, emphasizing the importance of these results in the context of human brain tumors.

Following our own style, we have written a very short (46 lines in length!) Discussion. We dedicate a few lines to highlighting two points: (1) the suggestion, derived from our allograft experiments, that the initial stages of tumour development and long-term tumour growth may be molecularly distinct events, and (2), the unique effect of the combined loss of TrxT and dhd on mbt tumour transcriptomics -unique because none of the suppressors of mbt reported before are as effective in erasing both the MBTS and SDS mbt signatures. Neither of these points are raised in Results. In the remaining few lines we put our results in the context of human Cancer/Testis and elaborate on the fact that the TrxT and dhd pair qualify as head-to-head, CT-X genes, like those reported in human oncology. This is as far as we are willing to go at this stage at emphasizing the importance of our results in the context of human tumours.

Reviewer #2

> 1. Figures should include information regarding the sex of the larvae, particularly as there has been a previously reported sex-linked effect in the phenotypes analysed. (e.g. in Figure 2 and Figure S1, where Indication of the sex of the animals should be provided in the figure OK and not just in the figure legend). We fully agree. Sex must always be taken into account as a biological variable. All the experiments reported in the manuscript were carried out with sexed samples, and were annotated accordingly in the original text. In compliance with the reviewer's request we have added this information also to the revised figure.

*> 2. Data regarding fertility. Can this be shown in a table format? Are dhdKO females fully sterile? What are the fertility levels of Df(1)J5? * Please note that we are not discovering anything here but merely corroborating what has been published before: the lack of TrxT does not affect fertility in either sex; the lack of Dhd results in female sterility (Torres-Campana et al., 2022, Tirmarche et al., 2016, Svensson et al., 2003, Pellicena-Palle et al., 1997). Adding a table would not be justified. Moreover, it would be a rather simple table: all single-pair mating tests (n=10 for each genotype) with Trxt KO and Dhd KO males, and TrxT KO females were as fertile as control flies, while all single-pair mating tests (n=10) with Dhd KO females were sterile.

> 3. Are dhd and TrxT the only genes affected by Df(1)J5? Is there transcriptional data from Df(1)J5 animals to suggest that nearby genes are not affected by the deficiency? Of particular interest would be to assess if snf is affected or not as it is a known regulator of gene expression and splicing. Yes dhd and TrxT are the only genes affected by Df(1)J5. That is the case according to Flybase (citing Svensson et al., 2003, and Salz et al., 1994) and confirmed by our own RNAseq data. No other transcripts, including snf, are affected by Df(1)J5.

> 4. In Figure 1C, statistical test plus indication of significance is not presented. The requested statistical test and significance data have been added as required to the revised figure and figure legend.

> 5. Related to Figure 1D. Additional neural markers could be assessed in dhdKO and TrxTKO flies. Whilst the gross morphology of the brain does not seem to be affected, there is a possibility that cell specification is affected. Specific markers for the NE, MED and CB could be used to assess this in more detail, particularly as the DE-cad images shown for dhdKO and TrxTKO flies seem to differ slightly from the control. We believe that there may be a small misunderstanding here. We have made this point clear in the revised version by referring to substantial published data showing that expression of these two genes is restricted to the germline and that, female fertility aside, TrxT and dhd deficient flies' development and life span are perfectly normal. If anything, Figure 1D is redundant. However, we would rather keep it as a control that our CRISPR KO mutants behave as expected.

> 6. Related to Figure 2A, images from TrxTKO; l(3)mbtts1, dhdKO and l(3)mbtts1 should be added at the very least in a supplementary figure. Additionally, data for NE/BL ratio should be provided for dhdKO, TrxTKO and Df(1)J5 in the absence of l(3)mbtts1 tumours. Related to Figure S1, quantification of NE/BL ratio for female lobes should be added to the figure. All the requested images and data have been included in the revised version in new figures Figure S2B, Figure S2A, and Figure S1A.

> 7. Related to Figure 2B and Figure S1, three rows of images are presented for each genotype. It is unclear whether these correspond to brain lobes from different larvae or different confocal planes from the same animal. This should be clarified in the figure and/or figure legend. This point has been clarified as requested in the revised figure legend. Each group of three rows correspond to brain lobes from different larvae of the same genotype.

> 7 cont. Related to this, in addition to the anti-DE-cadherin data, it would be informative to include immunofluorescence data using antibodies such as anti-Dachshund (lamina), anti-Elav (medulla cortex) and anti-Prospero (central brain and boundary between central brain and medulla cortex) (as assessed in e.g. Zhou and Luo, J Neurosci 2013) in the mbt tumour situation to accurately describe regions disrupted by the tumours. There is no denying that taking advantage of the many cell-type specific markers that are readily available in Drosophila could be of interest. The same applies to cell cycle markers like PH3, FUCCI, and many others. However, we believe that interesting as they may be, none of this markers will give us the clue on the molecular basis of TrxT and Dhd tumour function that is, of course, the open burning question that we are trying to address now.

> 8. Authors should clarify how the NE was defined when mbt tumours are generated, as it is severely affected. From the images provided, it is unclear which region corresponds to NE or how the NE/BL ratio was measured. It would be helpful to outline these regions in the images or, as mentioned above, use antibodies to define them. The figure has been modified to include the requested outlines defining the NE that indeed is correspond to the channel showing DE-Cadh staining.

> 9. Figure 2C does not have indication of statistical significance for the comparisons stated in the text. Potential explanations for the different roles of Dhd and TrxT in long-term tumour development should be explored in the discussion. The requested statistical significance data for these comparisons were stated in the second last paragraph of that section. To make these data more prominent we have also added this information to revised Figure 2C.

>9 cont. Related to this, does the analysis of the RNA-seq data from TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 animals reveal why they have similar effect on mbt tumour development but do not synergistically contribute to long-term growth? Unfortunately our analysis of the RNA-seq data from TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 animals does not give us any clue that could help us understand why they have similar effect on mbt tumour development, but not in long-term growth (allografts). To further explore this point, we have added new Figure S3 that includes a Venn diagramme showing the overlap between the affected mMBTS genes in TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1, together with the lists of enriched GOs among overlapping and non-overlapping genes. GO differences are tantalising, indeed, However, they do not immediately suggest any direct explanation for the different roles of Dhd and TrxT in long-term tumour development.

> 10. Authors should clarify if there is any overlap between the affected M-tSDS and F-tSDS in the TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 conditions. Would the limited overlap suggest that TrxT and dhd act in parallel rather than synergistically? This might also explain the differential effects on long-term tumour development. Additionally, the stronger effect observed in Df(1)J5 animals may be due to TrxT and dhd functional redundancy. Currently, there is limited evidence to suggest that TrxT and dhd act synergistically to regulate mbt tumour growth based on the presented data. See below.

> 11. Authors should include a Venn diagram depicting affected genes (M-tSDS and F-tSDS) in the TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1 and Df(1)J5; l(3)mbtts1 genotypes as this could clarify the percentage of overlap of gene signatures in these different conditions. Related to this point, authors could provide results from GO analysis to investigate whether specific functional clusters are altered in the different conditions. We have taken the liberty of fusing points 10 and 11 that are conceptually similar. The requested Venn diagrams showing the overlap between the affected M-tSDS and F-tSDS genes in the TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1, and Df(1)J5; l(3)mbtts1 conditions, and GO analysis are now shown in new Figure S5. Unfortunately, these new data do not suggest any obvious explanation for the differential effects of these two genes, nor do they allow us to derive any further conclusions regarding the nature of the pathways through which TrxT and dhd cooperate to sustain mbt tumour growth. However, our analyses demonstrate that efficient suppression of mbt phenotypic traits (in larval brains) and transcriptome requires the combined elimination of both germline thioredoxins, while the effect of individual removal of either of them is only partial. These data demonstrate the synergistic nature of TrxT and dhd function in mbt tumour growth.

> 12. In Figure 3E, authors should indicate more explicitly in the figure panel and/or figure legend which genes display significant differences in expression in the different samples. We apologise for not having made this point clear in the original version: All (21) genes shown in this Table are significantly downregulated in DfJ5;ts1 vs ts1. From these, nanos and Ocho are also significantly downregulated in TrxTKO;ts1 vs ts1, and Ocho, HP1D3csd, hlk, fj, Lcp9, CG43394, and CG14968 are significantly downregulated in dhdKO;ts1 vs ts1. These data have been included in the revised figure legend. Data on all other comparisons are included in Table S1.

> 13. In Figure S2C-F it is not clear if the graphs represent data from all tissues or data from male and female tissues separately, as shown in Figure 4. Apologies for the confusion. All samples were from male tissues as indicated in the original figure legend. To make it more clear, we have labelled all four panels in the revised figure.

> 14. Are TrxT and dhd also deregulated in other tumour types? Or is this specific for mbt tumours? This information could be provided to enhance the scope of the manuscript. Thank you for raising this point. TrxT and dhd are not dysregulated in the other tumour types that were analysed in Janic et al., 2010 (i.e pros, mira, brat, lgl and pins).

> 15. Authors conclude that TrxT and dhd cooperate in controlling gene expression between wild-type and tumour samples and that they act synergistically in the regulation of sex-linked gene expression in male tumour tissue. However, the link between the two observations (if indeed there is a link) has not been well explained. Is the effect on gene expression in tumours simply a result of the regulation of sex-linked transcription? Our data show that TrxT and dhd synergistically contribute to the emergence of both the MBTS (i.e tumour versus wild type) and SDS (i.e. male tumour versus female tumour). The only certainty at this time regarding the interconnection between both signatures is that they overlap, but only partially, which answers one the questions raised by the reviewer: the effect on gene expression in tumours is not simply a result of the regulation of sex-linked transcription. Beyond that, the link (if indeed there is a link) between these two signatures has not been investigated. The lack of insight on this issue is not surprising taking into account that, in contrast to classical tumour signatures (tumour versus healthy tissue), the concept of sex-linked tumour signatures is relatively new and only a handful of such signatures have been published. Moreover, the vast majority of classical tumour signatures have not been worked out in a sex-dependent manner.

Reviewer #3 Comments: > - In the first section of the results, as a first step to study the role of TrxT and dhd genes on mbt tumors the authors generate CRISPR knock outs of these genes and correctly validate them. However, afterwards, the experiment where the authors test the KO of these genes in a wild-type larva brain is not contextualized with the rest of the section. It might be best to first address the role of these genes in a tumor context and only then complement with the experiments in wild-type (in supplementary material). We do appreciate the reviewer's view, but respectfully disagree. In our opinion, the manuscript flows better by presenting the tools that we have generated in Figure 1, By corroborating published data showing that these two germline genes do not affect soma development (Torres-Campana et al., 2022, Tirmarche et al., 2016, Svensson et al., 2003, Pellicena-Palle et al., 1997) this first figure not only validates our CRISPR KO mutants, but also sets the stage to highlight their significant effect on a somatic tumour like mbt.

> - Fig 2 B - To back up the quantifications in Fig 2A the authors could include images of l(3)mbt ts1 tumors with TrxT KO and dhd KO also. The requested images are shown in new figure Figure S2B.

> Fig 2 B and C - Indeed, the results suggest that TrxT seems to be responsible for most tumor lethality upon l(3)mbt allografts, but not dhd. This is curious since l(3)mbt; dhd KO brain tumors have the same partial phenotype as l(3)mbt; TrxT KO (fig 1A). It would be interesting to further explore these phenotypes by staining l(3)mbt; TrxT KO and l(3)mbt; dhd KO brains with, for instance, PH3 to understand if the number of dividing cells of these tumors could be different. In addition, to back up this information, the authors could look at what happens to l(3)mbt tumors with TrxT KO and dhd KO at a later stage of development (or to larva or pupa lethality if that is the case) and compare it with l(3)mbt brains. We did explore the possibility of looking at later stages. Unfortunately, the onset of the lethality phase compounded by major tissue reshaping from larval to adult brain make these stages unsuitable to reach any meaningful conclusion. With regards to staining for PH3, we think that like FUCCI and a long list of other useful labels that could be explored, it is potentially interesting, but hardly likely to give us the clue on the molecular basis of TrxT and Dhd tumour function, that is of course the one important question that we are addressing now.

> - Fig 2 B - What happens to the medulla in a l(3)mbt brain tumor? Although the ratio of NE/BL is the same for wild-type and D(1)J5; l(3)mbt, it still seems that the medulla in D(1)J5; l(3)mbt brains is substantially bigger, although quantifications would be required. Do the authors know if the NE in D(1)J5; l(3)mbt brains is either proliferating less or differentiating more? There are no significant differences in medulla/BL nor in CB/BL ratios. The corresponding quantifications have been added to the revised version. As for the question on proliferation versus differentiation, the simple answer is that we do not know.

> Figure S1 - Although the effects of TrxT KO and dhd KO in male mbt tumors seem to be enhanced in relation to female tumors, the authors should include some form of tumor quantification for female tumors like in Fig 2 A. We have carried out the requested quantifications and added the results in a new panel in revised Figure S1A.

Moreover in the 2nd section of the results, relative to Fig 1S in "...Df(1)J5; l(3)mbtts1 female larvae although given the much less severe phenotype of female mbt tumours, the effect caused by Df(1)J5 is quantitatively minor." to say "quantitatively" minor, the authors should include not only quantifications, but a form of comparison between female tumors vs. male tumors. The requested quantification was published in Molnar et al., 2019. However, we agree on the convenience of doing it again with our new samples. The new data, that confirm published results, are now shown as a new panel in revised Figure S1C.

> - Fig 3D - The hierarchical clustering was done according to which parameters? A brief explanation could help a better interpretation of this results section. The requested information has been added to the Methods section. Hierarchical clustering was done using the function heatmap.2 in R to generates a plot in which samples (columns) are clustered (dendogram); genes (rows) are scaled by “rows"; distance = Euclidean; and hclust method = complete linkage. Expression levels are reported as Row Z-score.

> - Fig 3D - It could be beneficial for the authors to include an analysis of the downregulated genes shared between TrxT KO mbt tumors and dhd KO mbt tumors, as well as the genes that are not shared (besides MBTS genes). Could be something like a Venn diagram. Thanks for pointing this out. New Figure S3 shows the requested Venn diagram, as well as the list of enriched GOs for each group.There are no enriched GOs in the list of overlapping genes. TrxTKO; l(3)mbtts1-specific genes are enriched for GOs related to game generation, sexual reproduction, germ cell development and simlar GOs. dhdKO; l(3)mbtts1 -specific genes are enriched for GOs related to chitin, molting and cuticle development. Tantalising as they are, these observations do not immediately suggest any direct explanation for the different roles of Dhd and TrxT in long-term tumour development. We are happy to add these supplemental information, but we do not deem it worth of any further discussion at this point.

> - Results section 3 - "Expression of nanos is also significantly down-regulated upon TrxT loss, but remains unaffected by loss of dhd" - to corroborate the idea that TrxT and dhd work as a pair, but contribute to different functions within the tumor, it would be interesting for the authors to do an allograft experiment of dhd KO; l(3)mbt male tissue with nanos knock down in the brain, if genetically possible. The suggested experiment is published. The gene in question (nanos) is a suppressor of mbt tumour growth: In a nanos knock down background, l(3)mbt allografts do not grow (Janic 2010).

Minor comments: * > - In the first section of the results, the authors claim that "Consistent with the reported phenotypes of Df(1)J5...", but then the study is not mentioned.* The corresponding references (Salz et al., 1994; Svensson et al., 2003; Tirmarche et al., 2016) have been added.

> - Fig 1 B - It is a bit confusing to follow where TrxT and dhd are in the Genome browser view. I am guessing we should follow the TrxT-dhd locus from A, but the authors could make it clearer. Figure 1 has been changed to make this point more clear.

> - In the same section, in the next sentence, the homozygous and hemizygous is a bit confusing. "...homozygous TrxTKO females, dhdKO males, and TrxTKO males", should be corrected. We appreciate the suggestion, but would rather stick to classical terminology and refer to KO/KO females as homozygous and to KO/Y males as hemizygous.

>- In the same section (Fig 1C): "RNA-seq data also shows that TrxT is significantly upregulated in l(3)mbtts1 males compared to females (FC=7.06; FDR=1.10E-44) while dhd is not (FC=1.89; FDR=2.00E-14)." - But dhd is nevertheless upregulated, although less, in l3mbt males, right? The authors might need to rephrase. We refer to comparing males versus females, not wild type versus tumours. The text has been rephrased in the revised version to make this point clear.

> - Fig 2 A (quantifications), should be after the confocal images (Fig 2 B). We respectfully disagree on this minor point. We initially organised this figure in the order recommended by the reviewer, but we eventually found it easier to write the article using the order shown in the submitted figure. We would rather stick to this version.

> - Fig 2 B and Fig S1 - Please include an outline of at least neuroepithelia and, if possible, Central brain or medulla so that these regions can more clearly identified. Moreover, these results will be easier to interpret if you add a male symbol in this image and a female symbol in Figure S1, otherwise, it might seem like the same figure Outlines and symbols have been added to the revised figure, as required.

> - In results, section 2, "Consequently, in spite of the strong sex dimorphism of mbt tumours, the phenotype of Df(1)J5; l(3)mbtts1 larval brains is not sexually dimorph" - to back this up, quantifications of Df(1)J5; l(3)mbtts1 female vs male tumor size, as well as statistical analysis are needed, like previously said. The requested the new data is now shown in revised Figure S1C.

> - In results section 2 - "For allografts derived from, female larvae, we found that differences in lethality rate caused by TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1, Df(1)J5; l(3)mbtts1, and l(3)mbtts1 tissues (7-23%) were not significant (Figure 2C)" - there is no statistical analysis to conclude that the lethality rate is not significant, from 7% to 23% still seems like a difference. Thanks for pointing this out. We did of course generate the requested statistical analysis data, but failed to include it in the manuscript. Chi-square statistical test gives a p value=0.2346. These data have been added to the revised version.

> - Last paragraph of section 2 of results - very long and confusing sentence. Please rephrase text. We have rephrased this sentence to make it shorter and clearer.

> - On section 3 of results: "The vas, piwi and CG15930 transcripts are not significantly down-regulated following either TrxT or dhd depletion alone." - in Fig 3E, not only these transcripts seem to suffer a slight downregulation, but there is also no statistical analysis supporting this. There seems to be a misunderstanding here. The requested statistical data for each gene were shown in Table S1

> - First paragraph of section 3 results - the first sentence is written in a confusing way. Moreover, more context is needed in the sentence afterwards: "we first focused on transcripts that are up-regulated in male mbt tumour samples compared to male wild-type larval brains (mMBTS)." but using which data? The RNA seq data? Agreed; this paragraph has been amended in the revised version.

> - Brief conclusion missing on the second paragraph of the last section of results. As far as the results presented in this paragraph are concerned, we can only mention the two potentially interesting observations, which were pointed out in the original version: (i) the suggestion that nanos upregulation could be critical for sustained mbt tumour growth upon allograft, and (ii) the fact that three genes (vas, piwi and CG15930), also known to be required for mbt tumour growth, are downregulated in Df(1)J5; l(3)mbtts1, but remain unaffected following either TrxT or dhd depletion alone. We are unable to derive any other conclusion from these observations.

> - In the end of 3rd paragraph of last section of results: "...M-tSDS and F-tSDS genes is partially reduced in l(3)mbtts1 brains lacking either TrxT or dhd, but it is completely suppressed upon the lack of both." - "completely" might not be a correct word to use in this case, as there is still some small differences As requested, we have changed "completely" for "strongly".

> - 4th paragraph of last section of results: Either mention the male results and then female (to be in order with the figure, as the female graphs come after the male graphs) or change the order in the figure. Also, this paragraph is not very clear, could benefit from a better explanation of the results and conclusions. Point taken. Figure 4 has been changed and female graphs come before male graphs. The paragraph is clearer now. The conclusion from this paragraph is included in the final paragraph of this section.

> - Fig 4 C,D,E,F: to make it more clear, please write the name of the genotypes in question in the figure. At the reviewer's request, the genotypes in question are now written in each panel. Please note that we did not do so before because all four panels correspond to the same genotype: Df(J5); l(3)mbtts1 vs l(3)mbtts1, as we mentioned in the original figure legend.

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Referee #3

Evidence, reproducibility and clarity

Summary:

• In this manuscript, the authors address the role of the thioredoxins Dhd and TrxT in the development and growth of mbt tumors, a sexually dimorphic brain tumor that derives from the expansion of the neuroephitelium. To this end, the authors have successfully generated dhd and TrxT knock-out mutants using CRISPR-Cas9 and show that both dhd and TrxT individual knock-out partially reduces the mbt tumor-associated brain phenotype. Moreover, using Df(1)J5, a deficiency that affects both TrxT and dhd, the recovery of the phenotype is enhanced. However, although concomitant expression of dhd and TrxT is required for proper tumor development, they show that only TrxT is necessary for the growth of allografts derived from male l(3)mbt tumors. This is interesting, not only because TrxT and dhd are never co-expressed in physiological conditions, but also because this data suggests that the pathways leading to l(3)mbt tumor development are different from the ones that contribute to tumor proliferation and aggressiveness. Moreover, the authors show that TrxT and dhd contribute to the emergence of the mbt tumour signature (MBTS) and sex-dimorphic signature (SDS) of tumours by analysing transcriptomic data of TrxT KO; l(3)mbt, dhd KO; l(3)mbt and Df(1)J5; l(3)mbt. In fact, through hierarchical clustering, the authors show that male Df(1)J5; l(3)mbt brain transcriptomic profile becomes closer to wild-type brains than l(3)mbt ts1 tumors.

• This study presents novelty to the cancer research field and both the model and methodology used were appropriate. Nonetheless, this study deals with mbt tumors which are sexually dimorphic, as well as male and female germline-specific genes that in a tumor can alter male and female sex-dimorphic signatures, making this study very easy to become confusing to non-experts in the field if not written in a very clear way. Therefore, the text, especially in the results and discussion section, could be revised in general to improve the comprehension and flow of the manuscript, given that some sentences and paragraphs are hard to follow. In particular, the results section could benefit with more contextualization and a more detailed explanation of experiments. Moreover, the study is lacking some quantifications and a few additional experiments. These issues can certainly be addressed by reviewing the text as well as reorganizing and including a few quantifications and experiments as described below. I am an expert in Drosophila brain development and tumorigenesis.

Comments:

• In the first section of the results, as a first step to study the role of TrxT and dhd genes on mbt tumors the authors generate CRISPR knock outs of these genes and correctly validate them. However, afterwards, the experiment where the authors test the KO of these genes in a wild-type larva brain is not contextualized with the rest of the section. It might be best to first address the role of these genes in a tumor context and only then complement with the experiments in wild-type (in supplementary material).

• Fig 2 B - To back up the quantifications in Fig 2A the authors could include images of l(3)mbt ts1 tumors with TrxT KO and dhd KO also.

Fig 2 B and C - Indeed, the results suggest that TrxT seems to be responsible for most tumor lethality upon l(3)mbt allografts, but not dhd. This is curious since l(3)mbt; dhd KO brain tumors have the same partial phenotype as l(3)mbt; TrxT KO (fig 1A). It would be interesting to further explore these phenotypes by staining l(3)mbt; TrxT KO and l(3)mbt; dhd KO brains with, for instance, PH3 to understand if the number of dividing cells of these tumors could be different. In addition, to back up this information, the authors could look at what happens to l(3)mbt tumors with TrxT KO and dhd KO at a later stage of development (or to larva or pupa lethality if that is the case) and compare it with l(3)mbt brains.

• Fig 2 B - What happens to the medulla in a l(3)mbt brain tumor? Although the ratio of NE/BL is the same for wild-type and D(1)J5; l(3)mbt, it still seems that the medulla in D(1)J5; l(3)mbt brains is substantially bigger, although quantifications would be required. Do the authors know if the NE in D(1)J5; l(3)mbt brains is either proliferating less or differentiating more?

• Figure S1 - Although the effects of TrxT KO and dhd KO in male mbt tumors seem to be enhanced in relation to female tumors, the authors should include some form of tumor quantification for female tumors like in Fig 2 A. Moreover in the 2nd section of the results, relative to Fig 1S in "...Df(1)J5; l(3)mbtts1 female larvae although given the much less severe phenotype of female mbt tumours, the effect caused by Df(1)J5 is quantitatively minor." to say "quantitatively" minor, the authors should include not only quantifications, but a form of comparison between female tumors vs. male tumors.

• Fig 3D - The hierarchical clustering was done according to which parameters? A brief explanation could help a better interpretation of this results section.

• Fig 3D - It could be beneficial for the authors to include an analysis of the downregulated genes shared between TrxT KO mbt tumors and dhd KO mbt tumors, as well as the genes that are not shared (besides MBTS genes). Could be something like a Venn diagram.

• Results section 3 - "Expression of nanos is also significantly down-regulated upon TrxT loss, but remains unaffected by loss of dhd" - to corroborate the idea that TrxT and dhd work as a pair, but contribute to different functions within the tumor, it would be interesting for the authors to do an allograft experiment of dhd KO; l(3)mbt male tissue with nanos knock down in the brain, if genetically possible.

Minor comments:

• In the first section of the results, the authors claim that "Consistent with the reported phenotypes of Df(1)J5...", but then the study is not mentioned.

• Fig 1 B - It is a bit confusing to follow where TrxT and dhd are in the Genome browser view. I am guessing we should follow the TrxT-dhd locus from A, but the authors could make it clearer.

• In the same section, in the next sentence, the homozygous and hemizygous is a bit confusing. "...homozygous TrxTKO females, dhdKO males, and TrxTKO males", should be corrected.

• In the same section (Fig 1C): "RNA-seq data also shows that TrxT is significantly upregulated in l(3)mbtts1 males compared to females (FC=7.06; FDR=1.10E-44) while dhd is not (FC=1.89; FDR=2.00E-14)." - But dhd is nevertheless upregulated, although less, in l3mbt males, right? The authors might need to rephrase.

• Fig 2 A (quantifications), should be after the confocal images (Fig 2 B).

• Fig 2 B and Fig S1 - Please include an outline of at least neuroepithelia and, if possible, Central brain or medulla so that these regions can more clearly identified. Moreover, these results will be easier to interpret if you add a male symbol in this image and a female symbol in Figure S1, otherwise, it might seem like the same figure if one does not properly read the legend.

• In results, section 2, "Consequently, in spite of the strong sex dimorphism of mbt tumours, the phenotype of Df(1)J5; l(3)mbtts1 larval brains is not sexually dimorph" - to back this up, quantifications of Df(1)J5; l(3)mbtts1 female vs male tumor size, as well as statistical analysis are needed, like previously said.

• In results section 2 - "For allografts derived from female larvae, we found that differences in lethality rate caused by TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1, Df(1)J5; l(3)mbtts1, and l(3)mbtts1 tissues (7-23%) were not significant (Figure 2C)" - there is no statistical analysis to conclude that the lethality rate is not significant, from 7% to 23% still seems like a difference.

• Last paragraph of section 2 of results - very long and confusing sentence. Please rephrase text.

• On section 3 of results: "The vas, piwi and CG15930 transcripts are not significantly down-regulated following either TrxT or dhd depletion alone." - in Fig 3E, not only these transcripts seem to suffer a slight downregulation, but there is also no statistical analysis supporting this.

• First paragraph of section 3 results - the first sentence is written in a confusing way. Moreover, more context is needed in the sentence afterwards: "we first focused on transcripts that are up-regulated in male mbt tumour samples compared to male wild-type larval brains (mMBTS)." but using which data? The RNA seq data?

• Brief conclusion missing on the second paragraph of the last section of results.

• In the end of 3rd paragraph of last section of results: "...M-tSDS and F-tSDS genes is partially reduced in l(3)mbtts1 brains lacking either TrxT or dhd, but it is completely suppressed upon the lack of both." - "completely" might not be a correct word to use in this case, as there is still some small differences.

• 4th paragraph of last section of results: Either mention the male results and then female (to be in order with the figure, as the female graphs come after the male graphs) or change the order in the figure. Also, this paragraph is not very clear, could benefit from a better explanation of the results and conclusions.

• Fig 4 C,D,E,F: to make it more clear, please write the name of the genotypes in question in the figure.

Significance

This study presents an interesting new concept for Drosophila tumors, the cancer germline genes, which to my knowledge has been a poorly explored field, although it has a lot of potential. It is particularly interesting since it addresses the role of two germline specific thioredoxins, that are dispensable for somatic cells, but have a critical role in somatic mbt tumors, exploring new tumor vulnerabilities. This manuscript will benefit researchers in the field of cancer biology, in particular, to better understand cancer-testis (CT) genes and how they promote tumorigenesis, since the biological function for the most part remains unclear.

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Referee #2

Evidence, reproducibility and clarity

The manuscript by Molnar and colleagues is a follow-up from the authors' previously published work (Molnar et al 2019), where they demonstrated differential sex-linked gene expression in Drosophila l(3)mbt brain tumours and identified the thioredoxin proteins TrxT and Dhd in the mbt tumour signature (MBTS). In the current manuscript, the authors generated genetic mutants for both genes using CRISPR TrxTKO and dhdKO and a deficiency that spans both genes (Df(1)J5) to understand the role played by these thioredoxins in normal larval brain development and l(3)mbt tumour development. Both genes were found to be largely dispensable for normal larval brain development, however the authors uncovered a role in l(3)mbt tumour growth and development. Interestingly, although both TrxT and Dhd were required for l(3)mbt tumour development, they appeared to have distinct roles in long-term tumour growth, as assessed by allograft-induced lethality. Furthermore, the authors also investigated the link between the sexually dimorphic signatures of l(3)mbt tumours and the thioredoxins and suggest that both genes are required for the differential gene expression observed between the sexes.

Some of the conclusions are fairly well supported by the data presented. However, there are some aspects that are potentially not fully explored and that would provide more weight to the claims made by the authors. Some of these can be addressed by clarifications made in the text and/or figures and others would benefit from additional immunofluorescence staining experiments.

Specific comments are provided below.

1. Figures should include information regarding the sex of the larvae, particularly as there has been a previously reported sex-linked effect in the phenotypes analysed. (e.g. in Figure 2 and Figure S1, where Indication of the sex of the animals should be provided in the figure and not just in the figure legend).

2. Data regarding fertility. Can this be shown in a table format? Are dhdKO females fully sterile? What are the fertility levels of Df(1)J5?

3. Are dhd and TrxT the only genes affected by Df(1)J5? Is there transcriptional data from Df(1)J5 animals to suggest that nearby genes are not affected by the deficiency? Of particular interest would be to assess if snf is affected or not as it is a known regulator of gene expression and splicing.

4. In Figure 1C, statistical test plus indication of significance is not presented.

5. Related to Figure 1D. Additional neural markers could be assessed in dhdKO and TrxTKO flies. Whilst the gross morphology of the brain does not seem to be affected, there is a possibility that cell specification is affected. Specific markers for the NE, MED and CB could be used to assess this in more detail, particularly as the DE-cad images shown for dhdKO and TrxTKO flies seem to differ slightly from the control.

6. Related to Figure 2A, images from TrxTKO; l(3)mbtts1, dhdKO and l(3)mbtts1 should be added at the very least in a supplementary figure. Additionally, data for NE/BL ratio should be provided for dhdKO, TrxTKO and Df(1)J5 in the absence of l(3)mbtts1 tumours. Related to Figure S1, quantification of NE/BL ratio for female lobes should be added to the figure.

7. Related to Figure 2B and Figure S1, three rows of images are presented for each genotype. It is unclear whether these correspond to brain lobes from different larvae or different confocal planes from the same animal. This should be clarified in the figure and/or figure legend. Related to this, in addition to the anti-DE-cadherin data, it would be informative to include immunofluorescence data using antibodies such as anti-Dachshund (lamina), anti-Elav (medulla cortex) and anti-Prospero (central brain and boundary between central brain and medulla cortex) (as assessed in e.g. Zhou and Luo, J Neurosci 2013) in the mbt tumour situation to accurately describe regions disrupted by the tumours.

8. Authors should clarify how the NE was defined when mbt tumours are generated, as it is severely affected. From the images provided, it is unclear which region corresponds to NE or how the NE/BL ratio was measured. It would be helpful to outline these regions in the images or, as mentioned above, use antibodies to define them.

9. Figure 2C does not have indication of statistical significance for the comparisons stated in the text. Potential explanations for the different roles of Dhd and TrxT in long-term tumour development should be explored in the discussion. Related to this, does the analysis of the RNA-seq data from TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 animals reveal why they have similar effect on mbt tumour development but do not synergistically contribute to long-term growth?

10. Authors should clarify if there is any overlap between the affected M-tSDS and F-tSDS in the TrxTKO; l(3)mbtts1 and dhdKO; l(3)mbtts1 conditions. Would the limited overlap suggest that TrxT and dhd act in parallel rather than synergistically? This might also explain the differential effects on long-term tumour development. Additionally, the stronger effect observed in Df(1)J5 animals may be due to TrxT and dhd functional redundancy. Currently, there is limited evidence to suggest that TrxT and dhd act synergistically to regulate mbt tumour growth based on the presented data.

11. Authors should include a Venn diagram depicting affected genes (M-tSDS and F-tSDS) in the TrxTKO; l(3)mbtts1, dhdKO; l(3)mbtts1 and Df(1)J5; l(3)mbtts1 genotypes as this could clarify the percentage of overlap of gene signatures in these different conditions. Related to this point, authors could provide results from GO analysis to investigate whether specific functional clusters are altered in the different conditions.

12. In Figure 3E, authors should indicate more explicitly in the figure panel and/or figure legend which genes display significant differences in expression in the different samples.

13. In Figure S2C-F it is not clear if the graphs represent data from all tissues or data from male and female tissues separately, as shown in Figure 4.

14. Are TrxT and dhd also deregulated in other tumour types? Or is this specific for mbt tumours? This information could be provided to enhance the scope of the manuscript.

15. Authors conclude that TrxT and dhd cooperate in controlling gene expression between wild-type and tumour samples and that they act synergistically in the regulation of sex-linked gene expression in male tumour tissue. However, the link between the two observations (if indeed there is a link) has not been well explained. Is the effect on gene expression in tumours simply a result of the regulation of sex-linked transcription?

Significance

The current manuscript provides additional information regarding the regulation of mbt tumours and establishes TrxT and Dhd as potential cancer-germline genes in Drosophila. This will be of interest to researchers studying basic mechanisms of tumourigenesis and could potentially lead to identification of genes that could serve as biomarkers of disease. However, for this, a more general role of TrxT and Dhd needs to be established, as well as their potential conserved role as cancer-germline genes needs to be established.

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Referee #1

Evidence, reproducibility and clarity

Two cancer-germline (CG) genes encoding the Drosophila thioredoxins Deadhead (Dhd) and Thioredoxin-T (TrxT) are located head-to-head in the X chromosome. Cristina Molnar and coworkers investigate the effects of Dhd and TrxT in brain tumours of either sex caused by mutations in l(3)malignant brain tumour (l(3)mbt). Using CRISPR/Cas9-mediated knock-out alleles and RNA-seq, they demonstrate that, although both TrxT and Dhd are not required for normal brain development, they have a significant but partial effect on l(3)mbt brain tumour development, that is stronger in male than in female larval brains. However, allograft experiments show that only TrxT plays a significant role in long-term, sustained tumour growth. TrxT and dhd play a synergistic contribution role in development of mbt tumours and in the emergence of l(3)mbt tumour-linked transcriptomic signatures.

Major comments:

Most of the work in this paper is well conducted and the key conclusions are convincing. I think that the number of the replicates/animals for the experiments described in Figures 1 and 2 should be reported either in the figure legends or in the methods (statistical analysis). A relevant part of the discussion repeats what the authors have already said in the results. I would recommend to reorganize this section, emphasizing the importance of these results in the context of human brain tumors.

Significance

This work provides the first instance of an X-linked, head-to-head cancer-germline gene pair in Drosophila showing that these genes are dispensable for somatic cell development but have a crucial role to prevent malignant growth. Importantly, in humans, cancer germline genes and cancer testis (CT) genes have been involved in a wide range of cancers and about half of CT genes are located on the X chromosome. Thus, findings in this paper would be of interest to a broad audience that includes all the scientists studying the molecular mechanisms leading to cancer development.

The following keywords describe my expertise: Drosophila genetics, cell division, cancer genetics. I have less expertise to evaluate transcriptomics.

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Reply to the reviewers

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

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Referee #2

Evidence, reproducibility and clarity

Biddie et al. address the important question of what genomic annotations are relevant to the fine-mapping of trait-associated variation. They assessed data identifying DNase I hypersensitive sites, footprints, H3K27ac and other ChIP-seq peaks, ATAC-seq peaks, and eRNA locations using a benchmark set of allelically imbalanced DNase I hypersensitive sites and ChIP-seq peaks, and MPRA data. They find that a combination of DNase footprints and eRNA locations gives high enrichment for functional variants (albeit with low sensitivity) and demonstrate their FINDER on 53 traits from the GWAS catalog.

I have some questions to address before publication, all of which relate to clarifying the description in the manuscript.

1. I found this line in the abstract unclear: "This signature provides high precision, trading-off low recall".
2. Figure 1C is missing a y-axis label and a colour legend.
3. The authors note a high genomic coverage "by ATAC-seq (75.2%), [and] H3K27ac (61.5%)", which they attribute in part to "too low a threshold used in peak calling". However, both the benchmark datasets and the genomic predictors are utilized without consideration of the effect of thresholding. To what extent are DNase footprints and eRNA specifically informative, vs. representing datasets processed with highly selective cutoffs?
4. The benchmark datasets are described as molQTL, bWTL, and caQTL. "QTL" implies a regression of a trait (e.g. accessibility) on a genotype. This is not accurate here: the Vierstra and Abramov datasets investigate allelic imbalance (a related but orthogonal approach), while van Arensbergen is an MPRA.
5. QTLbase is cited alongside the Vierstra paper. I had some trouble searching in QTLbase but did not find the Vierstra dataset. It should be clarified whether QTLbase was used to download the Vierstra results, or to supplement it with other studies.
6. Fig. 4 discusses the effect of variant centrality in a DHS for prioritization, but it isn't included in the FINDER schematic in Fig. 7. How come it wasn't employed in FINDER?
7. The Discussion notes "Firstly, the identification of DNase footprints may be related to residency time of TFs on DNA, where rapidly exchanging factors impart poor footprints (Sung et al., 2014). Variants associated with altering binding of dynamic factors may therefore be missed. To overcome this, detection of footprints could be improved by enzymatic digestion bias correction". I don't see how enzymatic digestion bias is related to sensitivity to detect rapidly exchanging TFs.
8. It looks like the eRNA data were obtained from GRO-seq or PRO-seq data. It would be helpful to note key details like this directly rather than leaving it to the reader to try to figure out what is in the PINTS database.
9. The github link https://github.com/sbiddie/FINDER gives a 404 not found error. Is FINDER an actual tool implementation, or more generally describing the approach?

Minor comments:

1. Some of the figure text is quite small or blurry (e.g. Fig. 1A/B, Fig. S2).
2. Typo in Figure 1A legend: "Heatpmap".
3. The author of the last entry in the References is "Zhen Z" but should be "Zheng Z".

Significance

This work is highly relevant and well-done and provides practical information to guide future fine-mapping studies. The authors partially address the tradeoff between enrichment and recall, which is frequently swept under the rug. Their approach ought to be of high interest to the broad genetics and gene regulation communities.

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Referee #1

Evidence, reproducibility and clarity

Summary: Disease and trait associated genetic variation is primarily localizes to non-coding regulatory DNA. A wide-variety methods and assays are routinely used to delineate putative regulatory elements. In this manuscript Bidde et al. sought to evaluate which of these assays is useful for identifying and prioritize trait-associated regulatory variation. To these ends the authors perform enrichment analysis on a genetic variation from different sources encompassing both molecular phenotypes (QTLs) and trait-associated variation via GWA-studies. The authors show that genetic variants localizing to DNase I footprints and within elements associated with RNA production (enhancer RNA) are maximally enriched for both molQTLs and trait-associated variation vs. other markers of regulatory DNA. Overall, I find that this manuscript is technically sound, and is consistent with prior studies (namely the enrichment of GWAS variants within DNase I footprints -- Vierstra et al. 2020). I suggest only a few additional analyses and edits to the presentation.

Major comments:

1. The authors should expand the QTL studies and the GWAS variants via LD and recompute the enrichments. For example, I would take all variants in high LD (r2 > 0.8 or 0.9) with either a QTL or GWA-variant. This will likely increase total variants overlapping an annotation, but reduce overall enrichment (odds-score), and possibly provide some information about which chromatin marks are more associated with "causal" variants.
2. Can the authors comment on why eRNAs seem to be such a strong marker of functional variation? Are these just "strongest" (most accessible) distal elements? I would assume that these peaks have high overlap with chromatin accessibility peaks.
3. Would the ATAC-seq enrichment increase if the authors stratified regions by signal rather than aggregating all peaks? The vast majority of chromatin accessibility peaks are very weak and could be false-positives. Lets imagine that in each dataset 1% of peaks are FPs and that the FP peaks are mostly randomly distributed accross the genome. As such, aggregating hundreds to thousands of samples would have many FP peaks and greatly affect the enrichment analysis. Conversely, DNase I footprints are found in high signal peaks that are less likely to be false-positives. One approach to deal with this is to select ATAC-seq peaks matched to the peak signal in DHS peaks with footprints.

Minor comments:

1. Figure 1c -- no legend is provided specifying what the bar colors represent.
2. Pg. 10 -- "To overcome this, detection of footprints could be improved by enzymatic digestion bias correction (Calviello et al., 2019)." The DNase I footprinting dataset used in this paper performs extensive bias correction using a 6mer statistical model. Nevertheless, I completely agree the sentiment of the authors that low and variable sensitivity of footprinting is certainly driving a high false-negative rate with regards to comprehensively identifying function variants.
3. Figure 3 is a little too complicated for its purpose, which is to show the enrichment of bQTLS, caQTLs and raQTLs.

Significance

This manuscript provides a rigorous analysis characterize how various markers of chromatin help aid in the interpretation of non-coding genetic variation. The findings are not entirely novel, however, the analyses and approaches described are nevertheless useful for variant prioritization. This manuscript is broadly applicable and useful to anyone interested studying non-coding genetic variation.

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

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Reply to the reviewers

Reviewer #1

The paper by Yammine et al addresses a major problem in peculiarities of genotype to phenotype manifestation in collagen II and chondrodysplasia. It is a lucid and comprehensive study detailing what they see as the fundamental mechanism of Gly1170 Ser mutated Col2a1 gene.

At the heart of the matter is the debunking of the results from a mouse model generated by liang et al (Plos one 2014) paper in which the authors suggested that the phenotype seen only homozygous mice (heterozygous mice appear normal), was related to ER stress -UPR-apoptosis cascade resulting in the chondrodysplasia. Yammine et al paper uses a different model, a robust human iPSC-based tissue, with a CRISPRed variant show that despite the ability of the variant chondrocytes to deposit a Gly1170Ser-substituted collagen II in both the hetero- and homozygous models, is not accompanied by any substantive UPR. The authors of this current paper also argue that their model system is most closely resemble the human context, where heterozygous individual show pathology.

We appreciate the Reviewer highlighting the significance of this manuscript addressing a major issue in the field.

I have sieved all the data related to this topic and have gone back to examine the data and what struck me was the repeated use of the phrase "slow to fold" in the current paper and wondered whether the element of "TIME" is as important in the chondrogenesis of either models and it is this element that generate the difference between the two results? While iPSC-based tissue takes up to 44 days, a female mouse would have had two litters in this time and made many more growth plates. Could it be by "slowing" the chondrogenesis pathway, which is part of the procedure of differentiation of iPS cells into chondrocytes, the ER is not as "stressed" as in mouse development? I would like the authors to reflect and comment and put forward their view given UPR signaling pathways play a crucial role in chondrocytes in phases of high protein synthesis, e.g., during bone development by endochondral ossification (Journal of Bone Metabolism, vol. 24, no. 2, pp. 75-82, 2017).

The Reviewer here emphasizes a likely benefit of the human model that we had not previously considered, as differentiation and growth in our model are indeed far more similar to humans than the rapid timeline in mice. We also note that the evidence that collagen is slow to fold comes from the gold standard assay in the field for collagen folding rate, a point discussed in greater detail in response to Reviewer 2’s query (see below).

The literature evidence does indicate that transient UPR signaling is relevant for chondrogenesis. We selected UPR timepoints that do not interface with the differentiation process, but rather the tissue deposition process while chondrocytes are still actively depositing and maintaining the extracellular matrix, to be able to distinguish a physiological transient UPR during differentiation from a potential chronic and possibly pathologic one. We now clarify this point in the manuscript (see text below).

“These timepoints were selected to reflect an early and a late stage of cartilage maturation, but with both timepoints harvested post-chondrogenesis so as not to interfere with the physiologic transient UPR activation that can be important in that process.”

This is not withstanding the good argument given by the authors in defending their robust results, namely that the there is no evidence that the hydrophilic triple-helical domain of pro-collagen binds BiP, the main detector of accumulated misfolded proteins. What then do they make out of the immunostaining and qPCR with ER stress related genes in Liang et al paper?? I know that the data is not theirs but a comment on the indisputable data gives the reader a better understanding.

It is critical to note that the evidence for ER stress that induces the UPR is, at best, exceptionally weak for heterozygotes in the Liang et al paper, and arguably also weak for homozygotes. Liang et al observed, via quantitative PCR, that the mRNA levels of just Chop (which is also a marker of the integrated stress response and not a good readout for UPR activity) and ATF6 (whose RNA-level upregulation is not a standard marker of the UPR) were significantly upregulated in the disease-relevant heterozygous mice – given that other (more valid) UPR markers were not altered, this is not so different from our observation of a lack of UPR in the disease-relevant heterozygotes.

A somewhat more comprehensive set of UPR markers, including Chop, Xbp1(Total and Spliced), Grp78 (BiP), ATF4, and ATF6, was significantly upregulated only in homozygous mice compared to wild-type. PERK is one of many kinases upstream of ATF4 and Chop that can be activated by a variety of processes (the pathway is part of the integrated stress response, for example). Moreover, transcriptional upregulation of ATF4 (which is actually induced translationally, not transcriptionally) and ATF6 (which is actually induced proteolytically, not transcriptionally) are not normally used to read out UPR activation, so it is not so clear to us that a robust UPR was induced even in homozygotes. Moreover, there was not a substantial increase in Xbp1-S (S = spliced) relative to Xbp1-T (T= total) in the study of homozygous mice, which is the most appropriate measure of UPR activation – rather than change in Xbp1-T and Xbp1-S. The use of mostly non-standard genes to assess UPR induction, the weak upregulation of BiP (2.5-fold), and the unchanged ratio of Xbp1-S to Xbp1-T raise some questions regarding UPR induction even in the homozygotes. Regardless of these homozygote data, as noted above, the evidence for a UPR in heterozygotes is very weak, despite ER stress being the focus of the Liang et al paper.

With respect to immunostaining, Liang et al observed that tissue from homozygous mice (but not heterozygotes) contained significantly more apoptotic cells. Apoptosis could be a result of chronic, unresolved UPR signaling, but it could also result from any number of other pathways and is certainly not direct evidence for UPR-inducing ER stress. Additionally, for the homozygote apoptosis assay, Liang et al do not note how many mice were analyzed for each genotype, a value they did report for their other assays. While examining multiple sections for each genotype is valuable (they state ≥10), the assessment of biological replicates (additional mice) seems critical to confidently reach a conclusion.

Although I understand the choice of cell lines for overexpression, the transfection of the HT-1080 cells using wild-type and Gly1170Ser COL2A1encoding plasmids are not a match to the in vivo model (variation of efficiency, etc.) the appearance of BiP even at a lower fold increase does not negate ER stress, as the authors acknowledge but more important is what other paracrine signals which triggers the UPR signally pathway which is not linked to BiP? or an iPS system may lack? Is there anything else not only ATF6α (activating transcription factor 6 alpha), but IRE1α (inositol-requiring enzyme 1 alpha), and PERK (protein kinase RNA-like endoplasmic reticulum kinase).

Our finding that the UPR is not activated is based on comprehensive RNA-sequencing performed in the physiologically more relevant iPSC-derived chondrocyte, as opposed to the tumor cell line HT-1080. Our interactomic finding that BiP interacts to the same extent with wild-type and Gly1170Ser procollagen-II (in HT-1080 cells) strongly supports our proposal that the reason the UPR is not activated is that BiP fails to recognize unfolded triple-helical domains.

We note that, although HT-1080 cells are not a perfect match, they are the most accessible option for interactome-based studies. Because there is no MS-grade antibody for collagen-II IP, we need to IP a transfected, tagged collagen. We cannot do this in chondronoids, or in isolated chondrocytes that transfect poorly and rapidly dedifferentiate. Critically, Prockop and co-workers extensively validated HT-1080 cells as a platform for fibrillar collagen biochemical studies in Matrix 1993, 13, 399. Our own lab further characterized their capacity to properly handle fibrillar collagen variants in great molecular detail in ACS Chem Biol 2016, 11__, __1408.

Since our chondronoid system contains only chondrocyte cells, as is the case in cartilage, the cells can receive paracrine signals from other chondrocytes, but not other cell types. In joints within a whole animal, it is true that paracrine crosstalk occurs between different cell types of different tissues, including inflammatory cells for example. The chondronoid is very useful for elucidating the defects that occur at the chondrocyte-level, without confounding secondary effects. At the chondrocyte-level, Gly1170Ser-substituted procollagen-II does not activate the UPR.

The Reviewer’s comment regarding the absence of paracrine signals in an iPSC-based system is well-taken, and we added discussion as follows:

“These observations indicate that the chondrocytes were not raising such stress responses, at least when examined in the absence of paracrine signals from other cell types in the joint.”

The authors have given us plenty of alternatives that are relevant, and they prepared us for yet another paper on articular cartilage using iPS tissue model which I am looking forward to.

We are also excited about the upcoming potential of this model system!

Significance

I think this paper is publishable and it is important in understanding the mechanism by which mutation in collagen type II affect chondrogenesis and therefore bone formation. This paper will appeal to musculoskeletal scientist especially those who are interested in bone and its pathology. It would be important for the authors to respond to the critique of "TIME" and speed of protein synthesis which create a duress in the ER pathway.

We greatly appreciate the Reviewer’s comment again on the significance of this work, and their scholarly input which has substantially improved the paper. We hope they will agree that the manuscript is now ready for publication.

Reviewer #2

Evidence, reproducibility and clarity

*System: The investigators have used a human iPSC chondrocyte model system to investigate the biochemistry of the Chondrodysplasia caused by the p.Gly1170Ser mutation in the type II collagen gene (COL2A1). They studied presumably homogeneous chondronoids formed by 3 cell lines they previously reported in which the chondrocytes were either homozygous wild type for the gene, homozygous for the Cas Crispr induced mutation or heterozygous for the two alleles (their refs 42-45). In addition, they utilized cultured HT1080 human fibrosarcoma cells transfected with wild type and mutant Col2A1 to study differences in the interactomes of the two proteins.

*

*Analytic Parameters: They investigated the extracellular matrix formed by the three cells using collagen and proteoglycan staining and TEM and the transcriptional responses in chondronoids expressing the wild type and mutant genes.

*

*Observations: matrix formation was defective in the two mutation bearing cell populations, reflecting defective fibril formation proportional to the abnormal gene dose. They found increased accumulations of post-translational modifications (hydroxylation, and O-glycosylation) on the mutant collagen extracted from the chondronoids and EM evidence of collagen retention in the ER. They studied the comparative transcriptional profiles in the three phenotypes and failed to find a profound UPR response late in culture and only a mild upregulation of UPR genes in the young cultures. They could not find evidence for activation of the ISR except in the homozygous mutant cells.

*

*Using transfected HT-1080 cells (previously shown by these investigators not to express endogenous pro-collagen II but able to synthesize transfected pro-collagen genes) they were able to study the comparative wt and mutant pro-collagen interactomes.

*

Conclusions: They conclude that the p.gly1170ser mutation in Col2A1 results in abnormal folding which results in trapping of the protein in the ER and some interaction with cellular elements of the proteostatic response. They concluded that the cellular proteostasis machinery can recognize slow-folding Gly1170Ser through increased interactions with certain ER network components but not in the same fashion that has been described for liver cells producing mutated versions of high volume secreted proteins.

We appreciate this careful summary of our work.

*Major comments:

*

Their first conclusion, stated in the abstract, "Biochemical characterization reveals that Gly1170Ser procollagen-II is notably slow to fold and secrete." that the mutant polypeptide chain is slower folding than the wild type chain is based on the premise that the longer the chains are in the ER the greater the degree of lysine hydroxylation and O-glycosylation. Although this may be true, they do not provide a reference and I could not find a definitive description of the phenomenon. Their reference 48 only discusses the occurrence of intracellular post-translational modification of the lysines and continuing modification extracellularly but does not relate these phenomena to the rate at which the peptides traverse the cell. I think the reader would benefit from seeing experiments in which the rate of folding and secretion of the wild type and mutant chains are measured and the degree of post-translational modification are compared. Cabral WA et al showed differences in collagen folding and secretion rates in cyclophilin wt, knockouts and heterozygotes osteoblasts and fibroblasts by western blots. (2014) Abnormal Type I Collagen Post-translational Modification and Crosslinking in a Cyclophilin B KO Mouse Model of Recessive Osteogenesis Imperfecta. PLoS Genet 10(6): e1004465. doi:10.1371 / journal.pgen. 1004465). Performing such experiments in their chondronoids would confirm the authors' interpretation that the increased post-translational modification portrayed in their figure 4 reflects slowed folding and secretion related to the mutation.

We apologize for failing to provide essential background references and information to assess our assay for slow folding/secretion of procollagen. In fact, slow migration on SDS-PAGE is not only a widely used assay for comparing the rate of folding of procollagens, it has also remained the gold standard in the field for the past forty years. The studies cited below are some of the seminal papers in the field linking collagen’s rate of folding with its extent of posttranslational modifications and its electrophoretic mobility. We have now updated our citations accordingly.

1. Bateman, J.F.; Mascara, T.; Chan, D.; Cole, W.G. “Abnormal type I collagen metabolism by cultured fibroblasts in lethal perinatal osteogenesis imperfecta” Biochem J 1984, 217, 103.
2. Bonadio, J.; Holbrook, K.A.; Gelinas, R.E.; Jacob, J.; Byers, P.H. “Altered triple helical structure of type I procollagen in lethal perinatal osteogenesis imperfecta” J Biol Chem 1985, 260, 1734.
3. Bateman, J.F.; Chan, D.; Mascara, T.; Rogers, J.G.; Cole, W.G. “Collagen defects in lethal perinatal osteogenesis imperfecta” Biochem J 1986, 240, 699.
4. Godfrey, M.; Hollister, D.W. “Type II achondrogenesis-hypochondrogenesis: Identification of abnormal type II collagen” Am J Hum Genet 1988, 43, 904. The basis for this collagen-specific assay of folding rate is that the ER-localized procollagen proline and lysine hydroxylases require monomeric collagen strands as substrates, and cannot accommodate a folded triple helix in their active sites. Thus, accumulation of post-translational modifications on collagen depends on the procollagen triple-helical domain’s residence time as an unfolded monomeric region of the assembling triple-helical trimer within the ER. Some fraction of the hydroxylated lysines are later glycosylated, which slows migration on SDS-PAGE gels. We have now clarified our slow folding conclusion with more precise references and discussion in the manuscript.

Pulse-chase experiments like those suggested by the Reviewer would indeed be beneficial if they were possible in this system, but they simply are not. Although it might be possible to soak in a radiolabeled amino acid over a short time period, the assay still relies on separating the cell fraction from the secreted fraction. This is possible in monolayer cultures, but in a chondronoid composed of complex cartilage and cells we have no way to do it. One could propose that we extract the chondrocytes and then do the pulse-chase in a monolayer culture, but this unfortunately is also not possible as chondrocytes do not behave well outside the tissue setting and rapidly differentiate into other cell types. Fortunately, the procollagen overmodification assay is a widely used and well-accepted measure of slow folding, and thus addresses the issue.

I think Figure 4 needs more explanation for the reader. While, as expected, the homozygous mutant band is much slower than the homozygous wild type band, in the heterozygotes the band is intermediate rather than showing a discrete mixture of wild type and mutant proteins, reflecting different degrees of post-translational modification. Is this a function of mixed triple helices with heterogeneous degrees of post-translational modification? It deserves more comment, since the argument relating the degree of post-translational modification to the rate of folding is dependent on this observation. It would also be helpful to show the whole gel with collagen II markers.

We modified Figure 4 __to show the whole gel (in the SI, see __Fig. S3) and molecular weight markers. It also shows the wild-type collagen-II band. Most of the procollagen produced by the heterozygote is heterotrimeric for the disease-causing substitution (>87% of trimers will contain at least one mutant chain and thus experience delayed folding) and, therefore, the diffuse banding structure is to be expected. Further, we would speculate that in these challenged ER, even the folding of wild-type only trimers is impaired. The Reviewer’s comment suggests there may be some basis for that speculation. We added a note to this effect.

“The presence of a single broad, slow-migrating band as opposed to distinctive overmodified mutant versus normally modified wild-type strands is due to fact that the vast majority of trimers formed in heterozygotes (>85%) contain at least one Gly1170Ser strand that delays triple-helix folding.”

Another approach to the question of intracellular accumulation due to a slow rate of folding of the mutant collagen would be to perform pulse chase labeling of the three types of chondronoids with radiolabeled amino acids and sugars and processing the media and lysates with analysis using antibodies specific for the two collagen chain types. Given the authors extensive experience in studying collagen biosynthesis (e.g. Chan et al J. Biochem. Biophys. Methods 36 (1997) 11-29), such a supporting study would firmly establish whether the rate of folding/secretion differs between the wt and the homozygous and heterozygous chondroidinomas. Until the slow folding can be directly demonstrated in a quantitative fashion rather than by monitoring the secondary phenomenon of post-translational modification the hypothesis remains unproven.

Discussed above in response to the Reviewer’s earlier suggestion of pulse-chase and question regarding the post-translational modification assay, unfortunately the pulse-chase experiment is infeasible. Fortunately, the modification-based assay is already the gold standard in the collagen field.

Another issue that does not appear to be addressed is the consequence of having misfolded collagen chains in the dilated ER. Liang et al, using mice transgenic for one or two copies of the mutant human gene showed apoptosis in the homozygotes but not in the hets a finding similar to that of Kimura et al using transgenics carrying a different human COL2A1 mutation. Okada et al, using chondrocytes converted from human fibroblasts with clinical collagenopathy (heterozygous), although not the same mutation as in the present study, showed dilated ER and some level of apoptosis in the cultured cells. Hintze et al, examining chondrocytes expressing different mutants associated with different forms of spondyloepiphyseal dysplasia, suggested that the degree of stability of the mutations might determine whether apoptosis occurred, i.e. the thermolabile p.R989C was associated with apoptosis while cells expressing the more thermostable mutants p.275C, P.719C and p.G853E did not reveal any evidence for ongoing apoptosis R989. Is it possible that the smaller size of the homozygous chondronoids reflect fewer cells rather than less matrix (or both) as result of apoptosis? Examination of the chondronoids with reagents for caspase 3 or Tunel staining. One could also measure by Col/DNA ratio in wt, hets and homos. It might also have been useful for these experiments been more quantitative, i.e. by cell sorting rather than by eye. Would ImageJ software been helpful?

We greatly appreciate this suggestion. We now added results of TUNEL assays performed on sections of the chondronoids (see Fig. 8), including quantification of the results. Notably, we do not observe a significant difference in apoptosis between genotypes at the timepoint considered. This result is also supported by our transcriptional data, where we do not observe upregulation of apoptosis-related pathways, via the UPR or otherwise.

It is also unclear as to the conformation of chains trapped in the ER. There are many examples in which the natural tendency of misfolded proteins is to aggregate. This is certainly true in the neurodegenerative diseases. While at the magnification used here in the TEM's the ER inclusions appear homogeneous and amorphous, perhaps at higher magnification/resolution a more discrete structure might be seen.

From collagen-II immunohistochemistry confocal images, the intracellular collagen appears sometimes as aggregated puncta, and in other cases more diffuse and amorphous. Given this heterogeneity, we were not able to readily obtain clear additional structural characterization of the intracellular procollagen-II fraction.

*While the choice of time points for the transcriptional analysis, i.e. early and late seems well thought out, the lack of a significant response may be due to the timing and it might have been useful to do earlier or later time points or intermediate time points in case the response was transient, particularly since other laboratories have reported UPR activation and abnormalities in the context of the silencing of Xbp1, the spliced form of which is a major driver of at least one arm of the UPR. *

While our RNA-sequencing results at the specific timepoints we chose cannot rule out a transient activation of the UPR, they do indicate that chronic, unresolved UPR signaling is not the underlying cause of pathology, which is the main point we are making.

The notion that pro-collagen is largely hydrophilic without the potential for exposure of hydrophobic regions that might engage BiP, thus is not sensitive to BiP sensing, is interesting. Is it possible that the tendency of the mutant polypeptides to form the triple helix which in itself acts as kind of a self chaperoning structure? Looking at the kinetics of assembly inside the cell, see suggestions above, might provide further insight into the process beyond that obtained by looking at the modified state of the lysines.

We believe this notion is very strongly supported by the interactomic experiment showing that BiP fails to preferentially engage the poorly folding triple-helical variant. There are, however, many other chaperones and folding enzymes that assist collagen folding, including prolyl isomerases and Hsp47. Hence, it is not clear to us that substantial self-chaperoning occurs. Still, the self-chaperoning idea is intriguing, and we will note that prior work does indicate that triple-helical domains of individual procollagen polypeptides are strongly pre-organized for triple-helix formation (for a review, see Annu Rev Biochem 2009, 78, 929). That said, we hesitate to speculate here on the self-chaperoning idea without additional evidence.__

__Minor comments:

As I mentioned above, while the transcriptional interactome experiments are computationally sophisticated the cell biology and biochemistry would benefit from more and better quantitation.

We have included quantitation of the extent of intracellular procollagen accumulation and the extent of apoptotic cells, which we hope helps to address this point.

The paper is written in a style in which results and discussion are intermingled. Personally I prefer that the introductions are short, the results clearly and briefly presented and the discussion deals with the interpretation and conclusions. I thought that whole paragraphs could have been omitted. e.g. in the introduction *Omit paragraph "The fibrillar.........achondrogenesis type II" Omit paragraph "Conventional and... for example." Omit "Excitingly........in vitro and in vivo (36)." Results: First paragraph repeats last paragraph of introduction and not necessary in one place or the other, condense. *

We appreciate this feedback and have accordingly edited the manuscript for clarity and brevity, which includes deleting or significantly shortening all the paragraphs indicated by the Reviewer. These improvements are indicated in the track-changes version of the manuscript we resubmitted.

Figure 2 by eye MGP (Matrix gla protein inhibits vascular calcification of type II collagen) seems highly over-expressed in the homozygous mutants; MGP is supposedly an inhibitor of calcification, does its over-expression here reflect something about the adequacy of the matrix

Overexpression of MGP could indeed reflect a defect in the matrix of the homozygous variants. It is also likely a reflection of the delayed hypertrophy and maturation observed in the homozygous variants, as matrix calcification is a step in the endochondral ossification process. We did not follow-up on this particular observation, as it is exclusively observed in the less clinically relevant homozygous variant. We added a note to the manuscript to capture the Reviewer’s point about MGP, as below:

“The upregulation in the homozygous system of Matrix Gla Protein (MGP) (Fig. 2A), which inhibits vascular calcification of the matrix in vivo, further supports the delay in hypertrophy, and could lead to differences in the biomechanical properties of the matrix.”

Figure 5 is good but can it be confirmed by quantitative biochemistry?

We have included quantitation of the extent of intracellular procollagen accumulation and the extent of apoptotic cells.

__ __Did you stain with antibodies to other ER resident chaperones other than calreticulin?

Yes, we also stained the ER with PDI. However, the chondronoids require extensive optimization for immunostaining and we could obtain much better images using the ER marker for calreticulin, hence our choice of images to present in the manuscript.__

__Do cells with large amounts of intracellular G1170S die?

As indicated by the newly included TUNEL data, interestingly, even cells expressing exclusively the Gly1170Ser variant of procollagen-II do not seem to apoptose at a significantly higher rate than wild-type, at least at the timepoint considered. As mentioned above, we added these data as Fig. 8, and added discussion of these results and methodology in the relevant sections of the manuscript.__

__Does higher magnification EM reveal any structure of the material within the dilated ER?

We have so far not been able to use EM to obtain higher-resolution insight into intracellular procollagen structures, but we will work on this idea in future studies.__

__Are there any inflammatory cells in the Chondronoids? To respond to aberrant proteins?

There should not be any such cells present in the chondronoids, and we indeed do not observe any inflammatory response. As noted in the response to Reviewer 1, we added discussion regarding the absence of paracrine signals in this type of model system, which we do believe has major advantages for biochemical studies like those performed here.__

__Paragraph

* "Bypassing the UPR.......often do not" Is discussion not results*

Corrected, thanks.

Significance

The experimental system described here is clearly the wave of the present. Generating human ipSC's of different lineages is now being exploited to study a variety of disorders, to achieve better understanding of pathogenesis at the molecular level to serve as appropriate models for drug development, particularly in the context of high throughput screening. In addition, as in this case, relatively rare autosomal dominant disorders with phenotypes that resemble more common sporadic disease, may allow the development of treatments that are relevant for the sporadic disorder. While it is likely that the osteoarthritis that develops in the carriers of the COL2A1 mutations is a function of the host response to the aberrant mechanics resulting from the defective extra-cellular matrix caused by the mutation, having a pure system in which the primary defect can be corrected and the predisposing matrix deficit reversed, could allow normal reparative processes to mitigate the functional joint disability. While the transgenic mice are useful as a disease model, they represent not only the expression of the primary defect but the host pathophysiologic response to that defect, i.e. in this case how the mouse responds to the defective matrix state and whether those responses add additional pathogenic factors to the disease course. Having a tool in which to relatively assess the pure chondrocyte effect should allow more granular analysis of the primary process.

We appreciate the Reviewer’s careful and enthusiastic assessment of the significance of our work.__

__

Their findings reinforce the notion that involvement of the UPR as well as the other arms of the proteostatic response in chondrocytes expressing a variety of mutant collagens suggests a degree of heterogeneity, perhaps depending on the mutation involved. While I do not believe that their current data prove or rigorously test their proposed hypothesis, i.e. that "perhaps due to the pathologic substitution occurring within a triple-helical domain that lacks hydrophobic character, this ER protein accumulation is not recognized by cellular stress responses, such as the unfolded protein response", it is worth considering.

We provide that hypothesis as a reasonable explanation for the absence of a UPR, and it is strongly supported by our interactomic studies. Furthermore, neither we nor others have found evidence for BiP binding the triple helical domain of procollagen in any other studies. Still, that hypothesis is not the core point of the paper and we do appreciate the Reviewer’s perspective.

Given the fact that this is a relatively small field with a variety of observations concerning the role of proteostasis and the UPR in particular which seem to vary depending on the system, i.e. transgenic mice, transfected fibroblasts, the chondroidomas, these observations particularly with additional biochemistry to confirm their notions regarding folding rates etc, represent a useful technical addition to the field and should be interesting for people working on collagen biology, arthritis and protein folding.

I am not a collagen biologist hence my knowledge of some of the nuances of collagen biology may not be extensive. My own areas of interest include the assembly of multi-peptide proteins (such as immunoglobulins) for secretion; the mechanisms that allow them to exit the cell and the aggregation of misfolded proteins as exemplified by the amyloidoses and other forms of clinically relevant protein aggregation. Hence, I am very familiar with tissue culture, transgenic animals as disease models, studies of protein aggregation, and as a former rheumatologist, osteoarthritis.

We greatly appreciate the Reviewer providing such valuable and scholarly input from the perspective of a scientist with deep expertise in the secretory pathway and other diseases of protein misfolding, as well as from rheumatology. Specifically from the perspective of expertise in collagen biology/biochemistry, we hope that our detailed explanations of assays that are possible versus not possible with collagen in this system, the additional context for why our assessment of the modification of procollagen is correlated with folding/secretion rate, and the further analyses added to the paper, now make a convincing case that the improved manuscript is of high significance and is ready for publication.

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

System: The investigators have used a human iPSC chondrocyte model system to investigate the biochemistry of the Chondrodysplasia caused by the p.Gly1170Ser mutation in the type II collagen gene (COL2A1). They studied presumably homogeneous chondronoids formed by 3 cell lines they previously reported in which the chondrocytes were either homozygous wild type for the gene, homozygous for the Cas Crispr induced mutation or heterozygous for the two alleles (their refs 42-45). In addition, they utilized cultured HT1080 human fibrosarcoma cells transfected with wild type and mutant Col2A1 to study differences in the interactomes of the two proteins.

Analytic Parameters: They investigated the extracellular matrix formed by the three cells using collagen and proteoglycan staining and TEM and the transcriptional responses in chondronoids expressing the wild type and mutant genes.

Observations: matrix formation was defective in the two mutation bearing cell populations, reflecting defective fibril formation proportional to the abnormal gene dose. They found increased accumulations of post-translational modifications (hydroxylation, and O-glycosylation) on the mutant collagen extracted from the chondronoids and EM evidence of collagen retention in the ER. They studied the comparative transcriptional profiles in the three phenotypes and failed to find a profound UPR response late in culture and only a mild upregulation of UPR genes in the young cultures. They could not find evidence for activation of the ISR except in the homozygous mutant cells. Using transfected HT-1080 cells (previously shown by these investigators not to express endogenous pro-collagen II but able to synthesize transfected pro-collagen genes) they were able to study the comparative wt and mutant pro-collagen interactomes.

Conclusions: They conclude that the p.gly1170ser mutation in Col2A1 results in abnormal folding which results in trapping of the protein in the ER and some interaction with cellular elements of the proteostatic response. They concluded that the cellular proteostasis machinery can recognize slow-folding Gly1170Ser through increased interactions with certain ER network components but not in the same fashion that has been described for liver cells producing mutated versions of high volume secreted proteins.

Major comments:

Their first conclusion, stated in the abstract, "Biochemical characterization reveals that Gly1170Ser procollagen-II is notably slow to fold and secrete." that the mutant polypeptide chain is slower folding than the wild type chain is based on the premise that the longer the chains are in the ER the greater the degree of lysine hydroxylation and O-glycosylation. Although this may be true, they do not provide a reference and I could not find a definitive description of the phenomenon. Their reference 48 only discusses the occurrence of intracellular post-translational modification of the lysines and continuing modification extracellularly but does not relate these phenomena to the rate at which the peptides traverse the cell. I think the reader would benefit from seeing experiments in which the rate of folding and secretion of the wild type and mutant chains are measured and the degree of post-translational modification are compared. Cabral WA et al showed differences in collagen folding and secretion rates in cyclophilin wt, knockouts and heterozygotes osteoblasts and fibroblasts by western blots. (2014) Abnormal Type I Collagen Post-translational Modification and Crosslinking in a Cyclophilin B KO Mouse Model of Recessive Osteogenesis Imperfecta. PLoS Genet 10(6): e1004465. doi:10.1371 / journal.pgen. 1004465). Performing such experiments in their chondronoids would confirm the authors' interpretation that the increased post-translational modification portrayed in their figure 4 reflects slowed folding and secretion related to the mutation.

I think Figure 4 needs more explanation for the reader. While, as expected, the homozygous mutant band is much slower than the homozygous wild type band, in the heterozygotes the band is intermediate rather than showing a discrete mixture of wild type and mutant proteins, reflecting different degrees of post-translational modification. Is this a function of mixed triple helices with heterogeneous degrees of post-translational modification? It deserves more comment, since the argument relating the degree of post-translational modification to the rate of folding is dependent on this observation. It would also be helpful to show the whole gel with collagen II markers.

Another approach to the question of intracellular accumulation due to a slow rate of folding of the mutant collagen would be to perform pulse chase labeling of the three types of chondronoids with radiolabeled amino acids and sugars and processing the media and lysates with analysis using antibodies specific for the two collagen chain types. Given the authors extensive experience in studying collagen biosynthesis (e.g. Chan et al J. Biochem. Biophys. Methods 36 (1997) 11-29), such a supporting study would firmly establish whether the rate of folding/secretion differs between the wt and the homozygous and heterozygous chondroidinomas. Until the slow folding can be directly demonstrated in a quantitative fashion rather than by monitoring the secondary phenomenon of post-translational modification the hypothesis remains unproven.

Another issue that does not appear to be addressed is the consequence of having misfolded collagen chains in the dilated ER. Liang et al, using mice transgenic for one or two copies of the mutant human gene showed apoptosis in the homozygotes but not in the hets a finding similar to that of Kimura et al using transgenics carrying a different human COL2A1 mutation. Okada et al, using chondrocytes converted from human fibroblasts with clinical collagenopathy (heterozygous), although not the same mutation as in the present study, showed dilated ER and some level of apoptosis in the cultured cells. Hintze et al, examining chondrocytes expressing different mutants associated with different forms of spondyloepiphyseal dysplasia, suggested that the degree of stability of the mutations might determine whether apoptosis occurred, i.e. the thermolabile p.R989C was associated with apoptosis while cells expressing the more thermostable mutants p.275C, P.719C and p.G853E did not reveal any evidence for ongoing apoptosis R989. Is it possible that the smaller size of the homozygous chondronoids reflect fewer cells rather than less matrix (or both) as result of apoptosis? Examination of the chondronoids with reagents for caspase 3 or Tunel staining. One could also measure by Col/DNA ratio in wt, hets and homos. It might also have been useful for these experiments been more quantitative, i.e. by cell sorting rather than by eye. Would ImageJ software been helpful? It is also unclear as to the conformation of chains trapped in the ER. There are many examples in which the natural tendency of misfolded proteins is to aggregate. This is certainly true in the neurodegenerative diseases. While at the magnification used here in the TEM's the ER inclusions appear homogeneous and amorphous, perhaps at higher magnification/resolution a more discrete structure might be seen.

While the choice of time points for the transcriptional analysis, i.e. early and late seems well thought out, the lack of a significant response may be due to the timing and it might have been useful to do earlier or later time points or intermediate time points in case the response was transient, particularly since other laboratories have reported UPR activation and abnormalities in the context of the silencing of Xbp1, the spliced form of which is a major driver of at least one arm of the UPR. The notion that pro-collagen is largely hydrophilic without the potential for exposure of hydrophobic regions that might engage BiP, thus is not sensitive to BiP sensing, is interesting. Is it possible that the tendency of the mutant polypeptides to form the triple helix which in itself acts as kind of a self chaperoning structure? Looking at the kinetics of assembly inside the cell, see suggestions above, might provide further insight into the process beyond that obtained by looking at the modified state of the lysines.

Minor comments:

As I mentioned above, while the transcriptional interactome experiments are computationally sophisticated the cell biology and biochemistry would benefit from more and better quantitation.

The paper is written in a style in which results and discussion are intermingled. Personally I prefer that the introductions are short, the results clearly and briefly presented and the discussion deals with the interpretation and conclusions. I thought that whole paragraphs could have been omitted. e.g. in the introduction

Omit paragraph "The fibrillar.........achondrogenesis type II" Omit paragraph "Conventional and... for example." Omit "Excitingly........in vitro and in vivo (36)."

Results:

First paragraph repeats last paragraph of introduction and not necessary in one place or the other, condense. Figure 2 by eye MGP (Matrix gla protein inhibits vascular calcification of type II collagen) seems highly over-expressed in the homozygous mutants; MGP is supposedly an inhibitor of calcification, does its over-expression here reflect something about the adequacy of the matrix

Figure 5 is good but can it be confirmed by quantitative biochemistry?

Did you stain with antibodies to other ER resident chaperones other than calreticulin?

Do cells with large amounts of intracellular G1170S die?

Does higher magnification EM reveal any structure of the material within the dilated ER?

Are there any inflammatory cells in the Chondronoids? To respond to aberrant proteins?

Paragraph "Bypassing the UPR.......often do not" Is discussion not results

Referees cross-commenting

Are other reviewers concerned about the precise definition of slowed folding rather than utilizing the degree of post-translational modification as a surrogate?

Significance

The experimental system described here is clearly the wave of the present. Generating human ipSC's of different lineages is now being exploited to study a variety of disorders, to achieve better understanding of pathogenesis at the molecular level to serve as appropriate models for drug development, particularly in the context of high throughput screening. In addition, as in this case, relatively rare autosomal dominant disorders with phenotypes that resemble more common sporadic disease, may allow the development of treatments that are relevant for the sporadic disorder. While it is likely that the osteoarthritis that develops in the carriers of the COL2A1 mutations is a function of the host response to the aberrant mechanics resulting from the defective extra-cellular matrix caused by the mutation, having a pure system in which the primary defect can be corrected and the predisposing matrix deficit reversed, could allow normal reparative processes to mitigate the functional joint disability. While the transgenic mice are useful as a disease model, they represent not only the expression of the primary defect but the host pathophysiologic response to that defect, i.e. in this case how the mouse responds to the defective matrix state and whether those responses add additional pathogenic factors to the disease course. Having a tool in which to relatively assess the pure chondrocyte effect should allow more granular analysis of the primary process.

Their findings reinforce the notion that involvement of the UPR as well as the other arms of the proteostatic response in chondrocytes expressing a variety of mutant collagens suggests a degree of heterogeneity, perhaps depending on the mutation involved. While I do not believe that their current data prove or rigorously test their proposed hypothesis, i.e. that "perhaps due to the pathologic substitution occurring within a triple-helical domain that lacks hydrophobic character, this ER protein accumulation is not recognized by cellular stress responses, such as the unfolded protein response", it is worth considering.

Given the fact that this is a relatively small field with a variety of observations concerning the role of proteostasis and the UPR in particular which seem to vary depending on the system, i.e. transgenic mice, transfected fibroblasts, the chondroidomas, these observations particularly with additional biochemistry to confirm their notions regarding folding rates etc, represent a useful technical addition to the field and should be interesting for people working on collagen biology, arthritis and protein folding.

I am not a collagen biologist hence my knowledge of some of the nuances of collagen biology may not be extensive. My own areas of interest include the assembly of multi-peptide proteins (such as immunoglobulins) for secretion; the mechanisms that allow them to exit the cell and the aggregation of misfolded proteins as exemplified by the amyloidoses and other forms of clinically relevant protein aggregation. Hence, I am very familiar with tissue culture, transgenic animals as disease models, studies of protein aggregation, and as a former rheumatologist, osteoarthritis.

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Referee #1

Evidence, reproducibility and clarity

The paper by Yammine et al addresses a major problem in peculiarities of genotype to phenotype manifestation in collagen II and chondrodysplasia. It is a lucid and comprehensive study detailing what they see as the fundamental mechanism of Gly1170 Ser mutated Col2a1 gene.

At the heart of the matter is the debunking of the results from a mouse model generated by liang et al (Plos one 2014) paper in which the authors suggested that the phenotype seen only homozygous mice (heterozygous mice appear normal), was related to ER stress -UPR-apoptosis cascade resulting in the chondrodysplasia. Yammine et al paper uses a different model, a robust human iPSC-based tissue, with a CRISPRed variant show that despite the ability of the variant chondrocytes to deposit a Gly1170Ser-substituted collagen II in both the hetero- and homozygous models, is not accompanied by any substantive UPR. The authors of this current paper also argue that their model system is most closely resemble the human context, where heterozygous individual show pathology.

I have sieved all the data related to this topic and have gone back to examine the data and what struck me was the repeated use of the phrase "slow to fold" in the current paper and wondered whether the element of "TIME" is as important in the chondrogenesis of either models and it is this element that generate the difference between the two results?

While iPSC-based tissue takes up to 44 days, a female mouse would have had two litters in this time and made many more growth plates. Could it be by "slowing" the chondrogenesis pathway, which is part of the procedure of differentiation of iPS cells into chondrocytes, the ER is not as "stressed" as in mouse development? I would like the authors to reflect and comment and put forward their view given UPR signaling pathways play a crucial role in chondrocytes in phases of high protein synthesis, e.g., during bone development by endochondral ossification (Journal of Bone Metabolism, vol. 24, no. 2, pp. 75-82, 2017).

This is not withstanding the good argument given by the authors in defending their robust results, namely that the there is no evidence that the hydrophilic triple-helical domain of pro-collagen binds BiP, the main detector of accumulated misfolded proteins. What then do they make out of the immunostaining and qPCR with ER stress related genes in Liang et al paper?? I know that the data is not theirs but a comment on the indisputable data gives the reader a better understanding.

Although I understand the choice of cell lines for overexpression, the transfection of the HT-1080 cells using wild-type and Gly1170Ser COL2A1encoding plasmids are not a match to the in vivo model (variation of efficiency, etc.) the appearance of BiP even at a lower fold increase does not negate ER stress, as the authors acknowledge but more important is what other paracrine signals which triggers the UPR signally pathway which is not linked to BiP ? or an iPS system may lack? Is there anything else not only ATF6α (activating transcription factor 6 alpha), but IRE1α (inositol-requiring enzyme 1 alpha), and PERK (protein kinase RNA-like endoplasmic reticulum kinase). The authors have given us plenty of alternatives that are relevant, and they prepared us for yet another paper on articular cartilage using iPS tissue model which I am looking forward to.

Significance

I think this paper is publishable and it is important in understanding the mechanism by which mutation in collagen type II affect chondrogenesis and therefore bone formation.

This paper will appeal to musculoskeletal scientist especially those who are interested in bone and its pathology.

It would be important for the authors to respond to the critique of "TIME" and speed of protein synthesis which create a duress in the ER pathway.

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Reply to the reviewers

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

1. In this manuscript, Imoto et al. analyze the specific role of the Dynamin1 splice variant Dyn1xA in so-called ultrafast endocytosis, an important mechanism of synaptic vesicle recycling at synapses. In a previous publication (Imoto et al. Neuron 2022), some of the authors had shown that Dyn1xA, and not the other splice variant Dyn1xB, is essential for ultrafast endocytosis. Moreover, Dyn1xA forms clusters around the active zone for exocytosis and interacts with Syndapin 1 in a phosphorylation dependent manner. However, it was unclear which molecular interactions underlie the specific role of Dyn1xA. Here, the authors provide convincing evidence with pull down assays and CSP that Dyn1xA PRR interacts with EndophilinA1/2 with two binding sites. The first binding site lies in the part common to xA and xB, was previously characterized. The second site was previously uncharacterized, is specific for Dyn1xA, and is regulated by phosphorylation (phosphobox 2). The location of these splice variants and mutated forms at presynaptic sites correlate with the prediction made by the biochemical assays. Finally, the authors perform rescue experiments ('flash and freeze' and VGLUT1-pHluorin imaging experiments) to show that Dyn1xA-EndophilinA1/2 binding is important for ultrafast endocytosis. I find the results interesting, providing an important step in the understanding of the interplay between dynamin and the endocytic proteins interacting with it (endophilin, syndapin, amphiphysin) in the context of synaptic vesicle recycling. The manuscript is clearly written and for the most part the data supports the authors' conclusions (see specific comments below). However, there are some issues which need to be clarified before this manuscript is fully suitable for publication.

We thank the reviewer for noting the importance of our study. Indeed, our previous study has raised the question as to why only the Dyn1xA splice variant mediates ultrafast endocytosis, and our current manuscript now resolves this issue.

Introduction: the dynx1B Calcineurin binding motif is written PxIxIT consensus but actual sequence is PRITISDP. Is this a typo?

The sequence is correct. One thing we failed to mention is that the last amino acid in this motif can be either threonine or serine for calcineurin binding, as we demonstrated previously [Jing, et al., 2011 JBC; PMC3162388]. We have amended the text as follows.

1. calcineurin-binding motif (PxIxI[T/S]) 19.

Figure 1: the difference between the constructs used in panels C and D is not clear. In D, is it a truncation without residues 796 and 845? If so, it should be labelled clearly in the Western blots. In Panel E, Dyn1xA 746-798 should be labeled Dyn1x 746-798 because it is common to both splice variants.

We thank the reviewer for pointing this out. Both C and D used the full-length PRRs of Dyn1xA-746 to 864 and xB-746 to 851. To make the labeling clear, we changed Dyn1xA PRR to “Dyn1xA PRR (746-864)” and Dyn1xB PRR to “Dyn1xB PRR 746-851” in Figure 1. In the main text, we made the following changes.

1. 4: “To identify the potential isoform-selective binding partners, the full-length PRRs of Dyn1xA746-864 and xB746-851 (hereafter, Dyn1xA-PRR and Dyn1xB-PRR, respectively).”

Figure 1: For amphiphysin binding the authors write that "No difference in binding to Amphiphysin 1 was observed among these peptides (Figure1D-F)." They should write that Dyn1x 746-798 does not bind Amphiphysin1 SH3 domain, confirming the specificity of binding to the 833-838 motif.

We edited the sentence as suggested.

1. “Dyn1x 746-798 does not bind Amphiphysin1 SH3 domain (Figure 1G), confirming the specificity of binding to the 833-838 motif as reported in previous studies 29,30. (Figure 1D-F).”

Figure S2. The panels are way too small to see the shifts and the labelling. Please provide bigger panels

As suggested, we have now provided bigger panels in Figure S2, and amended the text and Figure legend accordingly.

We also removed Figure S2B as it was not referred to in the text in any way. (It was the reverse experiment – HSQCs of 15N-labelled SH3 titrated with unlabelled dynamin).l

Figure 2 panel B. There is a typo in the connecting line between the sequence and the CSP peaks. It is 846 instead of 864 (after 839).

Corrected.

Figure 3 panel E. In the text, the authors write that "Western blotting of the bound proteins from the R838A pull-down experiment showed that R838A almost abolished both Endophilin and Amphiphysin binding in xA806-864 (Figure 3D), and reduced Endophilin binding to xA-PRR (Figure 3E)." I think they should write "only slightly reduced Endophilin binding..." it is more faithful to the result and consistent with the conclusion that Endophilin A1 has two binding sites on Dyn1xA PRR.

We have now provided quantitative data for R838A and R846A (Fig. 3F and G). Endophilin binding is significantly reduced with R846A.

It is unclear why the R846A mutant affects binding of Dyn1xA 806-864 but not Dyn1xA-PRR-.

The reviewer asks why the R846A mutant affects binding of Dyn1xA 806-864, but not so much of Dyn1xA-PRR. The explanation is simply that there are two endophilin binding sites in Dyn1xA-PRR. The first is not present in the xA806-864 peptide, while both are present in Dyn1xA-PRR (the full length tail). When doing pull-down experiments, the binding tends to saturate – even when the second site is blocked by R846A. The first site is still able to bind, and the binding appears as normal. The same applies to the R838A mutant.

Moreover, it affects binding to endophilin as well as amphiphysin, and therefore it is not specific. It is thus not correct to write that "R846 is the only residue found to specifically regulate the Dyn1 interaction with Endophilin as a part of an SDE". In the Discussion (page 11), the authors refer to the R846A mutation as specifically affecting Endophilin binding. This should be toned down, as it also affects Amphiphysin binding. For this important point, the data on quantification of Endophilin binding should be presented.

The reviewer’s concern is about our claims of specificity of Endophilin A binding in Dyn1xA R846 mutation experiments. The reviewer is correct, and we have now defined specific parameters for those claims. Specifically, we have added new quantitative data from the Western blots in Fig 3E (full-length Dyn1aX-PRR) as Fig 3F-G. We used full-length Dyn1aX-PRR rather than the xA806-864 peptide because the subsequent transfection experiments use full length Dyn1xA. In the new figures 3F and 3G, we quantified Endophilin A, Amphiphysin and Syndapin1 amounts from the multiple Western blots such as Figure 3E (now n=14, 6 experiments, each in with 2-4 replicates for Dyn1xA PRR). R846A mutated in Dyn1xA-PRR significantly reduces the binding to Endophilin A, but it does not significantly affect the binding to Amphiphysin 1and Syndapin1 (Fig 3G). Therefore, this particular Dyn1xA-PRR mutation specifically affects Endophilin A binding, in the context of the full-length tail Dyn1aX-PRR. To make these results clear, we modified the text as below.

P7. “R838A and R846A caused smaller reductions in Endophilin binding compared to wild-type Dyn1xA-PRR, (Figure 3E, 3F, R838A, median 68.5 ; Figure 3G, R846A, median 59.3 % : R838A reduced the Dyn1/Amphiphysin interaction (Figure 3E, 3F, median 14.2 % binding compared to wild-type Dyn1xA-PRR). By contrast, R846A did not affect Amphiphysin and Syndapin binding to Dyn1xA-PRR (Figure 3E, 3G). Therefore, R846, being part of an SDE, is the only residue we found to specifically regulate the Dyn1 interaction with Endophilin in the context of the full length tail (DynxA-PRR)”.

Additionally, the reviewer notes that “the authors refer to the R846A mutation as specifically affecting Endophilin binding. This should be toned down, as it also affects Amphiphysin binding.” In the light of the above data and new quantitative analysis (Fig 3F-G), we have clarified the conclusion. However, to be clear that this statement is only correct in the context of the full-length DynxA-PRR, we amended texts as follows:

P7. “By contrast, R846A did not affect Amphiphysin and Syndapin binding to Dyn1xA-PRR (Figure 3E, 3G). Therefore, R846, being part of an SDE, is the only residue we found to specifically regulate the Dyn1 interaction with Endophilin in the context of the full length tail (DynxA-PRR)”.

New legends for Figure 3F and G have now been added as follows.

“(F) The binding of Endophilin A, and Amphiphysin 1 and Syndapin1 to Dyn1xA-PRR (wild type) or R838A mutant quantified from Western blots in (E). n=14 (6 experiments with 2-4 replicates in each). Median and 95% confidential intervals are shown. Kruskal-Wallis with Dunn’s multiple comparisons test (**p (G) The binding of Endophilin A, and Amphiphysin 1 and Syndapin1 to Dyn1xA-PRR (wild type) or R846A mutant quantified from Western blots in (E). n=14 (6 experiments with 2-4 replicates in each). Median and 95% confidential intervals are shown. Kruskal-Wallis with Dunn’s multiple comparisons test was applied (*p

Figure 3F-G (which are now 3H and 3I in the revised text): what do the star symbols represent in the graphs? I guess the abscissa represents retention time. Please write it clearly instead of a second ordinate for molecular mass, which does not make much sense if this reflects the estimate for the 3 conditions.

The “stars” are crosses (x) and represent individual data points. The figure legends have been updated for clarity. The reviewer is correct that the X-axis is retention time (min). The second Y-axis is needed to define the points in the curve marked with crosses (x’s). The legends for Figure 3H and I are now changed as follows.

“(H) SEC-MALS profiles for Dyn1xA alone (in green), Endophilin A SH3 alone (in red) and the complex of the two (in black) are plotted. The x-axis shows retention time. The left axis is the corresponding UV absorbance (280 nm) signals in solid lines, and the right axis shows the molar mass of each peak in crosses. The molecular weight of the complex was determined and tabulated in comparison with the predicted molecular weight. x represent individual data points.

(I) SEC-MALS profiles for a high concentration of Dyn1xA-PRR/Endophilin A SH3 complex (0.5 mg) (in dark blue) and a low concentration of Dyn1xA-PRR/endophilin A SH3 complex (0.167 mg) (in blue). The x-axis shows retention time. The left axis is the corresponding UV absorbance (280 nm) signals in solid lines, and the right axis shows the molar mass of each peak in crosses. The molecular weight of the complex was determined and tabulated in the table. x represent individual data points.”

Figure 4: The statement that "By contrast [to Dyn1xA], Endophilin A1 or A2 formed multiple clusters (1-5 clusters)" is not at all clear on the presented pictures. The authors should provide views of portions of axons with several varicosities, for the reader to appreciate the cases where there are more EndoA clusters than Dyn1 clusters.

In the revised Figure S4, we added additional STED images for a region of axons with more EndoA1/2 clusters than Dyn1xA clusters. The locations of Dyn1xA and EndoA1/2 clusters are annotated in each image based on the local maximum of intensity, which is determined using our custom Matlab analysis scripts (Imoto, et al., Neuron 2022; for the description of the methods, please refer to the Point #14 below). We also added Figure S3 to describe our analysis pipelines. In the Dyn1xA channel, outer contour indicates 50% of local maxima (boundary of Dyn1xA cluster) while inner contour indicates 70% of local maxima of the clusters. In the EndoA1/2 channel, local maxima of the clusters are indicated as points. To reflect these changes, we modified text as below.

P 9. “By contrast, Endophilin A1 or A2 formed multiple clusters (1-5 clusters) (Figure S4)”

The legends for Figure S4 are now as follows.

“Figure S4. Additional STED images for Figure 4.

(A) The top image shows an axon containing multiple boutons. Signals show overexpression of GFP-tagged Dyn1xA (Dyn1xA) and mCherry-tagged Endophilin A1 (EndoA1). The bottom images show magnifications of four boutons in the top image. Red hot look-up table (LUT) images on the right side of Dyn1xA and EndoA1 images are enhanced contrast images. Outer and inner contours represent 50% and 70% of local maxima of the Dyn1xA, respectively. Black circles represent local maxima of Endophilin A1. In these boutons, multiple EndophilinA1 puncta are present.

(B) The top image shows an axon congaing multiple boutons. Signals show overexpression of mCherry-tagged Dyn1xA (Dyn1xA) and GFP-tagged Endophilin A1 (EndoA1). The bottom images show magnifications of four boutons in the top image. Red hot LUT images on the right side of Dyn1xA and EndoA2 images are enhanced contrast images. Outer and inner contours represent 50% and 70% of local maxima of the Dyn1xA, respectively. Black circles represent local maxima of Endophilin A2. In these boutons, multiple EndophilinA2 puncta are present.

(C) STED micrographs of the same synapses as in Figure 4E with an active zone marker Bassoon (magenta) visualized by antibody staining. GFP-tagged Dyn1xA, Dyn1xA S851D/857D or Dyn1xA R846A (green) are additionally stained with GFP-antibodies. Local maxima of Dyn1xA, Dyn1xA S851D/857D or Dyn1xA R846A signals and minimum distance to the active zone boundary are indicated by dark blue lines.”

Moreover, overexpression of EndophilinA1/2-mCherry is not sufficient to assess its localization. Please consider either immunofluorescence or genome editing (e.g. Orange or TKIT techniques).

We agree with the reviewer that overexpression obscures the endogenous localization of proteins. To address this point in our previous publication, we titrated the amount of plasmids for Dyn1xA-GFP and transfected neurons just for 20 hours – this protocol allowed us to uncover the endogenous localization of Dyn1xA despite the fact that it was overexpressed in wild-type neurons (Imoto, et al., 2022). We also confirmed this localization by ORANGE-based CRISPR knock-in of GFP-tag in the endogenous locus of Dyn1 just after the exon 23 and confirm the true endogenous localization of Dyn1xA (Imoto, et al., 2022). Similar approaches were taken by the Chapman lab to localize Synaptotagmin-1 and Synaptobrevin 2 in axons (Watson et al, 2023, eLife, PMID: 36729040). We did not emphasize this in the first submission, but we took the same approach for the EndoA1/2 localization. This does not mean that they also unmask the endogenous localization, and the reviewer is correct that additional evidence would strengthen the data here. Thus, as suggested, we have looked at the endogenous EndophilinA1 localization by antibody staining. As the reviewer is likely aware, EndophilinA1 also localizes to other places including dendrites and postsynaptic terminals, making it difficult to analyze the data. However, we observe colocalization of Dyn1xA with endogenous EndoA1. Thus, we believe that our major conclusion here drawn based on EndoA1/2-mCherry overexpression is valid (Reviewer’s Figure 1). Since the Endophilin signals in neighboring processes obscures its localization in synapses-of-interest, repeating this localization experiments with ORANGE-based knock-in would be ideal. However, with the lead author starting his own group and many validations needed to confirm the knock-in results, this experiment would require us at least 4-6 months, and thus, it is beyond the scope of our current study. We will follow up on this localization in the near future, but given that endophilin is required for ultrafast endocytosis (Watanabe, et al., Neuron 2018, PMID: 29953872) and these proteins need to be in condensates at the endocytic sites for accelerating the kinetics of endocytosis (Imoto, et al., Neuron 2022, PMID: 35809574), we are confident that endogenous

EndoA1/2 are localized with Dyn1xA.

The analysis of the confocal microscopy data is not explained. How is the number of clusters determined? How far apart are they? Confocal microscopy may not have the resolution to distinguish clusters within a synapse.

We apologize for the insufficient description of the method. We had provided a more thorough description of the methods in our previous publication (Imoto, et al., Neuron 2022, PMID: 35809574). To make this more automated, we improved our custom Matlab scripts. Please note that all the analysis for the cluster location is performed on STED images, not on normal confocal images. To determine the cluster, first, presynaptic regions (based on Bassoon signals or Dyn1xA signals within boutons) in each STED image are cropped with 900 by 900 nm (regions-of-interest) ROIs. Then, our Matlab scripts calculate the local maxima of fluorescence intensity within the ROIs. To determine the distance between the active zone and the Dyn1xA or EndoA1/2 clusters, the Matlab scripts perform the same local maxima calculations in both channels and make contours at 50% intensity of the local maxima. The minimum distance reflects the shortest distance between the active zone and Dyn1xA/EndoA1/2 contours. To make these points clearer, we modified the main text and the Methods section. In addition, we have added workflow of these analysis as Figure S3.

P9. Main. “Signals of these proteins are acquired by STED microscopy and analyzed by custom MATLAB scripts, similarly to our previous work23.”

P20. Methods. “All the cluster distance measurements are performed on STED images. For the measurements, a custom MATLAB code package23 was modified using GPT-4 (OpenAI) to perform semi-automated image segmentation and analysis of the endocytic protein distribution relative to the active zone marked by Bassoon or relative to Dyn1xA cluster in STED images. First, the STED images were blurred with a Gaussian filter with radius of 1.2 pixels to reduce the Poisson noise and then deconvoluted twice using the built-in deconvblind function: the initial point spread function (PSF) input is measured from the unspecific antibodies in the STED images. The second PSF (enhanced PSF) input is chosen as the returned PSF from the initial run of blind deconvolution62. The enhanced PSF was used to deconvolute the STED images to be analyzed. Each time, 10 iterations were performed. All presynaptic boutons in each deconvoluted image were selected within 3030-pixel (0.81 mm2) ROIs based on the varicosity shape and bassoon or Dyn1xA signals. The boundary of active zone or Dyn1xA puncta was identified as the contour that represents half of the intensity of each local maxima in the Bassoon channel. The Dyn1xA clusters and Endophilin A clusters were picked by calculating pixels of local maxima. The distances between the Dyn1xA cluster and active zone boundary or Endophilin A clusters were automatically calculated correspondingly. For the distance measurement, MATLAB distance2curve function (John D'Errico 2024, MATLAB Central File Exchange) first calculated the distance between the local maxima pixel and all the points on the contour of the active zone or Dyn1xA cluster boundary. Next, the shortest distance was selected as the minimum distance. Signals over crossing the ROIs and the Bassoon signals outside of the transfected neurons were excluded from the analysis. The MATLAB scripts are available by request.”

In the legend of Figure S3,

“Protein localization in presynapses is determined by semi-automated MATLAB scripts (see Methods).

(A) Series of deconvoluted STED images are segmented to obtain 50-100 presynapse ROIs in each condition.

(B) Two representations of the MATLAB analysis interface are shown. The first channel (ch1, green) is processed to identify the pixels of local maxima within this channel. The second channel (ch2, magenta) is normally an active zone protein, Bassoon. Active zone boundary is determined by the contour generated at 50% intensity of the local maxima of ch2. The contours outside of the transfected neurons are manually selected on the interface and excluded from the analysis. Minimum distances from each pixel of the local maxima in ch1 to the contour in ch2 are calculated and shown in the composite image. The plot “Distance distribution” shows all the minimum distance identified in this presynapses ROI (unit of the y axis is nanometer). The plot “Accumulated distance distribution” shows the accumulated distance distribution from the initial to the current presynapses ROI. The plot “Histogram of total intensity” shows the intensity counts around individual local maxima pixels in ch1.”

For the STED microscopy, a representation of the processed image (after deconvolution) and the localization of the peaks would be important to assess the measurement of distances. If Dyn1xA S851/857D is more diffuse, are there still peaks to measure for every synapse?

We thank the reviewer for bringing up this important question. In Figure S4C, we have added the position of the local maxima of wild-type and mutant Dyn1xA shown in the main Figure 4E. As the reviewer pointed out, when a protein is more diffuse, it is difficult to find the peak intensity by STED. However, since these proteins are still found at a higher density within a very confined space of a presynapse and synapses are packed with organelles like synaptic vesicles and macromolecules, signals from even diffuse proteins can be detected as clusters, and local maxima can be detected in these images.

To illustrate this point better, we added Reviewer’s Figure 2 below. In this experiment, we transfected neurons with a typical amount of plasmids (2.0 µg/well) or ~10x lower amount (0.25 µg/well). When the density of cytosolic proteins is high (Reviewer’s Figure 2A), the depletion laser has to be strong enough to induce sufficient stimulated emission and resolve protein localization. Insufficient power would produce low resolution images, leading to inappropriate detection of the local maxima (Reviewer’s Figure 1A). Thus, we set our excitation and depletion laser powers to resolve the protein localization to ~40-80 nm at presynapses. Furthermore, to avoid mislocalization of proteins due to the overexpression, we use 0.25-0.5 ug/well (in 12-well plate) of plasmid DNA for transfection, which is around 10 times lower than the amount used in the typical lipofectamine neuronal transfection protocol (Imoto, et al., Neuron 2022). We also change the medium around 20 hours after the transfection instead of the typical 48 hours (Imoto, et al., Neuron 2022). With these modifications and settings, we can obtain the location of the local maxima of the diffuse signals (Reviewer’s Figure 1B and Figure 4E and Figure S4). We modified the Method section to make these points clearer.

P 17, “Briefly, plasmids were mixed well with 2 µl Lipofectamine in 100 µl Neurobasal media and incubated for 20 min. For Dyn1xA and Endophilin A expressions, 0.5 µg of constructs were used to reduce the overexpression artifacts23. The plasmid mixture was added to each well with 1 ml of fresh Neurobasal media supplemented with 2 mM GlutaMax and 2% B27. After 4 hours, the medium was replaced with the pre-warmed conditioned media. To prevent too much expression of proteins, neurons were transfected for less than 20 hours and fixed for imaging.”

P 20, “Quality of the STED images are examined by comparing the confocal and STED images and measuring the size of signals at synapses and PSF (non-specific signals from antibodies).”

Legends for Figure S4C,

“(C) STED micrographs of the synapses shown in Figure 4F with an active zone marker Bassoon (magenta). GFP-tagged Dyn1xA, Dyn1xA S851D/857D or Dyn1xA R846A are visualized by antibody staining of GFP (green). Local maxima of Dyn1xA, Dyn1xA S851D/857D or Dyn1xA R846A signals and minimum distance to the active zone boundary are overlaid.”

Figures 5 and 6: No specific comment. The data and its analysis are very nice and elegant. The comment on the lack of rescue of Dyn1xA on endosome maturation may be a bit overstated, because many "controls" (shRNA control Figure S5 or Dyn3 KO in Imoto et al. 2022) have a significant number of endosomes 10 s after stimulation.

We thank the reviewer for noting the strength of our data and pointing out this issue on endosomal resolution. In particular, the reviewer is concerned about our interpretation of the ferritin positive endosomes present at 10 s in time-resolved electron microscopy experiments. Indeed, the number of ferritin positive endosomes in Dyn1 KO, Dyn1xA OEx neurons (0.1/profile) is similar to the control conditions: scramble shRNA control (0.1/profile, Figure S5) and Dyn3KO neurons (0.2/profile) in our previous study (Imoto et al. 2022). Although we do not consider Dyn3 KO as a control, given the presence of abnormal endosomal structures, we agree with the reviewer that scramble shRNA control in Figure S5 does indicate that some ferritin-positive endosomes even at 10 s after stimulation. We would like to note that this result is in stark contrast to our previous studies where we observed the number of ferritin positive endosomes returning to the basal level in both wild-type neurons and many scramble shRNA controls (Watanabe et al. 2014, 2018, Imoto et al 2022). Thus, the majority of the data we have indicate that the number of ferritin positive endosomes returns to basal level by 10 s, suggesting that endosomes are typically resolved into synaptic vesicles by this time. However, given that we do not know the nature of the inconsistency here and we cannot exclude the possibility of overexpression artifact of Dyn1xA as an alternative, we changed the following lines.

P. 10, “Interestingly, the number of ferritin-positive endosomes did not return to the baseline (Figure 5E, F) as in previous studies3,35,36, suggesting that Dyn1xA may not fully rescue the knockout phenotypes or that overexpression of Dyn1xA causes abnormal endosomal morphology.”

By the way, why did the authors use Dyn1 KO in this study, and not Dyn1,3 DKO as in Imoto et al. 2022?

This is simply because Dyn3KO displayed an endosomal defect in our previous study (Imoto et al 2022), and we wanted to focus on endocytic phenotypes of Dyn1 KO and mutant rescues in this study.

In the Discussion, the authors present the binding sites (for endophilin and amphiphysin SH3 domains) as independent. However, these proteins form dimers or even multimers as they cluster around the neck of a forming vesicle. Even though they provide evidence in vitro (Figure 3) that in these conditions of high concentration one dyn1xA-PRR binds one SH3 domain, in cells multiple binding sites on the PRR to these proteins may involve avidity effects, as discussed for example in Rosendale et al. 2019 doi 10.1038/s41467-019-12434-9. For example, the high affinity binding of Dyn1-PRR to amphiphysin cannot be explained only by the sequence 830-838.

The reviewer suggests “In the Discussion, the authors present the binding sites (for endophilin and amphiphysin SH3 domains) as independent.” However, we do not claim these interactions are functionally independent, except in the context of in vitro experiments where they are sequence-independent.

They also suggest “However, these proteins form dimers or even multimers as they cluster around the neck of a forming vesicle”. However we do not agree with this in the context of our Discussion, because the evidence of multimers and clustering is convincing but is entirely in vitro data.

Thirdly they comment that “For example, the high affinity binding of Dyn1-PRR to amphiphysin cannot be explained only by the sequence 830-838.” We fully agree with the statement and felt we had addressed this in the manuscript. To explain, it’s important to point out our relatively new concept here and previously reported by us (Lin Luo et al 2016, PMID: 26893375) of the existence and importance of SDE and LDE for SH3 domains (Endophilin here, syndapin in our previous report). These elements act at a distance from the so-called core PxxP motifs and they provide much higher affinity and specificity than the core region alone. We had further mentioned this in the p11 discussion “Although this is a previously characterized binding site for Amphiphysin and is also present in Dyn1xB-PRR, the extended C-terminal tail of Dyn1xA contains short and long distance elements (SDE and LDE) essential for Endophilin binding, making it higher affinity for Endophilin.” Because the NMR identified F862 as a chemical shift for dynamin, we performed a pulldown with this mutant in the xA746-798 construct (which only contains the higher affinity site) and found that indeed “.F862A reduced Endophilin binding 29% (pOverall, the reviewer correctly points out that “multiple binding sites on the PRR to these proteins may involve avidity effects*” could play a role in vivo. We agree that avidity is an additional possibility, not examined in our study. Therefore, as suggested, we added the following sentence to the discussion on the SDE and LDE impacts.

P. 11. “Our pull-down results showed that R846A abolished endophilin binding to xA806-864 (which contains only the second and higher affinity binding site and the associated SDE (A839) and LDE (F862)) and reduced about 40% of endophilin binding to the Dyn1xA-PRR (which contains both binding sites) without affecting its interaction with Amphiphysin, providing important partner specificity, although we cannot exclude the possibility that avidity effects may additionally come in play in vivo 42

Reviewer #1 (Significance (Required)):

This study provides a significant advance on the mechanisms of dynamin recruitment to endocytic zones in presynaptic terminals. The work adds a significant step by experienced labs (Robinson, Watanabe) who have provided important insight in the mechanisms by many publications in the last years.

We thank the reviewer for the careful read of our manuscript and positive outlook of our work.

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

1. This is a compelling study that reports a key discovery to understand the molecular mechanism of ultrafast endocytosis. The authors demonstrate that the Dynamin splice version 1xA (Dynamin 1xA) uniquely binds Endophilin A, in contrast to Dynamin splice version 1xB (Dynamin 1xB) that does not bind Endophilin A and it is not required for ultrafast endocytosis. In addition, the Endophilin A binding occurs in a dephosphorylation-regulated manner. The study is carefully carried out and it is based on high quality data obtained by means of advanced biochemical methodologies, state-of-art flash-freezing electron microscopy analysis, superresolution microscopy and dynamic imaging of exo-and endocytosis in neuronal cultures. The results convincingly support the conclusions.

We thank the reviewer for supporting the conclusions of our study.

1. Although additional experiments are not essential to support the claims of the paper there is room, however, for improvement within the pHluorin experiments. These experiments, that are clearly informative and consistent with the rest of experimental data, do not apply the useful approach to separate endo- from exocytosis. The use of bafilomycin or folimycin to block the vesicular proton pump allows the unmasking the endocytosis that is occurring during the stimulus, that should correspond to ultrafast endocytosis. It would be very elegant to demonstrate that such a component, as expected according to the electron microscopy data, requires the binding of Endophilin A to Dynamin 1xA. If the authors have the pHluorin experiments running, the suggested experiments are very much doable because the reagents and the methodology is already in place and the new data could be generated in around six weeks.

We thank the reviewer for the suggestion. The reviewer is concerned that vGlut1 pHluorin experiment in Figure 6 may not correspond to ultrafast endocytosis. We agree that bafilomycin/folimycin treatment will reveal the amount of endocytosis that takes place while neurons are stimulated. However, we are not certain that endocytosis during this phase would fully correspond to ultrafast endocytosis because reacidification of endocytosed vesicles typically takes 3-4 s (Atluri and Ryan, 2006, PMID: 16495458; although see https://elifesciences.org/articles/36097) and thus, the nature of endocytosis cannot be fully determined by this assay. To claim that endocytosis measured by pHluorin assay during stimulation all correspond to ultrafast endocytosis, we would need to perform very careful work to track single pHluorin molecules at the ultrastructural level and corelate their internalization to pHluorin signals. Perhaps, a rapid acid quench technique used by the Haucke group would also be appropriate to estimate the amount of ultrafast endocytosis (Soykan et al. 2017 PMID: 28231467), but we are not set up to perform such experiments here. Also, our lead author, Yuuta Imoto, is leaving the lab to start up his own group, and it will take us months rather than weeks to get the requested experiments done. Since the point of this experiment was to test whether the interaction of Dyn1xA and EndoA is essential for protein retrieval regardless of the actual mechanisms and the reviewer acknowledges that this point is sufficiently supported by the experiments, we will set this experiment as the priority for the next paper.

Instead of the bafilomycin or rapid acid quenching experiments, we have now added data from vglut1-pHluorin experiment with a single action potential. With a single action potential, all synaptic vesicle recycling is mediated by ultrafast endocytosis in these neurons (Watanabe et al, 2013 PMID: 24305055; Watanabe et al. 2014, PMID: 25296249). Our electron microscopy experiments in Figure 5 is also performed with a single action potential. As with 10 action potentials, 20 Hz experiments, re-acidification of vglut1-pHluorin is blocked when Dyn1 and EndophilinA1 interaction is disrupted (Figure 6 F-I). We added a description of this result as below.

P 11. “Similar defects were observed when the experiments were repeated with a single action potential – synaptic vesicle recycling is mediated by ultrafast endocytosis with this stimulation paradigm25 (S851/857 recovery is 73.3% above the baseline; R846A, recovery is 30.0% above the baseline) (Figure S9 A-D). Together, these results suggest that the 20 amino acid extension of Dyn1xA is important for recycling of synaptic vesicle proteins mediated by specific phosphorylation and Endophilin binding sites within the extension.”

The methods are carefully explained. Some of the experiments are only replicated in two cultures and the authors should justify the reasons to convince the audience that the approaches used have enough low variability for not increasing the n number. The pHluorin experiments, however, are performed only in a single culture; they should replicate these experiments in at least 3 different cultures (three different mice).

The reviewer is correct. The variability is very low in our ultrastructural studies and STED imaging, and thus, in all our previous publications, two independent cultures are used. We do agree that in the ideal case, we would like to have three independent cultures, but given the nature of ultrastructural studies (control, mutants, and multiple time points), triplicating the data would add another year to our work. We are currently developing AI-based segmentation analysis, and once this pipeline is established, we will be able to increase N. However, please note that for these experiments, we examine around 200 synapses from each condition in electron microscopy studies (Table S2)– these numbers are far more than the gold standard in the field. Likewise, 50-100 synapses are examined for STED experiments (Table S2). To examine variability of our analysis results, we compared a significance between the dataset using cumulative curves and Kolmogorov–Smirnov test (Figure S11). As shown in the summarized data and p value in each condition, there are no significant difference between the datasets.

For pHluorin analysis, the reviewer is correct. We repeated the experiments twice to increase the N after the initial submission. The data are consistent, and the conclusions are not changed by the additional experiments (Figure 6 and Figure S9). We also changed the Statistical analysis section in Methods as below.

P. 19. “All electron microscopy data are pooled from multiple experiments after examined on a per-experiment basis (with all freezing on the same day); none of the pooled data show significant deviation from each replicate (Table S2).”

p 19, “All fluorescence microscopy data were first examined on a per-experiment basis. For Figure 4, the data were pooled; none of the pooled data show significant deviation from each replicate (Figure S11 and Table S2). Sample sizes were 2 independent cultures, at least 50-100 synapses from 4 different neurons in each condition..”

Legends for Figure S11

Figure S11. Data variability in Figure 4.

Cumulative curves are made from each dataset of (A) distance of Endophilin A1 puncta from the edge of Dyn1xA puncta, (B) distance of Endophilin A2 puncta from the edge of Dyn1xA puncta, distance distribution of Dyn1xA from active zone edge in (C) neurons expressing wild-type Dyn1xA-GFP, (D) Dyn1xA-S851/857-GFP and (E) Dyn1xA-R846-GFP. n > 4 coverslips from 2 independent cultures. Kolmogorov–Smirnov (KS) test, p values are indicated in each plot.

Minor comments: 4. Prior studies referenced appropriately and the text and figures are clear and accurate.

We thank the reviewer for the careful read of our manuscript.

The authors should discuss about the mediators (enzymes) responsible for dephosphorylation of phosphor-box 2 that is key for the Dynamin 1xa-Endophilin A interaction.

We thank the reviewer for the suggestion. We added a discussion on a potential mediator, Dyrk1, as below.

P. 12. ”What are the kinases that regulate Dyn1? The phosphorylation of phosphobox-1 is mediated by Glycogen synthase kinase-3 beta (GSK3ß) and Cyclin-dependent kinase 5 (CDK5)17, while phosphobox-2 is likely phosphorylated by Trisomy 21-linked dual-specificity tyrosine phosphorylation-regulated kinase 1A (Mnb/Dyrk1)44,45 since Ser851 in phosphobox-2 is shown to be phosphorylated by Mnb/Dyrk1 in vitro32. Furthermore, overexpression of Mnb/Dyrk1 in cultured hippocampal neurons causes slowing down the retrieval of a synaptic vesicle protein vGlut146. Consistently, our data showed that phosphomimetic mutations in phosphobox-2 results disruption of Dyn1xA localization, perturbation of ultrafast endocytosis, and slower kinetics of vGlut1 retrieval. However, how these kinases interplay to regulate the interaction of Dyn1xA, Syndapin1 and Endophilin A1 for ultrafast endocytosis is unknown.”

It would be very helpful to include a final cartoon depicting the key protein-protein interactions regulated by dephosphorylation (activity) and the sequence of molecular events that leads to ultrafast endocytosis

As suggested, we made a model figure, (new Figure 7) showing how Dyn1xA and its interaction with EndoA and Syndapin1 increases the kinetics of endocytosis at synapses. Regarding the sequence of molecular events, we think that there are already dephosphorylated fraction of Dyn1xA molecules sitting on the endocytic zone at the resting state and they mediate ultrafast endocytosis. However, it is equally possible that activity-dependent dephosphorylation of Dyn1xA also may play a role (Jing et al. 2011, PMID: 21730063). However, we have no evidence about the sequence of activity dependent modulation of Dyn1xA and its binding partners during ultrafast endocytosis yet. This is much beyond what we have reported in this work and therefore, excluded from the model figure. We added the following to the end of the discussion:

p13, “Nonetheless, these results suggest that Dyn1xA long C-terminal extension allows multivalent interaction with endocytic proteins and that the high affinity interaction with Endophilin A1 permits phospho-regulation of their interaction and defines its function at synapses (Figure S7)”.

Figure legend Figure 7,

“Figure 7. Schematics depicting how specific isoforms Dyn1xA and Endophilin A mediate ultrafast endocytosis.

A splice variant of dynamin 1, Dyn1xA, but not other isoforms/variants can mediate ultrafast endocytosis. (A) Dyn1xA has 20 amino acid extension which introduces a new high affinity Endophilin A1 binding site. Three amino acids, R846 at the splice site boundary, S851 and S857, act as long-distance element which can enhance affinity of proline rich motifs (PRM) to SH3 motif from outside of the PRM core sequence PxxP. (B) At a resting state, Dyn1xA accumulates at endocytic zone with SH3 containing BAR protein Syndapin 123 and Endophilin A1/2. When phosphobox-1 (Syndapin1 binding) and phosphobox-2 (Endophilin A1/2 binding, around S851/S857) within Dyn1xA PRD are phosphorylated, these proteins are diffuse within the cytoplasm. A dephosphorylated fraction of Dyn1xA molecules can interact with these BAR domain proteins. Loss of interactions including Dyn1xA-R846A or -S851/857D mutations, disrupts endocytic zone pre-accumulations. Consequently, ultrafast endocytosis fails.”

Reviewer #2 (Significance (Required)):

This is a remarkable and important advance in the field of endocytosis. The study reports a key discovery to understand the molecular mechanism of ultrafast endocytosis. Scientist interested in synaptic function and the general audience of cell biologist interested in membrane trafficking will very much value this study. The mechanism reported will potentially be included in textbooks in the near future.

My field of expertise includes molecular mechanisms of presynaptic function and membrane trafficking.

I have not enough experience to evaluate the quality of the NMR experiments, however, I do not have any problem at all with, in my opinion, elegant results reported.

We thank the reviewer for the positive outlook of our manuscript.

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Referee #2

Evidence, reproducibility and clarity

This is a compelling study that reports a key discovery to understand the molecular mechanism of ultrafast endocytosis. The authors demonstrate that the Dynamin splice version 1xA (Dynamin 1xA) uniquely binds Endophilin A, in contrast to Dynamin splice version 1xB (Dynamin 1xB) that does not bind Endophilin A and it is not required for ultrafast endocytosis. In addition, the Endophilin A binding occurs in a dephosphorylation-regulated manner. The study is carefully carried out and it is based on high quality data obtained by means of advanced biochemical methodologies, state-of-art flash-freezing electron microscopy analysis, superresolution microscopy and dynamic imaging of exo-and endocytosis in neuronal cultures. The results convincingly support the conclusions.

Although additional experiments are not essential to support the claims of the paper there is room, however, for improvement within the pHluorin experiments. These experiments, that are clearly informative and consistent with the rest of experimental data, do not apply the useful approach to separate endo- from exocytosis. The use of bafilomycin or folimycin to block the vesicular proton pump allows the unmasking the endocytosis that is occurring during the stimulus, that should correspond to ultrafast endocytosis. It would be very elegant to demonstrate that such a component, as expected according to the electron microscopy data, requires the binding of Endophilin A to Dynamin 1xA. If the authors have the pHluorin experiments running, the suggested experiments are very much doable because the reagents and the methodology is already in place and the new data could be generated in around six weeks.

The methods are carefully explained. Some of the experiments are only replicated in two cultures and the authors should justify the reasons to convince the audience that the approaches used have enough low variability for not increasing the n number. The pHluorin experiments, however, are performed only in a single culture; they should replicate these experiments in at least 3 different cultures (three different mice).

Minor comments:

Prior studies referenced appropriately and the the text and figures are clear and accurate.

1. The authors should discuss about the mediators (enzymes) responsible for dephosphorylation of phosphor-box 2 that is key for the Dynamin 1xa-Endophilin A interaction.
2. It would be very helpful to include a final cartoon depicting the key protein-protein interactions regulated by dephosphorylation (activity) and the sequence of molecular events that leads to ultrafast endocytosis

Significance

This is a remarkable and important advance in the field of endocytosis. The study reports a key discovery to understand the molecular mechanism of ultrafast endocytosis. Scientist interested in synaptic function and the general audience of cell biologist interested in membrane trafficking will very much value this study. The mechanism reported will potentially be included in textbooks in the near future.

My field of expertise includes molecular mechanisms of presynaptic function and membrane trafficking.

I have not enough experience to evaluate the quality of the NMR experiments, however, I do not have any problem at all with, in my opinion, elegant results reported.

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

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Imoto et al. analyze the specific role of the Dynamin1 splice variant Dyn1xA in so-called ultrafast endocytosis, an important mechanism of synaptic vesicle recycling at synapses. In a previous publication (Imoto et al. Neuron 2022), some of the authors had shown that Dyn1xA, and not the other splice variant Dyn1xB, is essential for ultrafast endocytosis. Moreover, Dyn1xA forms clusters around the active zone for exocytosis and interacts with Syndapin 1 in a phosphorylation dependent manner. However, it was unclear which molecular interactions underlie the specific role of Dyn1xA. Here, the authors provide convincing evidence with pull down assays and CSP that Dyn1xA PRR interacts with EndophilinA1/2 with two binding sites. The first binding site lies in the part common to xA and xB, was previously characterized. The second site was previously uncharacterized, is specific for Dyn1xA, and is regulated by phosphorylation (phosphobox 2). The location of these splice variants and mutated forms at presynaptic sites correlate with the prediction made by the biochemical assays. Finally, the authors perform rescue experiments ('flash and freeze' and VGLUT1-pHluorin imaging experiments) to show that Dyn1xA-EndophilinA1/2 binding is important for ultrafast endocytosis. I find the results interesting, providing an important step in the understanding of the interplay between dynamin and the endocytic proteins interacting with it (endophilin, syndapin, amphiphysin) in the context of synaptic vesicle recycling. The manuscript is clearly written and for the most part the data supports the authors' conclusions (see specific comments below). However, there are some issues which need to be clarified before this manuscript is fully suitable for publication.*

Introduction: the dynx1B Calcineurin binding motif is written PxIxIT consensus but actual sequence is PRITISDP. Is this a typo? Figure 1: the difference between the constructs used in panels C and D is not clear. In D, is it a truncation without residues 796 and 845? If so, it should be labelled clearly in the Western blots. In Panel E, Dyn1xA 746-798 should be labeled Dyn1x 746-798 because it is common to both splice variants. For amphiphysin binding the authors write that "No difference in binding to Amphiphysin 1 was observed among these peptides (Figure1D-F)." They should write that Dyn1x 746-798 does not bind Amphiphysin1 SH3 domain, confirming the specificity of binding to the 833-838 motif. Figure S2. The panels are way too small to see the shifts and the labelling. Please provide bigger panels Figure 2 panel B. There is a typo in the connecting line between the sequence and the CSP peaks. It is 846 instead of 864 (after 839). Figure 3 panel E. In the text, the authors write that "Western blotting of the bound proteins from the R838A pull-down experiment showed that R838A almost abolished both Endophilin and Amphiphysin binding in xA806-864 (Figure 3D), and reduced Endophilin binding to xA-PRR (Figure 3E)." I think they should write "only slightly reduced Endophilin binding..." it is more faithful to the result and consistent with the conclusion that Endophilin A1 has two binding sites on Dyn1xA PRR. It is unclear why the R846A mutant affects binding of Dyn1xA 806-864 but not Dyn1xA-PRR. Moreover, it affects binding to endophilin as well as amphiphysin, and therefore it is not specific. It is thus not correct to write that "R846 is the only residue found to specifically regulate the Dyn1 interaction with Endophilin as a part of an SDE". In the Discussion (page 11), the authors refer to the R846A mutation as specifically affecting Endophilin binding. This should be toned down, as it also affects Amphiphysin binding. For this important point, the data on quantification of Endophilin binding should be presented. Figure 3F-G: what do the star symbols represent in the graphs? I guess the abscissa represents retention time. Please write it clearly instead of a second ordinate for molecular mass, which does not make much sense if this reflects the estimate for the 3 conditions. Figure 4: The statement that "By contrast [to Dyn1xA], Endophilin A1 or A2 formed multiple clusters (1-5 clusters)" is not at all clear on the presented pictures. The authors should provide views of portions of axons with several varicosities, for the reader to appreciate the cases where there are more EndoA clusters than Dyn1 clusters. Moreover, overexpression of EndophilinA1/2-mCherry is not sufficient to assess its localization. Please consider either immunofluorescence of genome editing (e.g. Orange or TKIT techniques). The analysis of the confocal microscopy data is not explained. How is the number of clusters determined? How far apart are they? Confocal microscopy may not have the resolution to distinguish clusters within a synapse. For the STED microscopy, a representation of the processed image (after deconvolution) and the localization of the peaks would be important to assess the measurement of distances. If Dyn1xA S851/857D is more diffuse, are there still peaks to measure for every synapse? Figures 5 and 6: No specific comment. The data and its analysis is very nice and elegant. The comment on the lack of rescue of Dyn1xA on endosome maturation may be a bit overstated, because many "controls" (shRNA control Figure S5 or Dyn3 KO in Imoto et al. 2022) have a significant number of endosomes 10 s after stimulation. By the way, why did the authors use Dyn1 KO in this study, and not Dyn1.3 DKO as in Imoto et al. 2022? In the Discussion, the authors present the binding sites (for endophilin and amphiphysin SH3 domains) as independent. However, these proteins form dimers or even multimers as they cluster around the neck of a forming vesicle. Even though they provide evidence in vitro (Figure 3) that in these conditions of high concentration one dyn1xA-PRR binds one SH3 domain, in cells multiple binding sites on the PRR to these proteins may involve avidity effects, as discussed for example in Rosendale et al. 2019 doi 10.1038/s41467-019-12434-9. For example, the high affinity binding of Dyn1-PRR to amphiphysin cannot be explained only by the sequence 830-838.

Significance

This study provides a significant advance on the mechanisms of dynamin recruitment to endocytic zones in presynaptic terminals. The work adds a significant step by experienced labs (Robinson, Watanabe) who have provided important insight in the mechanisms by many publications in the last years.

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Reply to the reviewers

Please find below a point-by-point reply to the reviewers, with our comments in plain text, and reviewer comments in italics. Direct quotations of MS revisions in the below point-by-point reply are in quotation marks.

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

**The manuscript "Circadian regulation of protein turnover and proteome renewal" investigates the role of protein degradation in the circadian control of proteostasis. The researchers suggest that the relatively static levels of protein levels in a cell are incongruent with the known oscillation in protein synthesis. They therefore hypothesize that there should be a compensatory mechanism to counteract rhythmic protein synthesis, rhythmic protein degradation. To investigate this, they employ bulk pulse chase labeling to study the process of degradation. They identify a synchronization between the creation and turnover of proteins in a cell, implying the clock helps to maintain homeostasis through a novel mechanism. They note that these phases align with energy availability, granting a plausible reasoning behind the biological implementation of this regulation. In summary, this is a sound manuscript that adds to the research field. The experiments in this manuscript are well thought out, organized, and explained. In general, the authors do not go further in their conclusions than I think is warranted given the data that they have, though I think that there are some key items that should be addressed before the publication of this manuscript. *

Thank you for reading and appreciating our work

Major notes: 1) In figure 1, a clearer idea of what the ** means would be appreciated. What was the standard of significance for this measure?

Thank you, this was already reported in the methods section but is now reported in the figure legend also.

* 2) In Figure 1b, it is important to note clearly in the text that the this is not a direct measure of protein degradation, but a subtractive proxy. Though I don't think that necessarily makes the authors conclusions incorrect, the same result could also be obtained if an extra 15% of the proteins were moved into the insoluble fraction. This is the same for Figure 1E and F. *

Considering only the pulse shown in the left-hand graph of 1B, the reviewer is correct that this could arise by rhythmic partitioning of nascently synthesised proteins between digitonin-soluble and insoluble fractions. This could not readily explain the variation in the % of nascently synthesised digitonin-soluble protein that is degraded however (right hand graph), hence the need for pulse-chase rather than pulse alone. As such, we do not exclude circadian-regulated solubility of nascently synthesised protein or that there is a rhythm of protein synthesis in the soluble fraction, both are likely true. Rather Figure 1B indicates the relative proportion of nascently-synthesised protein in the soluble fraction that is degraded within 1h of synthesis is not constant over time. This is consistent with current understanding of the regulated increase in activity of protein quality control mechanisms (including proteasome-mediated degradation) that are required to maintain protein homeostasis upon an increase in bulk translation (Gandin and Topisirovic, Translation, 2014).

In contrast, the lysates probed in Fig 1F were extracted in denaturing urea/thiourea buffer and so cannot be explained by variation in protein solubility.

Considering 1E, to explain this result entirely through solubility changes would require that puromycinylated polypeptides to become more soluble, at discrete phases of the circadian cycle, but only when the proteasome is inhibited. Whilst we cannot formerly exclude this possibility, we are not aware of evidence to support it, whereas there is prior evidence supporting circadian regulation of protein synthesis and proteasome activity.

To communicate all of this more clearly we have made the following revisions to the text:

Page 6: ".The experiment was performed over a 24h time series followed by soluble protein extraction using digitonin, which preferentially permeabilises the plasma membrane over organelle membrane."

Page 6: " Importantly, the proportion of degraded protein varied over time, being highest at around the same time as increased protein synthesis (Fig 1B), indicating time-of-day variation in digitonin-soluble protein turnover which cannot be solely attributed to previously reported circadian regulation of protein solubility (Stangherlin et al, 2021b). Rather, it suggests that global rates of protein degradation may be co-ordinated with protein synthesis rates, and may vary over the circadian cycle."

Fig 1a legend: "...with digitonin buffer"

Fig 1e legend: "...in digitonin buffer"

Fig1f legend: "... and extracted with urea/thiourea buffer"

* 3) In figure 1c, is the noted oscillation in protease activity due to the oscillation of these proteins? What are the predicted mechanisms behind this? I don't think that this is necessarily within the scope of this paper but should be addressed in the discussion. Also, the peak degradation rate from Figure 1B is 4 hours before the peak enzyme activities. How can this observation be reconciled? *

Besides this study, our two previous proteomic investigations of the fibroblast circadian proteome detected no biologically significant or consistent rhythm in proteasome subunit abundance (Wong et al., EMBO J, 2021; Hoyle et al., Science Translational Medicine, 2017). Moreover, proteasomes are long-lived stable complexes whose activity is determined by a combination of substrate-level, allosteric and post-translational regulatory mechanisms that includes their reversible sequestration into storage granules (Albert et al., PNAS, 2020; Fu et al., PNAS, 2021; Yasuda et al., Nature, 2020). It is therefore very likely that the observed rhythm in trypsin- and chymotrypsin-like activity occurs post-translationally. Proteasome subunit composition is also known to change, which might be another reason for differences between the protease activities (Marshall and Vierstra, Front Mol Biosci, 2019; Zheng et al., J Neurochem, 2012).

Due to the nature of the experiment, the degradation rate inferred from Figure 1B does not reflect proteasome activity, exclusively. Rather it reflects the combined sum of processes that remove nascently produced proteins from the cell's digitonin-soluble fraction, which includes proteasomal degradation, but also autophagy, protein secretion and sequestration into other compartments. Therefore, the peak degradation in Fig 1B would not necessarily be expected to coincide with the peak of proteasome activity in Fig 1C. Figure 1A/B is intended as an exemplar for the investigation's rationale and was the first to be performed chronologically.

To communicate this succinctly, we have revised the relevant text as follows:

Page 7: "Previous proteomics studies under similar conditions have revealed minimal circadian variation in proteasome subunit abundance (Wong et al, 2022), suggesting that proteasome activity rhythmicity, and therefore rhythms in UPS-mediated protein degradation, are regulated post-translationally (Marshall & Vierstra, 2019; Hansen et al, 2021)"

* 4) For the pSILAC analysis, the incorporation scheme has a six-hour window between the comparison of the light and heavy peptides. This makes it somewhat difficult to assess whether you are looking a clock effect from T1 or T1+6. This does not negate the findings, but it does question when the synthesis is occurring and what is being compared, which I think should be more clearly discussed in the manuscript. This is discussed later in the manuscript but should be mentioned in this section. *

Thank you for this suggestion. To communicate this more clearly, we have rearranged the labels at the top of schematic graphs in figures 2b and 3b in order to clearly distinguish the pulse-labelling window from the time of sample collection. The following text has been added to the methods section:

Page 9: "To enable sufficient heavy labelling for detection, a 6h time window was employed, thus measuring synthesis and abundance within each quarter of the circadian cycle "

* 5) There are no error bars on figure 2C. What the pSILAC just done in a singlet? If so, the rhythms estimation is likely a large overestimate and should be noted. *

This first pSILAC experiment was performed in singlet with respect to external time for the RAIN analysis, but is duplicate for the two-way ANOVA that is also reported, by treating each cycle as a separate replicate. In fact, the 6.2% of proteins that were significantly rhythmically abundant by RAIN actually agree well with two previous experiments we performed using mouse fibroblasts under identical conditions: the first with 3h resolution over 3 cycles in singlet (7% rhythmic), the second with 4 biological independent replicates over one cycle (8% rhythmic) (Wong et al., EMBO J, 2021). The curve fits shown in 2C are the standard damped sine wave fits, with p-values from RAIN reported in the figure legend.­­

Most importantly however, and as noted in the text, the absolute % of rhythmically abundant proteins is rather irrelevant and indeed the absolute numbers of 'rhythmic' proteins can vary wildly, dependent on the analysis method and stringency. The only important point to be gleaned from the estimates shown in Figure 2e is that by either statistical test, most rhythmically abundant proteins are not rhythmically synthesised, and vice versa; however, the % of proteins that are both rhythmically synthesised and rhythmically abundant is 6 to 11--fold higher than would be expected by chance (taking proteins rhythmic by RAIN and ANOVA, respectively; in both cases the overlap between the two sets is highly significant) . This serves as a positive control, i.e., a minority of proteins show correlated rhythms of synthesis and abundance that are consistent with the canonical activity of 'clock-controlled genes' which cannot be explained by overestimation of rhythmicity.

Odds Ratio comparison synthesis vs total

Synthesis rhythmic by RAIN - listA size=148, e.g. A8Y5H7, B2RUR8, E9Q4N7

Total rhythmic by RAIN - listB size=149, e.g. A1A5B6, A2A6T1, A2AI08

Intersection size=34, e.g. A8Y5H7, O08795, O54910

Union size=263, e.g. A8Y5H7, B2RUR8, E9Q4N7

Genome size=2528

Contingency Table:

notA inA

notB 2265 114

inB 115 34

Overlapping p-value=5.4e-13

Odds ratio=5.9

Overlap tested using Fisher's exact test (alternative=greater)

Jaccard Index=0.1

Synthesis rhythmic by ANOVA - listA size=66, e.g. A8Y5H7, O35639, O55143

Total rhythmic by ANOVA - listB size=83, e.g. A8Y5H7, B2RQC6, E9Q6J5

Intersection size=16, e.g. A8Y5H7, P22561-2, Q3TB82

Union size=133, e.g. A8Y5H7, O35639, O55143

Genome size=2528

Contingency Table:

notA inA

notB 2395 50

inB 67 16

Overlapping p-value=9.7e-11

Odds ratio=11.4

Overlap tested using Fisher's exact test (alternative=greater)

Jaccard Index=0.1

Nevertheless, we agree with the reviewer's general point and have revised the text as follows:

Page 9: "... and may be susceptible to overestimation of rhythmicity."

Page 9: "Consistent with similar previous studies, Page 9: "The proportion of such proteins was more than expected by chance (pMethods, Page 21: "...(n=1 per timepoint)"

* 6) Why were the genes selected in 2C? these are not discussed anywhere else in the manuscript.*

These are simply illustrative examples so that the reader can better understand what we mean, i.e., two proteins in different phases and one that did not change, all within a similar range of abundance. The selected proteins were not discussed because we do not expect the reader to attach any specific meaning to them. We have revised the figure to include in 2C examples of each rhythmicity category shown in 2E. To make this clear, we now state the following:

Figure 2 legend: "No specific meaning is inferred from the protein identities”.

• 7) The authors note that for Figure 2 "These observations are consistent with widespread rhythmic regulation of protein degradation." However, only 5-10% of the proteome is oscillating at any level and less with a discrepancy between synthesis and abundance, so "widespread" is an exaggeration and this statement should be limited to the degradation in the rhythmic proteome. *

We take the reviewer's point, but the term rhythmic proteome is also inaccurate since half the proteins with rhythmic degradation did not show an abundance rhythm in both mass spec experiments. We therefore revised this sentence as follows:

Page 10: "These observations are consistent with widespread temporal organisation of protein degradation within the circadian-regulated proteome."

* 8) The authors note that their more developed strategy in figure 3 would allow for the detection of less abundant proteins. However, they do not discuss that they in fact found less proteins overall, or if they were able to detect proteins of lower abundance. This is of some concern in determining if this is indeed the better method that they predict. How can the authors reconcile this issue? How can they rationalize this explains their increase in oscillating elements? *

Thank you for raising this point, we did not explain ourselves sufficiently clearly. As stated in the revised text, once we had analysed the first iteration of pSILAC (Fig 2), we realised that detection of heavy-labelled proteins was "inevitably limited and biased the proteome coverage towards abundant proteins with higher synthesis rates". In other words, in order to be considered in our analysis both unlabelled and heavy-labelled peptides needed to be detected in every sample at every time point. In fact, if we do not consider heavy-labelling, the overall coverage in the Fig 3 experiment (6577 proteins) was better than the Figure 2 experiment (6264 proteins), as expected, due to technical improvements in the methods used (by the time of the experiment in Fig. 3, we were able to perform the analysis using mass spectrometry techniques with better fractionation and detection, namely FAIMS and MS3). When the analysis criteria are applied however, this falls to 2302 and 2528 proteins, respectively. Because of the way that mass spectrometry works, many proteins needed to be excluded from analysis because the heavy label wasn't detected in one or more samples. In these cases, we cannot infer that no heavy-labelled protein was present in that sample or even that it was present at lower levels than other samples - it simply wasn't detected and therefore we cannot make any quantitative comparisons. Non-detection of any given heavy peptide may occur for several reasons, the most likely being that it co-elutes from the chromatography column at the same time as other much more abundant (light) peptides and simply escapes detection. This is an unavoidable limitation of the technique, we hope the reviewer can understand our need to restrict the analysis to those proteins whose nascent synthesis, and total abundance in the MMC fraction, can be confidently quantified.

As the experiments in Fig 2 and Fig 3 were performed independently, with separate TMT sets and different instrumentation, we are also unable to compare absolute abundances of the proteins between the two.

To communicate this more clearly we have amended Figures 2e and 3e to state the total coverage in the legends, as well as clearly stating the coverage of heavy-labelled proteins in the figure itself. We have also added the following explanation to the text:

Page 11:

“Despite enriching for only one cellular compartment, the overall coverage in this experiment was similar to the previous one (6577 and 6264 proteins, respectively), due to the altered and more targeted approach; with heavy peptides detected for 2302 proteins."

*9) In the comparison of complex turnover rates, the authors need to provide a metric that backs their statement that "the majority of component subunits not only showed similar average heavy to total protein ratios but also a similar change in synthesis over the daily cycle" for figure 3F. *

Our apologies for this oversight, this is now presented in new Fig S3D.

* 10) In reference to the AHA incorporation, why is the hypothesis not that, like the puramycin, you would not see oscillation unless you add BTZ? Shouldn't the active degradation regulate the incorporation of AHA such that there is no visible rhythm unless you suppress degradation? *

AHA is a methionine analogue that is sparsely incorporated into polypeptide chains with minimal effect on protein function/structure (Dietrich et al., PNAS, 2006). Unlike puromycin, therefore, AHA does not lead to chain termination or protein misfolding/degradation (Dermit et al., Mol Biosyst, 2017) and so pulsed application at different phases of the circadian cycle is sufficient to reveal protein synthesis rhythms. The novelty in Fig 3H is the combination of AHA labelling with native PAGE that allows us to validate rhythmic production of high molecular weight protein complexes. This would not be possible with puromycin because prematurely-terminated polypeptide chains are not able to assemble into native complexes unless chain termination happens to occur at the extreme C-terminus and the C-terminus does not partake in any intermolecular interactions within the assembled complex.

* 11) The authors claim that there is enrichment of the actin cytoskeleton, but where this data can be found should be explained. The only thing that is shown is a few selected graphs of proteins in this pathway. *

We previously reported circadian regulation of the actin cytoskeleton in Hoyle et al. (Sci Trans Med, 2017). The extremely high relative amplitude of Beta-actin (the structural component of microfilaments) in the MMC fraction is, in and of itself, entirely sufficient to demonstrate a circadian rhythm in the relative ratio of globular to filamentous actin that was originally identified by Ueli Schibler's lab (Gerber et al., Cell, 2013) and then shown to have a cell-autonomous basis in fibroblasts in Hoyle et al (2017). We have included further examples of an actin-binding protein (Corinin1b) and a motor protein (Myosin 6) to further illustrate this, but do not feel further discussion is warranted because it was comprehensively addressed in our previous work. The enrichment for actin was determined by GO analysis, which is now shown in the Fig 4A and referred to in the text.

The important point in Fig 4C is the difference in phase with the examples shown in Fig 4B and summarised in Figure 4A, i.e., there are a small number of proteins whose presence in the MMC fraction is highest in advance of the majority of rhythmically abundant proteins, but this earlier group doesn't show any significant synthesis rhythm. Actin is one of the most abundant cellular proteins, and by mass it accounts for 67% of the circadian variation of rhythmically abundant proteins that peak in this fraction at the same phase. All these data and analyses are available for scrutiny in Supplementary Table 2.

To communicate this more clearly we have expanded on this point as follows:

Page 13: " These proteins were enriched by 9-fold for actin and associated regulators of the actin cytoskeleton (q* 12) The authors note an oscillation in the total levels of p-eif2, commenting that these do not arise from the rhythms in total eif2a but temperature and feeding rhythms. However, unless I misunderstood, this work was done in fibroblast cell culture, so in this case, where would these temperature and feeding rhythms come from? *

We were insufficiently clear. Daily rhythms of p-eIF2 have been observed under physiological conditions in mouse, in vivo. We do not observe similar rhythms in cultured fibroblasts under constant conditions unless the cells are challenged by stress. By inference therefore, it seems likely that daily rhythms of p-eIF2 in vivo arise from the interaction between cell-autonomous mechanisms and daily systemic cues such as, insulin/IGF-1 signalling and body temperature that are in turn driven by daily rhythms in CNS control, daily feed/fast rhythms and daily rest/activity rhythms, respectively. We have amended the text as follows:

Page 15: "...and so suggest that daily p-eIF2α rhythms in mouse tissues likely arise through the interaction between cell-autonomous mechanisms and daily cycles of systemic cues, e.g., insulin/IGF-1 signalling and body temperature rhythms driven by daily feed/fast and rest/activity cycles, respectively."

* 13) In Figure 5d, the treatment impeding degradation is causing cell death while the inhibition of translation does not. However, wouldn't too much, or not enough, translation, without compensatory regulation from degradation cause a problem in the same way that degradation does? *

It is well-established that acute treatment with high concentrations of proteasomal inhibitors rapidly leads to proteotoxic stress that will trigger apoptosis unless resolved (Dantuma and Lindsten, Cardiovasc Res, 2010). Treatment with CHX is certainly stressful to cells, but in a different way, and cells die through mechanisms generally regarded to be necrotic and certainly do not involve the canonical proteotoxic stress responses that are activated by MG132 and similar drugs. Our findings show that, by whatever mechanisms cells die with CHX treatment, it does not change over the circadian cycle whereas death via proteotoxic stress does, consistent with our prediction. We hope the reviewer agrees it is beyond the scope of our study to explain why CHX-mediated cell death does not show a circadian rhythm in mouse fibroblasts.

*Reviewer #1 (Significance (Required)):

*The information that stems from this work is relevant and of interest to circadian clock field as how the regulation of the output of the circadian clock is implemented is still a major question in the field. This manuscript suggests a novel and plausible method for how, at least in part, this regulation occurs. However, the manuscript uses methods that do not measure degradation directly, which is a minor limitation. In addition, the mechanisms by which this regulation is imparted are not addressed in any meaningful way, even in the discussion.

We are sorry that we did not adequately discuss the extensive previous work that has already addressed regulatory mechanisms. We would like to stress that this manuscript concerns protein turnover and proteome renewal, of which degradation is obviously an important part but not the sole focus.

To communicate this more clearly, we have amended the title to:

"Circadian regulation of macromolecular complex turnover and proteome renewal"

... which we previously explicitly predicted in the discussion of previous papers (Feeney et al., Nature, 2016; O'Neill et al., Nat Comms, 2020; Wong et al., EMBO J, 2022) and our recent review (Stangherlin et al., Curr Opin Syst Biol, 2021).

With respect to measurement of degradation - Physiologically, cellular rates of proteasomal degradation are so intimately coupled with protein synthesis that, over circadian timescales, the former cannot meaningfully be studied in isolation. It is possible that the reviewer is alluding to historical methods that measure change over time in the presence of translational or proteasomal inhibitors, but these have long been known to introduce artifacts - because translational inhibition rapidly leads to reduced proteasome activity, whereas proteasomal inhibition rapidly reduces protein synthesis rates through the integrated stress response. We would be interested to hear of any more direct method for measuring protein degradation proteome-wide than the pulsed SILAC method we developed, as we are not aware of any. Even proteasomal proximity labelling coupled with MG132 treatment, recently developed by the Ori lab, does not directly measure degradation (bioarxiv https://www.biorxiv.org/content/10.1101/2022.08.09.503299v1). By definition, degradation can only be measured through the disappearance of something that was previously present, usually by comparing its rate of production with the change in steady state concentration (if any), which we have done using multiple methods.

With respect to regulation of degradation - We speculated on the mechanisms regulating rhythms in protein turnover in our several previous papers (Feeney et al., Nature, 2016; O'Neill et al., Nat Comms, 2020; Wong et al., EMBO J, 2021; Stangherlin et al, Nat Comms, 2021), whereas outside the circadian field these mechanisms have been addressed extensively. This was also discussed in detail in our recent review on the topic (see Stangherlin et al., COISB, 2021). In this review, we lay out the evidence for a model whereby most aspects of circadian cellular physiology might be explained by daily rhythms in the activity of mammalian target-of-rapamycin complexes (mTORC). This model makes multiple predictions and informs the central hypothesis which is tested in the current manuscript: that circadian rhythms in complex turnover and proteome renewal should be prevalent over abundance rhythms. An enormous body of work over the last two decades has already clearly established mTORC1 as the master regulator of bulk protein synthesis and degradation, and a substantial number of independent observations have demonstrated circadian regulation of mTORC1 activity in vivo and in cultured cells. The mechanisms that drive cell-autonomous mTORC1 signalling are only partially understood (e.g. Feeney et al., Nature, 2016; Wu et al., Cell Metab, 2019), and we continue to explore this experimentally but they certainly lie well beyond the scope of this investigation.

Therefore, to address the reviewer's concern about inadequate discussion of mechanism, we have expanded on mTORC in the introduction and discussion, as follows:

Page 3: "Daily rhythms of PERIOD and mTORC activity facilitate daily rhythms of gene expression and protein synthesis. In particular, mTORC1 is a master regulator of bulk 5'-cap-dependent protein synthesis, degradation and ribosome biogenesis (Valvezan & Manning, 2019) whose activity is circadian-regulated in tissues and in cultured cells (Ramanathan et al, 2018; Feeney et al, 2016a; Stangherlin et al, 2021b; Mauvoisin et al, 2014; Jouffe et al, 2013; Sinturel et al, 2017; Cao, 2018). It is plausible that daily rhythms of mTORC activity underlie many aspects of daily physiology (Crosby et al, 2019; Stangherlin et al, 2021a; Beale et al, 2023b)."

Page 17: "The mechanistic underpinnings for cell-autonomous circadian regulation of the translation and degradation machineries remain to be fully explored, but are likely to be driven by daily rhythms in the activity of mTORC: a key regulator of protein synthesis and degradation as well as macromolecular crowding and sequestration (Stangherlin et al, 2021b, 2021a; Cao, 2018; Adegoke et al, 2019; Ben-Sahra & Manning, 2017; Delarue et al, 2018). In particular, global protein synthesis rates are greatest when mTORC1 activity is highest, in tissues and cultured cells, whereas pharmacological treatments that inhibit mTORC1 activity reduce daily variation in crowding and protein synthesis rates (Feeney et al, 2016a; Lipton et al, 2015; Stangherlin et al, 2021b). Given our focus on proteomic flux and translation-associated protein quality control, autophagy was not directly within the scope of this study but is also mTORC-regulated and subject to daily regulation (Ma et al, 2011; Ryzhikov et al, 2019). In vivo, daily regulation of mTORC activity arises primarily through growth factor signalling associated with daily feed/fast cycles (Crosby et al, 2019; Byles et al, 2021). The mechanisms facilitating cell-autonomous circadian mTORC activity rhythms are incompletely understood but may include Mg.ATP availability (Feeney et al, 2016a) and its direct regulation by PERIOD2 (Wu et al, 2019). This will be an important area for future work."

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

Summary: This is a very interesting and well written paper that addresses key questions in the circadian organization of proteostasis. The paper investigates origins of cellular circadian rhythms, invoking a premise early that there is a poor correlation between rhythmic gene expression - regulated by the canonical TTFL - and rhythms of the proteome, which are rather meager. Specifically, they ask how a relatively stable proteome is possible if cells engage in rhythms of cellular protein synthesis? Their hypothesis is that protein degradation must rhythmically compensate for rhythms of synthesis and much of the manuscript is focused on defining the relationship between rhythmic global synthesis and rhythmic degradation. They employ a series of detailed proteomic investigations and biochemical assessments of protein synthesis coupled with various circadian reporters to assess proteosome function. The proteomic experiments reveal a limited number of proteins with oscillations in either synthesis or abundance or both and no discernible pathway organization however, a followup and more refined study that utilized fractionated samples and boosted heavy SILAC identified strikingly, that many proteins in relatively heavy fractions are rhythmic and that these fall into possible complexes including ribosome and chaperonins. Finally, they perform in vivo experiments testing whether the timing of proteotoxic stimuli regulates the degree of the integrated stress response measured as pEif2a. Overall, I think that this is a fascinating paper that addresses and important question but falls short on mechanistically unifying them and completely contextualizing the findings in light of the canonical modes of circadian timekeeping leaving us with an important, but mostly descriptive set of findings. In addition, there are a number of important questions about data interpretation, some issues with data quality that should be addressed outlined below. With revision and further explication, this study will be an excellent addition to the growing field of circadian organization of the cellular proteome. *

Thank you for reading and appreciating our work

*Major and minor Comments. Figure 1. Fig 1a. The difference in Pulse and Chase at ZT24 does not appear to reflect the quantified data in 1b. This should be reconciled to make the figure convincing. *

When working with radioactive cell lysates it is not possible to equalise the level of protein loaded on each gel beforehand as would happen with a western blot, for example. For this reason, the radioactive signal was normalised to the protein level subsequently measured by coomassie staining, as is standard practise for this type of assay, with all 4 replicates being shown in supplementary Fig.1A. An overnight phosphor screen image is presented in the main Fig.1A for illustrative purposes, but we take the point that this might not be immediately obvious. In revised Fig 1A we therefore now also show the relevant coomassie as well as labelling to make clear that the radioactive signal was normalised to protein levels.

* How was the timing of the chase collection determined? *

For these proof-of-principle experiments, we empirically determined the minimum duration of pulse and chase necessary to detect a quantifiable signal.

*Fig 1d-e. What is the evidence that puro labeling results in 'rapid' turnover. *

Apologies, this has been established for some time. Some additional papers are now cited in this section of the text (Liu et al, PNAS, 2012; Lacsina et al., PLoS One, 2011; Szeto et al., Autophagy, 2006)

*Fig 1e seems to be missing the data from the treated and untreated conditions? How are the lines produced (e.g. linear versus rhythmic? Are these drawn lines or actual regressions?). *

Fig 1e depicts the result of the experiment schematically explained in 1d. The only conditions were +Puro or +Puro+BTZ. There was no completely untreated condition, as puromycin incorporation is the basis of the assay (Lacsina et al., PLoS One, 2012; Szeto et al., Autophagy, 2006) and puromycin does not occur naturally in cells. We realise the figure could potentially be confusing without the associated raw data (anti-puromycin blots) - these are shown in supplementary Fig. 2A.

To explain the method more clearly, the following has been added to the results section where this experiment is described:

" As determined by anti-puromycin western blots, over two days under constant conditions, puromycin incorporation in the presence of BTZ showed significant circadian variation. In contrast, cells that were treated with puromycin alone showed no such variation, and nor did total cellular protein levels (Fig 1E, Fig S2A).”

The fit lines are produced by statistical comparison of fits, i.e., our hypothesis (damped cosine fit) vs null hypothesis (no or constant change over time, linear fit, y = mx+c), using sum-of-squares F test. The statistically preferred fit is plotted and p-value displayed on the graph, i.e., the regression line of the preferred fit and parameters are plotted. These details are reported in the figure legends.

* Why was 30 minutes chosen as labeling time? It seems hard to understand here how protein degradation kinetics can be measured by puromycin labeling if the authors' claim that puromycin labeling potentially changes degradation rates as a function - primary or secondary - of the labeling itself. It seems they are measuring the potential to degrade proteins. *

Puromycin labelling is a 20 year-old widely-used technique that can be employed in a range of applications. It was first used in a circadian context by Lipton et al (Cell, 2015) whose work we quickly followed (Feeney et al, Nature, 2016). Briefly, puromycin mimics tyrosyl-tRNA to block translation by labelling and releasing elongating polypeptide chains from translating ribosomes. When used at low concentrations (1 ug/mL in this case) puromycin is sparsely and sporadically incorporated into a small minority of elongating polypeptide chains. Those prematurely terminated chains have puromycin at the C-terminus, which can be detected by western blotting. We chose 30 minutes after optimisation experiments, as it was the shortest incubation time where a robust signal could be observed in these cells with this concentration of puromycin. The puromycinylated peptides are preferentially degraded by the ubiquitin-proteasome system because they are efficiently recognised as misfolded/aberrant proteins by chaperones within tens of minutes of being translated. Unless used at much higher concentrations, or over much longer timescales, there is no reason to believe that puromycin affects the degradation machinery itself, but the degradation of puromycinylated peptides depends on the proteasome. Therefore, puromycin+a proteasome inhibitor provides a reliable proxy for translation rate in the preceding 30 minutes, whereas puromycin alone tells us the steady state concentration under normal conditions, i.e., where proteasomes remain active. By subtracting the latter from the former we can infer the level of degradation of puromycinylated peptides that must have occurred in the previous 30 minutes. It is not a perfect technique, but its results agree with other findings in this manuscript: that protein turnover varies more than steady state protein abundance. With respect to the potential to degrade proteins, this is measured in Fig 1C.

* How do they determine that they are measuring degradation of functionally relevant proteins as opposed to a host of premature truncations? *

We do not. This is measured by stable isotope labelling in Figures 2-4. Figure 1 provides the rationale for what follows in subsequent figures, i.e., proof-principle experiments suggesting that turnover is not constant over the circadian cycle. No single experiment in Figure 1 is expected to convince the reader that of circadian turnover. Rather, several independent methods suggest that bulk protein synthesis and degradation (turnover) are not constant over time, and deviate from the null hypothesis with variation that appears to change over the 24h circadian cycle.

* Fig 1e bottom - again is this a true regression line? *

It is not a regression line, otherwise a p-value of fit would be shown. Fig1e bottom shows the bioluminescence measured at each timepoint from parallel control cultures (average of triplicates, error bars shown as dotted lines). Due to very high temporal resolution (every 30 min) and robustness of the cell line, it appears as a virtually perfect damped (co)sine wave. We apologise that this was not explained more clearly in the figure legend, now amended as follows:

"Parallel PER2::LUC bioluminescence recording from replicate cell cultures (mean +/- SEM, every 30 min) is shown below, acting as phase marker."

*Perhaps two time points should be examined here - similar to the pulse chase performed with 35S labeling? *

We are sorry we were not fully clear with our method here. The puromycin (+/- BTZ) labelling was performed over two days every 4h (so 12 timepoints in total), which can be inferred from the data points in the top two graphs in Fig. 1E, and x-axis - but is now also clearly stated in the figure legend. The bottom right graph was a continuous bioluminescence recording, integrated every 30 min from the set of parallel culture dishes. The bioluminescence data serves as a circadian phase marker, so that we can infer at which biological times synthesis and inferred turnover was higher vs lower.

We’ve adjusted the text to explain our method more clearly:

“Acute (30 min) puromycin treatment of cells in culture, with or without proteasomal inhibition (by bortezomib, BTZ), allowed us to measure both total nascent polypeptide production (+BTZ) and the amount of nascent polypeptides remaining when the UPS remained active (-BTZ). This allowed inference of the level of UPS-mediated degradation of puromycylated peptides within each time window, as a proxy for nascent protein turnover (Fig. 1D).”

* Fig 1f. It appears that Puro labeling results in a rhythm between ZT1 and ZT13 but no statistic is provided and appears that the 'ns' is the results of variance in the data as opposed to difference in means? - would this not contradict the cellular result? What accounts for the rhythm reversal in the presence/absence of BTZ. *

To be clear, we measured the level of puromycin incorporation in mouse liver in vivo following a similar method employed by Lipton et al, Cell, 2015 (Figure 2). The prediction was that, exactly as in cells (Fig 1E), treatment with a proteasome inhibitor would lead to a much greater increase in puromycinylated peptides at ZT13 than ZT1, because this is when protein synthesis is known to be higher and thus (we predict) protein degradation should also be higher. The experiment was not designed or powered to detect a time effect, it was designed to detect an interaction between time-of-puromycin treatment and BTZ, with the specific prediction being that BTZ would have a greater effect during the active phase. This is what we observed.

* While the authors have previously demonstrated an increase in rhythmicity of the proteome in Cry1/Cry2 double knockout cells, it would have been welcome here to test a global loss of circadian transcription in the degradation assay. One might expect that these rhythms would also be even higher. What I am really asking is: what is the mechanism for rhythmic degradation and is it dependent on the canonical clock? *

To address the reviewer's curiosity, we used the proteasome-Glo assay (also used in Fig 1C) to assess whether there was an interaction between genotype (WT vs CKO) and time at opposite phases of the circadian cycle over 2 days. We found a significant interaction by two-way ANOVA, indicating that components of the 'canonical clock' regulate the temporal organisation of proteasomal activity (see revised Figure S1). Circadian regulation of mammalian cellular functions, such as protein turnover, is a complex and dynamic process, whereas gene deletion affects the steady state and may be epistatic to phenotype rather than revealing gene function. We are therefore reluctant to speculate what this result means in the present manuscript, which is focused entirely on testing the hypothesis that global protein turnover and complex biogenesis have cell-intrinsic circadian rhythms in non-stressed, wild type cells.

To communicate this, the text has been revised as follows:

"Moreover, we detected a significant interaction between genotype and biological time when comparing trypsin-lik proteasome activity between wild type and Cryptochrome1/2-deficient cells, that lack canonical circadian transcriptional feedback repression (Fig S1B-E). "

* **Fig 2. How was the 'fixed window' timeframe determined? *

A trial experiment was performed with labelling windows of various length, and 6h was determined to be the shortest window where enough heavy label incorporation was detected to be able to assess circadian changes. This was the case with our first methodology, which was subsequently improved (Figure 3), and therefore labelling window reduced to 1.5h.

* *Fig 3h. While admittedly difficult, the native PAGE is not of great quality and kind of unconvincing. Also not really sure why the AHA labeling is used here an nowhere else in the paper.

AHA is a methionine analogue that is sparsely incorporated into polypeptide chains with minimal effect on protein function/structure (Dietrich et al., PNAS, 2006). Unlike puromycin, therefore, AHA does not lead to chain termination or protein misfolding/degradation (Dermit et al., Mol Biosyst, 2017). In Figure 1, the aim was to validate previous reports of rhythmic protein synthesis assess whether there was any evidence for rhythmic turnover. To this end, we employed two independent methods (35S-labelling and puromycin-incorporation). We did not want to rely on AHA for measuring turnover: although it has been validated and used for this purpose in some studies (McShane et al., Cell, 2016), AHA is not fully equivalent to methionine, and cellular aminoacyl-tRNA synthetases have much higher affinity to methionine than they do to AHA (Ma and Yates, Expert Rev Proteomics, 2018). It is thus impossible to perform AHA labelling without methionine-free medium, and in turn methionine starvation and media changes are known to have an effect on cell signalling and cell metabolism, which would be particularly pronounced in circadian context (over days rather than over hours).

By contrast, in Fig 3H, we use AHA with native PAGE to specifically validate one inference from the mass spectrometry analyses: circadian production of high molecular weight protein complexes. This would not be possible with puromycin because prematurely terminated polypeptide chains are not able to assemble into native complexes unless chain termination happens to occur at the extreme C-terminus and the C-terminus does not partake in any intermolecular interactions within the assembled complex.

The raw data (full gels, all replicates) are presented in Figure S2e, which of course was used for quantification. We have now picked a different example for the main figure, which hopefully allows for clearer representation.

The text in the results section describing the AHA experiment is now amended as follows:

" To validate these observations by an orthogonal method, we pulse-labelled cells with methionine analogue L-azidohomoalanine (Dieterich et al, 2006). AHA is an exogenous substrate, that cells have lower affinity to than methionine, and it could potentially impact on stability of the labelled proteins (Ma & Yates, 2018) – therefore, we only used AHA to assess nascent complex synthesis, rather than turnover. We analysed the incorporation of the newly synthesised, AHA labelled proteins into highest molecular weight protein species detected under native-PAGE conditions (Fig 3H, S3F). We observed a high amplitude daily rhythm of AHA labelling, indicating the rhythmic translation and assembly of nascent protein complexes. Taken together, these results show that daily rhythms in synthesis and degradation may be particularly pertinent for subunits of macromolecular protein complexes"

Fig 4. I was a little disappointed here that the authors did not directly assess macromolecular assembly of at least one of their "hits" and demonstrate functional relevance and most of the analysis is maintained at a very superficial, systemic level. STRING assemblies are not terribly helpful without clear k-means clustering or some other clearly visualizable metric for stratifying and organizing the putative PPI data - this figure (S3) could be markedly improved.

We agree that validation is important. The ribosome is by far the most abundant macromolecular complex in the cell, and was one of the major complexes to show clear evidence for circadian regulation of turnover, but not abundance, by our pSILAC proteomics. To validate this result, we took advantage of two important observations: (1) that all fully assembled ribosomes incorporate ribosomal RNA (rRNA) which can readily be separated from other cellular RNA by density gradient centrifugation; (2) pulse-labelling with heavy uridine-15N2 allows nascent RNA to be distinguished from pre-existing RNA. Thus, combining stable isotope labelling with ribosome purification, we can distinguish nascently assembled ribosomes from total when the RNA is extracted, digested with RNAse, and the % heavy/total UMP quantified by mass spectrometry. These data are presented in new figure 5, and are consistent with findings in Figures 3/4 that circadian regulation of ribosome turnover is prevalent over abundance, and that the phase of highest ribosome turnover coincides with the phases of high translation and turnover overall. We hope by addressing the reviewer's question by an entirely orthogonal method, they can share more confidence in our conclusions.

The statistical metric for STRING, specifically the p-value for enrichment in physical protein-protein interactions, is presented in the main Fig. 3G. It is now also reported in the legend for new Figure S4 itself.

* Is it possible that some macromolecular complexes have rhythms because their constituent proteins have differential half-lives when in one complex compared with another in circadian time? This possibility was not discussed. *

To our knowledge, there is no evidence that any major macromolecular complex in the cell has a functionally significant rhythm in abundance on a cell-autonomous basis. The reviewer’s suggestion is an intriguing possibility, but we can think of no way that it could be measured, even in principle. The simplest interpretation of our data from the independent techniques we employ (pSILAC with fractionation, native PAGE + AHA incorporation) is a rhythm in synthesis.

*Fig. 5. Why is the first histogram in 3c not at unity? *

This measures the average fold-induction in aggregation when cells are treated with MG132 for 4h at the indicated timepoints. Unity would indicate no induction at all, so the presented quantifications show that MG132 always elicited an increase in aggregation, with an effect size that varied with circadian phase.

* Do ZT24 and ZT48 differ, similarly do ZT36 and ZT60?*

No, neither difference is statistically significant (adjusted p-values of p=0.9 and p=0.07, respectively). This is now specified in the figure legend. Tendency to aggregate is also likely to change as a function of time in culture, which is why we think there is a slight increase overall in the second day of the experiment.

* Fig S4f is not of good quality with missing eIF2a total and therefore no loading controls. *

Thank you for prompting us to double-check this. We found that the levels of eIF2a were quite variable between the animals, and therefore we performed this experiment with 6 biological replicates. We have double-checked the quantification, and have now excluded 3 unreliable samples (the ones with undetectable levels of total eIF2a – ZT18 +BTZ replicate 1 & ZT18 -BTZ replicate 2, as well as ZT6 +BTZ replicate 4, where a smear does not allow for a reliable quantification of phospho-eIF2a) instead of 2 that were excluded originally. This still leaves at least 5 biological replicates in each group. In fact, the difference between BTZ and control in ZT6 is now deemed to be even more significant, going down to adjusted p=0.0007.

*S4e? true regression lines? *

The same method was used as in Figure 1. The fit lines are produced by statistical comparison of fits, i.e. our hypothesis (damped cosine fit) vs null hypothesis (no change over time, linear fit), using sum-of-squares F test. The statistically preferred fit is plotted and p-value displayed on the graph. These details are reported in the figure legends and methods section.

While I thought these experiments were effective, they did not tie back well to the rest of the paper. What are the consequences of a temporally sensitive ISR? Which pathways does it effect in circadian time? Here, the main holes in this study are somewhat exposed; namely, a lack of mechanistic depth in explaining the very fascinating, albeit mostly descriptive, findings. The implicit assumption made here is that aggregation is 'bad' but could the opposite be just as true? Taking these considerations in account would further strengthen the discussion.

The purpose of (former) Fig 5 was entirely to test the functional consequences and potential translational relevance of a daily rhythm in protein turnover. The mechanisms upstream and downstream of the ISR, and link with many diseases, are already quite well understood but we apologise that we did not draw more heavily on the prior literature to provide sufficient context for this experiment. Protein aggregation has long been associated with proteotoxic stress, and we do not assume it is good or bad, we simply use it as an additional validation of a temporally sensitive ISR. To correct this omission we have added the following to the results section before these experiments are introduced:

"Disruption of proteostasis and sensitivity to proteotoxic stress are strongly linked with a wide range of diseases (Wolff et al, 2014; Harper & Bennett, 2016; Labbadia & Morimoto, 2015; Hipp et al, 2019). Evidently, global protein translation, degradation and complex assembly are crucial processes for cellular proteostasis in general, so cyclic variation in these processes would be expected to have (patho)physiological consequences....

...Informed by our observations, we predicted that circadian rhythms of global protein turnover would have functional consequences for maintenance of proteostasis. Specifically, we expected that cells would be differentially sensitive to perturbation of proteostasis induced by proteasomal inhibition using small molecules such as MG132 and BTZ, depending on time-of-day."

Reviewer #2 (Significance (Required)):

This is a fascinating paper that addresses key questions in the circadian organization of the proteome. The paper's main findings are that rhythms of protein synthesis and degradation are temporally coordinated to maintain overall stability of the proteome in mouse fibroblasts. Furthermore, the authors present evidence that this temporal organization may be important for assembly of macromolecular complexes. While very interesting, the main limitations are a lack of biochemical and mechanistic explanation and evidence that verifies these, mostly descriptive, findings.

The fundamental biochemical mechanisms of protein synthesis, degradation, protein quality control and stress response have been studied for decades and are increasingly well understood, at least in cultured cancer cells. What is not understood is the extent to which all of these essential cellular systems are subject to physiological variation over the circadian cycle in quiescent cells. This is the fundamental knowledge gap our study attempts to fill by testing the discrete hypotheses that (1) circadian regulation of macromolecular complex turnover is more prevalent than abundance and that (2) proteome renewal is more prevalent than compositional variation. We suggest that establishing these essential principles of circadian cellular physiology is an essential prerequisite for performing the type perturbational experiments we presume the reviewer would prefer. We would like to reassure the reviewer that such studies have been and are being performed, but we are concerned that the inclusion of a very extensive additional body of work within this manuscript would detract from the clear communication of our major finding that complex turnover and proteome renewal has a cell-autonomous basis.

*There are some relatively minor statistical and data quality issues that are probably addressable relatively quickly.

**Upon revision the study would be a welcome addition to investigators interested in proteostasis, circadian biology, cell biology and proteomics.

**I am a physician-scientist with expertise in circadian rhythms, cell biology, protein synthesis, and biochemistry.

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

**Seinkmane et al investigate circadian regulation of protein synthesis and degradation in cultured cells and in mice. Their main new finding is that protein synthesis and degradation are in many cases rhythmic but coordinated such that the proteome is rhythmically renewed without an apparent rhythm in total protein abundance. Particularly the pool of large protein complexes is rhythmically renewed in this fashion.

Using pulsed SILAC in combination with mass spectrometry, the authors are able to distinguish between total and newly synthesized protein levels in mouse lung fibroblasts. Analysis of these data shows that the synthesis of a large number of proteins is rhythmic although the total amount is constant, or that proteins are synthesized at a constant rate but the total amount is rhythmic, suggesting that degradation is rhythmic. By analyzing macromolecular complexes, defined as a high-speed pellet, they also present evidence that the rhythmic components of large complexes oscillate in the same phase and have a similar protein turnover rate. The authors conclude that complexes assemble rhythmically. **The authors also present evidence that the activity of the proteasome oscillates in a circadian manner. Based on this observation, they show (in fibroblasts and in mice) that the response to proteotoxic stress (monitored by eIF2alpha phosphorylation levels, protein aggregation, and apoptosis) is higher at circadian times of high proteasome activity.

**I am an expert in the circadian field, and the hypothesis and concept behind the work presented here are potentially very interesting, and the experimental design is in principle suitable to answer these questions. However, after reading the paper several times, I cannot find the set of experiments that would convincingly support the authors' conclusions.

**Major questions/points:

*The major limitation of the manuscript is that the conclusions rely heavily on statistical analysis and massive processing of data from a bewilderingly large number of very different experiments. In looking at the figures, I have often wondered if the presence or absence of a rhythm is real or a product of the heavily processed data. The fact that a cosine wave fits through data points better than a straight line does not necessarily mean that a circadian rhythm is present.

We agree that comparison of fits alone does not provide sufficiently reliable evidence. However, the fact that many independent methods (cosinor, RAIN, ANOVA) yield similar overall findings lends more confidence to our findings. We would also argue that the large number of different experiments is a positive aspect of the paper and lends weight to the general conclusions. We instead ask the reviewer to consider an alternative question - we and many other labs have found no evidence for any change in total cellular protein content, and yet there is extensive evidence from independent labs for a 'translational rush hour' whilst (excepting some low abundance transcription factors) very few cellular proteins change by more than 10% over the circadian cycle (see Stangherlin et al, COISB, 2022 for extended discussion of this). We hypothesised a parsimonious explanation for this clear contradiction, and designed experiments whose data were analysed by widely used methods that yielded results that were consistent with prediction. Perhaps the reviewer will at least concede that, if the presented findings do not refute the hypothesis, it should not be rejected until a superior one is proposed?

* I think that in particular, the SILAC experiment(s) should be repeated and also performed with an arrhythmic control (such as CRY1/2 KO). *

Whilst we agree that CRY1/2 KO cells show no circadian regulation of transcription and much more variable rhythms in PER2::LUC activity than wild type controls (Putker et al., EMBO J, 2021), in our hands circadian rhythms in proteome composition and protein phosphorylation in CRY1/2 KO are at least as prevalent as in wild type cells (see Wong et al., EMBO J, 2022). Indeed, when we performed a proteasome activity assay in CRY1/2 KO fibroblasts, we observed there was an apparent circadian variation, similar to WT but with a different phase. These data are now presented in revised Figure S1. Similarly, Lipton et al (Cell, 2015) showed circadian translational rhythms in cultured Bmal1 KO cells (see final figure), therefore it is not clear what would constitute an appropriate 'arrhythmic' control.

In this study, for proteomics experiments, we used a combination of SILAC and TMT, as each technique alone would not be sufficient to answer our specific questions. These two techniques are very resource-intensive on their own, and even more so in combination. We therefore had to prioritise and for the second SILAC-TMT experiment decided to focus on cellular fractionation and questions pertaining macromolecular complexes, which were directly relevant to our hypothesis. While it would undoubtedly also be interesting to study how canonical clock genes, such as Cry1/2, impact turnover on a proteome-wide scale, the focus of our study is physiological regulation of proteome composition, rather than the function of Cryptochrome genes which we already explored in previous work (Putker et al., EMBO J, 2021; Wong et al., EMBO J, 2022).

Comparability between the whole cell and MMC SILAC experiments is also limited due to the different experimental conditions (6h vs. 1.5h pulse, +booster).

We do not make any direct comparisons, other than to report that broadly comparable numbers of proteins were detected. Implicitly this means there must be greater coverage of protein complexes in the second pSILAC experiment, which our data bears out. If we were not to report the first experiment, the reader would not understand why we refined the method used in the second. In reporting the results of the 6h pulse, we make the limitations of this experiment very clear i.e. biased towards highly abundant, highly turnover proteins, irrespective of cellular compartment. We should add that even in this experiment there was a clear trend towards rhythmic turnover of ribosomal proteins, but this did not quite achieve significance (p = 0.07) and so we did not want to make claims beyond the data.

*The essential and new message of the paper is that (at least some) macromolecular complexes undergo circadian renewal (degradation and synthesis). Rather than just analysing an operationally defined pellet fraction by mass spectrometry, this could be shown in more detail and directly for one or two specific macromolecular complexes. Ribosomes, for example, seem particularly suitable, because there would also be the very simple approach of measuring the synthesis of ribosomal RNA by pulse labelling. To me, such an analysis would be perfectly sufficient as a proof of principle. I would then omit aspects such as rhythmic stress response, since many additional experiments are needed to demonstrate this convincingly. *

Thank you for the excellent suggestion, we agree that validation is important. The ribosome is by far the most abundant macromolecular complex in the cell and was one of the major complexes to show clear evidence for circadian regulation of turnover, but not abundance, by our pSILAC proteomics. To validate this result, we took advantage of two important observations: (1) that all fully assembled ribosomes incorporate ribosomal RNA (rRNA) which can readily be separated from other cellular RNA by density gradient centrifugation; (2) pulse-labelling with heavy uridine-15N2 allows nascent RNA to be distinguished from pre-existing RNA. Thus, combining stable isotope labelling with ribosome purification, we can distinguish nascently assembled ribosomes from total ribosomes when the RNA is extracted, digested with RNAse, and the ratio of light to heavy UMP quantified by mass spectrometry. These data are presented in new figure 5, and are consistent with findings in Figures 3/4 that circadian regulation of ribosome turnover is prevalent over abundance, and that the phase of highest ribosome turnover coincides with the phases of high translation and turnover overall. We hope by addressing the reviewer's question by an entirely orthogonal method, he/she can share more confidence in our conclusions.

The final figure is included because it tests predictions that were informed by the preceding experiments. It is not intended to be comprehensive exploration of how the integrated stress response changes with the circadian cycle, nor have we claimed this.

* Specific points: The reader is strongly influenced by the cosine wave or straight lines in the graphs (e.g. 1c, e, 3h, 5b, etc) produced by the analysis of rhythmicity, which basically only gives a yes or no answer. But it is not really that simple. If the algorithm detects a rhythm what is its period? Is it the same as the period of the luciferase reporter? If the period lengths correlate, do the phases as well (e.g. see differences in phases 1c and e)? These questions are not addressed. *

The temporal resolution of the time course data is much lower than the luciferase reporter and so the error of the fit is greater (usually 1-2h). For the cosine wave curve fit and the associated extra sum-of-squares F test, the period of the oscillation was fixed at either 24h or 25h, as determined from a parallel PER2::LUC control recording. This is now explicitly stated in the methods section

In terms of phase, the general trend across all experiments is that bulk protein turnover, synthesis and degradation is higher during the 6-8h following the peak of PER2::LUC than at any other point in the circadian cycle. This is also consistent with our previous findings in mouse and human cells (Feeney et al, Nature, 2016; Stangherlin et al., Nat Comms, 2021) as well as findings from many different labs in vivo (e.g. Janich et al., Genome Res, 2016; Atger et al., 2015, PNAS; Sinturel et al., 2017, Cell). We are cautious about trying to be any more specific than this because each assay is measuring something different, and (as can be seen across the figures) there is also some modest variation in the phase of PER2::LUC between experiments, with respect the prior entraining temperature cycle (this will be reported in our forthcoming publication, Rzechorzek et al, in prep). To address the reviewer's point therefore, we have added the following to the discussion:

"Across all experiments in this study, we find that protein synthesis, degradation and turnover is highest during the 6-8h that follow maximal production of the clock protein PER2. This is coincident with increased glycolytic flux and respiration (Putker et al, 2018), increased macromolecular crowding in the cytoplasm, decreased intracellular K+ concentration and increased mTORC activity (Feeney et al, 2016a; Stangherlin et al, 2021b; Wong et al, 2022)."

* **The algorithm in Fig 1c predicts a rhythm for the chymotrypsin-like and the trypsin-like but not for the caspase-like activity. The peptide assay measures core proteasome activity independent of ubiquitylation and should therefore be dependent on proteasome concentration in the sample. How can then only two of the three proteasomal activities be rhythmic? Please elaborate and repeat with arrhythmic cells (e.g. CRY1/2 KO). The period length does not seem to correlate with the one of the reporter. Why is that? *

The arrhythmic controls idea is partially addressed in the response above. We did perform a proteasome activity assay in CRY1/2 KO fibroblasts, and observed daily variation similar to WT, albeit with a different apparent phase. These data are now shown in Figure S1, and referred to in the main text as follows:

"Moreover, we detected a significant interaction between genotype and biological time when comparing trypsin-like proteasome activity between wild type and Cryptochrome1/2-deficient cells, that lack canonical circadian transcriptional feedback repression (Fig S1B-E)".

Besides this study, our two previous proteomic investigations of the fibroblast circadian proteome detected no biologically significant or consistent rhythm in proteasome subunit abundance (Wong et al., EMBO J, 2021; Hoyle et al., Science Translational Medicine, 2017). Moreover, proteasomes are long-lived stable complexes whose activity is determined by a combination of substrate-level, allosteric and post-translational regulatory mechanisms that includes their reversible sequestration into storage granules (Albert et al., PNAS, 2020; , Fu et al., PNAS, 2021; Yasuda et al., Nature, 2020). It is therefore very likely that the observed rhythm in trypsin- and chymotrypsin-like activity occurs post-translationally. Proteasome subunit composition is also known to change, which might be another reason for differences between the protease activities (Marshall and Vierstra, Front Mol Biosci, 2019; Zheng et al., J Neurochem, 2012).

To communicate this succinctly, we have revised the relevant text as follows:

Page 7: "Moreover, we detected a significant interaction between genotype and biological time when comparing trypsin-like proteasome activity between wild type and Cryptochrome1/2-deficient cells, that lack canonical circadian transcriptional feedback repression (Fig S1B, (Wong et al, 2022)). Previous proteomics studies under similar conditions have revealed minimal circadian variation in proteasome subunit abundance (Wong et al, 2022), suggesting that proteasome activity rhythmicity, and therefore rhythms in UPS-mediated protein degradation, are regulated post-translationally (Marshall & Vierstra, 2019; Hansen et al, 2021)."

Regarding period length, we apologise for an oversight in Fig 1c: unlike all other experiments presented here, these fits were originally done with a flexible period length (between 20h and 36h). This has now been re-fitted in a similar manner to the other experiments (fixed period of 24h, same as the parallel PER2::LUC controls), and the updated data are presented. This has not influenced the results of the statistical tests (only changed the p-values slightly, but the significance levels remain the same).

Fig. 1a,b suggest that there is a rhythm in global protein synthesis with a significant peak at 40h. Yet, Fig. 1e suggests otherwise. How can that be? Also, the degradation graph (lower panel 1c) has to be plotted with the ratios calculated from the data points and not the heavily processed fitted graphs. This can be very misleading.

Fig1a,b was performed under quite different conditions to 1e. As described in the methods section, 35S-labelling experiments require a medium change during both pulse and chase (to replace normal Met with radioactive Met, and vice versa). To avoid growth factor/mTORC1-mediated stimulation of protein synthesis & turnover, these acute media changes must occur in the absence of serum; otherwise media changes would introduce artifacts. In contrast, puromycin labelling (Fig 1e) is performed without any media changes (as puromycin can be added directly to culture cell media), and therefore was performed in normal culture conditions of 10% serum. Thus, due to its well-established effect of growth factor/mTORC1 signalling on bulk translation rate, it is very likely that differences in the phase of translational rhythms between Fig1a,b and 1e are attributable to differing serum concentrations – this phenomenon of serum-dependency of phase is also described in Beale et al, 2023, bioRxiv https://doi.org/10.1101/2023.06.22.546020. The only important point, is that neither of these proof-of-principle experiments support the null hypothesis: that translation rate and turnover remains constant over the circadian cycle. Thus, the hypothesis being tested in Figure 1 is not rejected, and provides the rationale for the subsequent proteome-wide analyses.

With respect to 1E, given the variance of measurement, the curve fits to Puro and Puro+BTZ already serve to test whether there is any significant ~24h component, a ratio of the respective data points would simply compound the error of measurement. The degradation plot is provided purely for illustrative purposes to help the reader i.e. if these fits were true, what would be expected? We have revised the figure to more clearly communicate that the degradation plot is presented purely as a visual aid, labelled “inferred”, and now show ratio plots in revised Figure 1.

* **It also strikes me as odd that the amplitude of degradation increases (peak at 28h lower than at 30h) while the amplitude of the core clock oscillation dampens over time (peak at 54h higher than at 53h due to desynchronisation. Only two data values around 54h are responsible for the detected rhythm (2nd peak). Furthermore, phase and period do not agree with the rhythm of proteolytic activities shown in 1c. How can this be explained? *

Due to the nature of the experiment, the degradation rate inferred from Figure 1B & 1E does not reflect proteasome activity exclusively. Rather it reflects the combined sum of processes that remove nascently produced proteins from the cell's digitonin-soluble fraction, which includes proteasomal degradation, but also autophagy, protein secretion and sequestration into other compartments. Therefore, the peak degradation in Fig 1B & E would not necessarily be expected to coincide with the peak of proteasome activity in Fig 1C. Again, these experiments in Figure 1 simply serve to test the hypothesis (change over circadian cycle) vs the null hypothesis (no change over the circadian cycle).

To the question of amplitude increase, we speculate that this is due to metabolic changes in cultures over the course of three days – as serum and nutrients from the last medium change at T0 are depleted, cells need to increase degradation to promote turnover and recycling. As we suggest that the rhythms in turnover help cellular bioenergetic efficiency, it is quite plausible that amplitude increases as nutrient-concentrations fall. We are in process of further investigation into how exactly these rhythms vary with nutrient and serum status.i

* Regarding the MS data shown in Figure 2, is it possible to show a positive / quality control? Best would be MS data of Luciferase (or PER2,3, RevErb/alpha, DBP) to show oscillation of protein levels with the same phase and period as the reporter. *

Unfortunately, none of these low abundance transcription factors were detected in our MS runs. This is not surprising, given that their copy numbers are estimated at * In Fig. 2c examples of the 4 groups of proteins presented in 2e should be shown (both synthesis and total abundance arrhythmic, either one rhythmic or both rhythmic) and not just what appears to be random examples of rhythmic and arrhythmic proteins. *

As also requested by another reviewer, we have revised the figure to include examples of each of the rhythmicity categories. No specific meaning is inferred from the chosen protein identities.

Is it possible at all to distinguish between synthesis/turnover and assembly/disassembly of macromolecular complexes in the MMC SILAC experiment? If so, how?

We followed the established protocol originally developed in our collaborator Kathryn Lilley's lab, where it has previously been shown that most proteins in the MMC fraction are in macromolecular assemblies (Geladaki et al, Nat Commun, 2019). Proteins that are rhythmically abundant in this fraction, but without an accompanying synthesis rhythm (e.g. Beta-actin, see Hoyle et al., Sci Trans Medicine, 2017) can be reliably assumed to arise solely from rhythmic assembly/disassembly i.e. they are captured in this fraction when assembled, but lost, and therefore not detected, in this fraction when disassembled. However, in the case of rhythmic synthesis and abundance, it is not possible with this technique to directly infer that rhythmic synthesis of a given protein is responsible for its rhythmic assembly in a complex, though they do correlate.

Therefore, our new figure 5 (with thanks again for this suggestion) approaches this by an orthogonal method, relying on the important observations that a) ribosomes incorporate ribosomal RNA (rRNA) b) this can be readily separated from most other cellular RNA by density gradient centrifugation and c) pulse-labelling with heavy uridine-15N2 allows nascent RNA to be distinguished from pre-existing RNA. Using this technique, we validate a rhythm in production and assembly of mature ribosomes, with its peak consistent with the highest turnover time as measured in Figs 1 and 3, and MMC fraction proteomics (Supplemental table 3), at the descending phase of PER2::LUC.

* **Looking at Fig. 4b,c, what is the fraction of rhythmic proteins from the MMC experiment that also oscillate in either synthesis, total abundance or both in the whole cell? Is there a general correlation at all? Please show. *

There were no correlations greater than would be expected by chance (the sets of proteins rhythmic in either synthesis or degradation did not overlap significantly between whole-cell and MMC fractions, as determined by an odds ratio test).

To communicate this we have added the following text:

"It is also worth noting that although there were small sets of proteins that were rhythmic in both whole-cell (Figure 2) and MMC fractions (Figure 3), in both synthesis and total abundance, none of these four overlaps were higher than would have been expected by chance."

* **Why is the phase of the oscillating proteins different in the two experiments (compare Figs. 2f,g and 4a) and does either of them match with the phase of the PER2::LUC reporter, which should be the peak synthesis phase of the clock? *

This was a labelling error on our part, our apologies and thanks for drawing it to our attention. We had attempted to harmonise all these phase values so that they were mutually comparable between the two mass spec experiments, but omitted to update all the figures. They have now all been updated to be inter-consistent. From our experiments, the peak of PER2::LUC consistently precedes the timing of maximum bulk translation. This phase difference is, at least in part, attributable to the inactivation kinetics of firefly luciferase (see Feeney et al., J Biol Rhythms, 2016), i.e., under conditions of saturating luciferin substrate, PER2 protein abundance peaks several hours later than PER2::LUC activity when measured in longitudinal live cell assays.

* Regarding the sensitivity to MG132 in Fig. 5b it doesn't make sense that, while eIF2alpha phosphorylation is arrhythmic in untreated cells and the levels of eIF2alpha phosphorylation are (apparently) not exhibiting a rhythmic change by administration of MG132 at different circadian timepoints, the ratio of P-eIF2alpha with and without MG132 suddenly is. Please show in Fig. S4b quantifications of the individual experiments with and without MG132. What is presented in 5b is after all the ratio of ratios of quantifications of Western blots, each of which individually does not display any appreciable rhythm. For me this is two much of processing of data. In my opinion, the MG132 4h acute treatment must show a detectable rhythm.*

We apologise for being unclear in this panel and description. Our hypothesis concerned the fold-induction of the p-eIF2alpha:eIF2alpha ratio changing as a function of MG132 and time. Our reasoning being that the ratio may be more biologically-relevant as it is the relative change that cells sense and respond to, and not the absolute abundance of p-eIF2alpha. We applied a quantitative, two-channel fluorescent antibody technique to enable detection and quantification of p-eIF2alpha and eIF2alpha from each replicate at each time point from the same band of the same blot. We agree that no p-eIF2alpha rhythm is evident from a cursory inspection of any of the blots. This is due to the innate variance between dishes in extracted protein concentration, as well as the levels of basal eIF2alpha and its phosphorylation, and is the reason that we took great pains to be as quantitative as possible using the two-channel immuno-detection (LICOR). Due to the natural and stochastic variation in eIF2alpha levels and extraction between replicates and over time, it is difficult to get identical eIF2alpha loading to reveal the overlying rhythm in p-eIF2alpha, and furthermore, identical loading would give a misleading impression of the level of temporal variation of eIF2alpha levels. Quantification reveals temporal variation in the MG132 treated samples but not in the untreated controls (Supp Fig 5A) – suggesting that there may be circadian regulation of the cellular response to MG132 challenge, rather than a cell-autonomous p-eIF2alpha rhythm under basal conditions. We quantified fold-induction from MG132 vs untreated to present in Figure 6A. We have presented all the raw data in supplementary figure 5 for readers to validate through their own analysis.

*Minor:

In Fig. 1f please show dot blot with error bars as well as the individual experiments in the supplementals. Please check the graph legend (N>=3?) *

Thank you for pointing out these omissions. The dot blot with error bars is now shown in Fig. 1F, and the full gels are now included as Fig. S2B. The main figure legend for 1f has also had the following added (explaining the N numbers):s

"Four mice were used per condition, but in some cases one of the four injections were not successful i.e. no puromycin labelling was observed and so no quantification could be performed (full data in Fig. S2B)."

* Please explain the mechanism of the "booster" used in the second SILAC experiment. *

The following has been revised in the text:

" Namely, we added a so-called booster channel: an additional fully heavy-labelled cell sample within a TMT mixture (Klann et al, 2020). When the mixture is analysed by MS, heavy peptides from the booster channel increase the overall signal of all identical heavy peptides at MS1 level; at MS2 and MS3 this results in improved detection of heavy proteins in the other TMT channels of interest, and is particularly advantageous for the proteins with lower turnover that would fall below the MS1 detection limit without the booster."

*

**p10 3rd paragraph: S2e not S3e *

Thank you, this has been fixed.

p12 last paragraph please add reference to Figs. 5f,g

Thank you, this has been added.

*Reviewer #3 (Significance (Required)): *

xxxxx

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Referee #3

Evidence, reproducibility and clarity

Seinkmane et al investigate circadian regulation of protein synthesis and degradation in cultured cells and in mice. Their main new finding is that protein synthesis and degradation are in many cases rhythmic but coordinated such that the proteome is rhythmically renewed without an apparent rhythm in total protein abundance. Particularly the pool of large protein complexes is rhythmically renewed in this fashion.

Using pulsed SILAC in combination with mass spectrometry, the authors are able to distinguish between total and newly synthesized protein levels in mouse lung fibroblasts. Analysis of these data shows that the synthesis of a large number of proteins is rhythmic although the total amount is constant, or that proteins are synthesized at a constant rate but the total amount is rhythmic, suggesting that degradation is rhythmic. By analyzing macromolecular complexes, defined as a high-speed pellet, they also present evidence that the rhythmic components of large complexes oscillate in the same phase and have a similar protein turnover rate. The authors conclude that complexes assemble rhythmically. The authors also present evidence that the activity of the proteasome oscillates in a circadian manner. Based on this observation, they show (in fibroblasts and in mice) that the response to proteotoxic stress (monitored by eIF2alpha phosphorylation levels, protein aggregation, and apoptosis) is higher at circadian times of high proteasome activity.

I am an expert in the circadian field, and the hypothesis and concept behind the work presented here are potentially very interesting, and the experimental design is in principle suitable to answer these questions. However, after reading the paper several times, I cannot find the set of experiments that would convincingly support the authors' conclusions.

Major questions/points:

The major limitation of the manuscript is that the conclusions rely heavily on statistical analysis and massive processing of data from a bewilderingly large number of very different experiments. The critical experiments lack replicates and obvious controls. In looking at the figures, I have often wondered if the presence or absence of a rhythm is real or a product of the heavily processed data. The fact that a cosine wave fits through data points better than a straight line does not necessarily mean that a circadian rhythm is present. I think that in particular, the SILAC experiment(s) should be repeated and also performed with an arrhythmic control (such as CRY1/2 KO). Comparability between the whole cell and MMC SILAC experiments is also limited due to the different experimental conditions (6h vs. 1.5h pulse, +booster). The essential and new message of the paper is that (at least some) macromolecular complexes undergo circadian renewal (degradation and synthesis). Rather than just analysing an operationally defined pellet fraction by mass spectrometry, this could be shown in more detail and directly for one or two specific macromolecular complexes. Ribosomes, for example, seem particularly suitable, because there would also be the very simple approach of measuring the synthesis of ribosomal RNA by pulse labelling. To me, such an analysis would be perfectly sufficient as a proof of principle. I would then omit aspects such as rhythmic stress response, since many additional experiments are needed to demonstrate this convincingly.

Specific points:

The reader is strongly influenced by the cosine wave or straight lines in the graphs (e.g. 1c, e, 3h, 5b, etc) produced by the analysis of rhythmicity, which basically only gives a yes or no answer. But it is not really that simple. If the algorithm detects a rhythm what is its period? Is it the same as the period of the luciferase reporter? If the period lengths correlate, do the phases as well (e.g. see differences in phases 1c and e)? These questions are not addressed.

The algorithm in Fig 1c predicts a rhythm for the chymotrypsin-like and the trypsin-like but not for the caspase-like activity. The peptide assay measures core proteasome activity independent of ubiquitylation and should therefore be dependent on proteasome concentration in the sample. How can then only two of the three proteasomal activities be rhythmic? Please elaborate and repeat with arrhythmic cells (e.g. CRY1/2 KO). The period length does not seem to correlate with the one of the reporter. Why is that?

Fig. 1a,b suggest that there is a rhythm in global protein synthesis with a significant peak at 40h. Yet, Fig. 1e suggests otherwise. How can that be? Also, the degradation graph (lower panel 1c) has to be plotted with the ratios calculated from the data points and not the heavily processed fitted graphs. This can be very misleading. It also strikes me as odd that the amplitude of degradation increases (peak at 28h lower than at 30h) while the amplitude of the core clock oscillation dampens over time (peak at 54h higher than at 53h due to desynchronisation. Only two data values around 54h are responsible for the detected rhythm (2nd peak). Furthermore, phase and period do not agree with the rhythm of proteolytic activities shown in 1c. How can this be explained?

Regarding the MS data shown in Figure 2, is it possible to show a positive / quality control? Best would be MS data of Luciferase (or PER2,3, RevErb/alpha, DBP) to show oscillation of protein levels with the same phase and period as the reporter. In Fig. 2c examples of the 4 groups of proteins presented in 2e should be shown (both synthesis and total abundance arrhythmic, either one rhythmic or both rhythmic) and not just what appears to be random examples of rhythmic and arrhythmic proteins.

Is it possible at all to distinguish between synthesis/turnover and assembly/disassembly of macromolecular complexes in the MMC SILAC experiment? If so, how? Looking at Fig. 4b,c, what is the fraction of rhythmic proteins from the MMC experiment that also oscillate in either synthesis, total abundance or both in the whole cell? Is there a general correlation at all? Please show.

Why is the phase of the oscillating proteins different in the two experiments (compare Figs. 2f,g and 4a) and does either of them match with the phase of the PER2::LUC reporter, which should be the peak synthesis phase of the clock?

Regarding the sensitivity to MG132 in Fig. 5b it doesn't make sense that, while eIF2alpha phosphorylation is arrhythmic in untreated cells and the levels of eIF2alpha phosphorylation are (apparently) not exhibiting a rhythmic change by administration of MG132 at different circadian timepoints, the ratio of P-eIF2alpha with and without MG132 suddenly is. Please show in Fig. S4b quantifications of the individual experiments with and without MG132. What is presented in 5b is after all the ratio of ratios of quantifications of Western blots, each of which individually does not display any appreciable rhythm. For me this is two much of processing of data. In my opinion, the MG132 4h acute treatment must show a detectable rhythm.

Minor:

In Fig. 1f please show dot blot with error bars as well as the individual experiments in the supplementals. Please check the graph legend (N>=3?)

Please explain the mechanism of the "booster" used in the second SILAC experiment.

p10 3rd paragraph: S2e not S3e

p12 last paragraph please add reference to Figs. 5f,g

Significance

xxxxx

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Referee #2

Evidence, reproducibility and clarity

Summary:

This is a very interesting and well written paper that addresses key questions in the circadian organization of proteostasis. The paper investigates origins of cellular circadian rhythms, invoking a premise early that there is a poor correlation between rhythmic gene expression - regulated by the canonical TTFL - and rhythms of the proteome, which are rather meager. Specifically, they ask how a relatively stable proteome is possible if cells engage in rhythms of cellular protein synthesis? Their hypothesis is that protein degradation must rhythmically compensate for rhythms of synthesis and much of the manuscript is focused on defining the relationship between rhythmic global synthesis and rhythmic degradation. They employ a series of detailed proteomic investigations and biochemical assessments of protein synthesis coupled with various circadian reporters to assess proteosome function. The proteomic experiments reveal a limited number of proteins with oscillations in either synthesis or abundance or both and no discernible pathway organization however, a followup and more refined study that utilized fractionated samples and boosted heavy SILAC identified strikingly, that many proteins in relatively heavy fractions are rhythmic and that these fall into possible complexes including ribosome and chaperonins. Finally, they perform in vivo experiments testing whether the timing of proteotoxic stimuli regulates the degree of the integrated stress response measured as pEif2a.

Overall, I think that this is a fascinating paper that addresses and important question but falls short on mechanistically unifying them and completely contextualizing the findings in light of the canonical modes of circadian timekeeping leaving us with an important, but mostly descriptive set of findings. In addition, there are a number of important questions about data interpretation, some issues with data quality that should be addressed outlined below. With revision and further explication, this study will be an excellent addition to the growing field of circadian organization of the cellular proteome.

Major and minor Comments.

Figure 1.

Fig 1a. The difference in Pulse and Chase at ZT24 does not appear to reflect the quantified data in 1b. This should be reconciled to make the figure convincing. How was the timing of the chase collection determined? Fig 1d-e. What is the evidence that puro labeling results in 'rapid' turnover. Fig 1e seems to be missing the data from the treated and untreated conditions? How are the lines produced (e.g. linear versus rhythmic? Are these drawn lines or actual regressions?). Why was 30 minutes chosen as labeling time? It seems hard to understand here how protein degradation kinetics can be measured by puromycin labeling if the authors' claim that puromycin labeling potentially changes degradation rates as a function - primary or secondary - of the labeling itself. It seems they are measuring the potential to degrade proteins. How do they determine that they are measuring degradation of functionally relevant proteins as opposed to a host of premature truncations? Fig 1e bottom - again is this a true regression line? Perhaps two time points should be examined here - similar to the pulse chase performed with 35S labeling? Fig 1f. It appears that Puro labeling results in a rhythm between ZT1 and ZT13 but no statistic is provided and appears that the 'ns' is the results of variance in the data as opposed to difference in means? - would this not contradict the cellular result? What accounts for the rhythm reversal in the presence/absence of BTZ.

While the authors have previously demonstrated an increase in rhythmicity of the proteome in Cry1/Cry2 double knockout cells, it would have been welcome here to test a global loss of circadian transcription in the degradation assay. One might expect that these rhythms would also be even higher. What I am really asking is: what is the mechanism for rhythmic degradation and is it dependent on the canonical clock?

Fig 2. How was the 'fixed window' timeframe determined?

Fig 3h. While admittedly difficult, the native PAGE is not of great quality and kind of unconvincing. Also not really sure why the AHA labeling is used here an nowhere else in the paper.

Fig 4. I was a little disappointed here that the authors did not directly assess macromolecular assembly of at least one of their "hits" and demonstrate functional relevance and most of the analysis is maintained at a very superficial, systemic level. STRING assemblies are not terribly helpful without clear k-means clustering or some other clearly visualizable metric for stratifying and organizing the putative PPI data - this figure (S3) could be markedly improved.

Is it possible that some macromolecular complexes have rhythms because their constituent proteins have differential half-lives when in one complex compared with another in circadian time? This possibility was not discussed.

Fig. 5.

Why is the first histogram in 3c not at unity? Do ZT24 and Zt48 differ, similarly do ZT36 and ZT60? Fig S4f is not of good quality with missing eIF2a total and therefore no loading controls. S4e? true regression lines?

While I thought these experiments were effective, they did not tie back well to the rest of the paper. What are the consequences of a temporally sensitive ISR? Which pathways does it effect in circadian time? Here, the main holes in this study are somewhat exposed; namely, a lack of mechanistic depth in explaining the very fascinating, albeit mostly descriptive, findings. The implicit assumption made here is that aggregation is 'bad' but could the opposite be just as true? Taking these considerations in account would further strengthen the discussion.

Significance

This is a fascinating paper that addresses key questions in the circadian organization of the proteome. The paper's main findings are that rhythms of protein synthesis and degradation are temporally coordinated to maintain overall stability of the proteome in mouse fibroblasts. Furthermore, the authors present evidence that this temporal organization may be important for assembly of macromolecular complexes. While very interesting, the main limitations are a lack of biochemical and mechanistic explanation and evidence that verifies these, mostly descriptive, findings.

There are some relatively minor statistical and data quality issues that are probably addressable relatively quickly.

Upon revision the study would be a welcome addition to investigators interested in proteostasis, circadian biology, cell biology and proteomics.

I am a physician-scientist with expertise in circadian rhythms, cell biology, protein synthesis, and biochemistry.

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Referee #1

Evidence, reproducibility and clarity

The manuscript "Circadian regulation of protein turnover and proteome renewal" investigates the role of protein degradation in the circadian control of proteostasis. The researchers suggest that the relatively static levels of protein levels in a cell are incongruent with the known oscillation in protein synthesis. They therefore hypothesize that there should be a compensatory mechanism to counteract rhythmic protein synthesis, rhythmic protein degradation. To investigate this, they employ bulk pulse chase labeling to study the process of degradation. They identify a synchronization between the creation and turnover of proteins in a cell, implying the clock helps to maintain homeostasis through a novel mechanism. They note that these phases align with energy availability, granting a plausible reasoning behind the biological implementation of this regulation. In summary, this is a sound manuscript that adds to the research field. The experiments in this manuscript are well thought out, organized, and explained. In general, the authors do not go further in their conclusions than I think is warranted given the data that they have, though I think that there are some key items that should be addressed before the publication of this manuscript.

Major notes:

1. In figure 1, a clearer idea of what the ** means would be appreciated. What was the standard of significance for this measure?
2. In Figure 1b, it is important to note clearly in the text that the this is not a direct measure of protein degradation, but a subtractive proxy. Though I don't think that necessarily makes the authors conclusions incorrect, the same result could also be obtained if an extra 15% of the proteins were moved into the insoluble fraction. This is the same for Figure 1E and F.
3. In figure 1c, is the noted oscillation in protease activity due to the oscillation of these proteins? What are the predicted mechanisms behind this? I don't think that this is necessarily within the scope of this paper but should be addressed in the discussion. Also, the peak degradation rate from Figure 1B is 4 hours before the peak enzyme activities. How can this observation be reconciled?
4. For the pSILAC analysis, the incorporation scheme has a six-hour window between the comparison of the light and heavy peptides. This makes it somewhat difficult to assess whether you are looking a clock effect from T1 or T1+6. This does not negate the findings, but it does question when the synthesis is occurring and what is being compared, which I think should be more clearly discussed in the manuscript. This is discussed later in the manuscript but should be mentioned in this section.
5. There are no error bars on figure 2C. What the pSILAC just done in a singlet? If so, the rhythms estimation is likely a large overestimate and should be noted.
6. Why were the genes selected in 2C? these are not discussed anywhere else in the manuscript.
7. The authors note that for Figure 2 "These observations are consistent with widespread rhythmic regulation of protein degradation." However, only 5-10% of the proteome is oscillating at any level and less with a discrepancy between synthesis and abundance, so "widespread" is an exaggeration and this statement should be limited to the degradation in the rhythmic proteome.
8. The authors note that their more developed strategy in figure 3 would allow for the detection of less abundant proteins. However, they do not discuss that they in fact found less proteins overall, or if they were able to detect proteins of lower abundance. This is of some concern in determining if this is indeed the better method that they predict. How can the authors reconcile this issue? How can they rationalize this explains their increase in oscillating elements?
9. In the comparison of complex turnover rates, the authors need to provide a metric that backs their statement that "the majority of component subunits not only showed similar average heavy to total protein ratios but also a similar change in synthesis over the daily cycle" for figure 3F.
10. In reference to the AHA incorporation, why is the hypothesis not that, like the puramycin, you would not see oscillation unless you add BTZ? Shouldn't the active degradation regulate the incorporation of AHA such that there is no visible rhythm unless you suppress degradation?
11. The authors claim that there is enrichment of the actin cytoskeleton, but where this data can be found should be explained. The only thing that is shown is a few selected graphs of proteins in this pathway.
12. The authors note an oscillation in the total levels of p-eif2, commenting that these do not arise from the rhythms in total eif2a but temperature and feeding rhythms. However, unless I misunderstood, this work was done in fibroblast cell culture, so in this case, where would these temperature and feeding rhythms come from?
13. In Figure 5d, the treatment impeding degradation is causing cell death while the inhibition of translation does not. However, wouldn't too much, or not enough, translation, without compensatory regulation from degradation cause a problem in the same way that degradation does?

Significance

The information that stems from this work is relevant and of interest to circadian clock field as how the regulation of the output of the circadian clock is implemented is still a major question in the field. This manuscript suggests a novel and plausible method for how, at least in part, this regulation occurs. However, the manuscript uses methods that do not measure degradation directly, which is a minor limitation. In addition, the mechanisms by which this regulation is imparted are not addressed in any meaningful way, even in the discussion.

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Referee #3

Evidence, reproducibility and clarity

Abe et al. generated multiple novel mouse model that follows and labels Col4a2 by fusing it with GFP. The creation of this mouse model allowed for the analysis of the basement membrane in real-time using live imaging of embryonic explant cultures. The combination of the mouse model with live imaging revealed new insights into how the basement membrane turnover occurs during early hair follicle development. After setting the stage the authors establish its utility with embryonic tissue, which revealed membrane buds that could be visualized with eGFP at different time intervals for 19h. The growth of the hair follicle bud during that time could be divided three distinct areas, the upper, lower stocks, and the tip. Where the tip and lower stalk increased in BM length, while the upper stalk decreased. BM length correlated with increased cellular replication. Using a double transgenic model system, they evaluated the differences between 'cell displacement', 'BM expansion', and 'cell autonomous movement'. Diving deeper with the Col4a2-mKiGR mouse model investigated Col4a2 turnover to reveal similar results mentioned above. Lastly MMP inhibitors were used to investigate how hair follicle growth is affected, which revealed inhibition of cellular replication and inhibition of Col4a2 turnover. These results inhibited hair follicle elongation which made the forming hair follicles thicker.

Overall, this is an interesting paper for hair follicle biologists since it investigates the early moments of the budding follicle in real time using a ex vivo culture model. In addition, there is additional appeal because the authors use live imaging the hair follicle neogenesis as a basement membrane model, which is interesting and novel. The manuscript is clearly written, and the data support the overall conclusions. My comments below are to help in clarity which may be used to develop clearer figures and additional text.

Major:

In Figure 2 for the cell displacement and expansion part. I found the figure and text confusing, particularly in regard to how the data shows the bleached edge of the BM moving alongside the cells. Could the authors make this clearer in the figure and in the writing of the text?

The authors created a Col4a2-mKikGR mouse line that is supposed to follow Col4a2 turnover. It is difficult to understand how the authors can claim that it was turnover with the explanation in the text of how the mouse model works. Could the authors write a better description of the mouse model in the text?

Significance

The strengths of the paper are the use of a novel mouse model that can track collagen (Col4a2) with a tagged GFP and the live imaging model system. This has led to a novel and important knowledge on the interplay between the BM and cells. The limitation of the manuscript is that the entire manuscript utilizes a single protocol (live imaging) to investigate BM dynamics. This might be due to the sophisticated nature of the model systems, but it is a limitation.

To my knowledge the study is novel because of the mouse model to track Col4a2 dynamics with GFP. This model led to some interesting findings about hair follicle development in that different regions expand differently with the BM. This is good foundational knowledge using the latest state of the art techniques in live imaging of embryonic tissue culture systems.

The audience that would be interested in this manuscript is broad, which would span cell and developmental biology but also specialists in membrane and protein biology that can finally see in real time the dynamics of Col4a2 building skin and hair.

My expertise in in hair follicle development and repair and stem cell biology.

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Referee #2

Evidence, reproducibility and clarity

The authors successfully generated a knock-in mouse line expressing fluorescence-tagged endogenous collagen IV. Homozygous mice exhibited normal survival with no apparent developmental abnormalities. Through imaging of the back skin of COL4A2-eGFP mice in ex vivo culture, the authors observed a faster expansion rate of the basement membrane (BM) at the growing tips of developing hair follicles, while the upper stalk region showed a slower BM expansion rate. Real-time imaging also revealed that the BM and basal epithelial cells moved in the same direction. Fluorescence recovery after photobleaching (FRAP) and the photoconvertible protein mKikGR experiments demonstrated a faster turnover rate of COL4A2 at the tips of the hair follicles. The authors used MMP inhibitors to suppress the recovery of COL4A2-eGFP, BM expansion, and observed abnormalities in the developmental process of hair follicle morphology. The findings are novel and interesting, some aspects of how the experiments and quantifications were conducted should be clarified to allow the readers to fully appreciate the results.

Major Comments:

1. BM Expansion Statistics: Regarding the statistical analysis of BM expansion, is the length of the BM affected by the z-axis plane at the time of imaging? How is it ensured that the BM length measured at different time points corresponds to the same z-axis?
2. Cell Movement Statistics (Figure 2): In the statistical analysis of cell movement in Figure 2, the lack of other references raises questions about ensuring that the cells measured at different time points are the same cells.
3. The authors concluded that the inhibition of MMP delayed the recovery of COL4A2-eGFP after photobleaching, indicating the crucial role of MMP activity in the incorporation of COL4A2 into the BM. Does MMP inhibition lead to a reduction in the synthesis of the COL4A2 protein, thereby delaying the recovery of COL4A2 in the BM?

Minor Comments:

In Figure 1D, the representative image and the statistical graph are inconsistent. For example, in the upper stalk region, all basal epithelial cells have Ki67 signals according to the representative image.

Significance

The authors successfully generated knock-in mice expressing fluorescence-tagged endogenous collagen IV. With this novel mouse model, researchers can directly observe the dynamic changes in the extracellular matrix of different organs in mammals during development and disease, revealing the potential roles of the extracellular matrix.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Wuergezhen et al. generated two fluorescently tagged Col4a2 mouse models, including EGFP-Col4a2 and the photoconvertible mKikGR-Col4a2. They showed that tagged collagen IV get incorporated in the basement membranes of various tissues in the developing and adult mice, and fully support embryonic development, fertility, and physiological functions. The authors followed up investigating Col4a2 dynamics during embryonic development of the hair follicle. Using FRAP, they showed that the basement membrane expands with a faster rate near the tip region. This coincided with faster turnover rates of Col4a2 at the tip relative to the lower and upper stalk. In addition, the authors demonstrated that Col4a2 turnover depends on MMPs.

Major comments:

• Are the key conclusions convincing?

The major conclusions of the manuscript are convincing. These include that tagging collagen IV does not compromise its function, differential expansion of the basement membrane, differential turnover of the Col4a2, the MMP dependence for normal basement membrane expansion and turnover. However, some claims detailed below need to be clarified or addressed to improve the manuscript. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

In Figure 2B-C, the authors conclude that basement membrane expands at different rates, depending on the region with higher expansion rates near the hair follicle tip. From their methods, they conducted repetitive photobleaching cycles every 2-3 hours to maintain the bleached status of ROIs and tracked changes in basement membrane length. However, it sounds challenging to repetitively photobleach the same ROI in a dynamically expanding tissue, which may compromise the accuracy of length measurements. It would be helpful if the authors could provide movies corresponding to these experiments for clarity. In addition, this repetitive bleaching should be highlighted in the figure and figure legend, as readers could get confused about why there is no recovery here when comparing to the FRAP experiment.

In Lines 180-198 and Figure 2F-H, the authors interpreted cell movement as contributed by cell-autonomous vs basement membrane expansion, which is speculative. Another possibility is that cell movement was all autonomous, while basement membrane expansion was caused by mechanical stretching that was in turn caused by cell proliferation. This conclusion should be rephrased.

Following MMPi treatment, the authors found that basement membrane expansion was halted (Figure 4C-D). Yet, they later showed that hair follicles widened under MMPi treatment (Figure 4E-J). Under these conditions, I would have expected such widening to be accompanied by basement membrane expansion at the lower or upper stalk, which is not the case, at least for the first 7 hours (Figure 4C-D). How do the authors interpret this? - 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.

Considering the rapid expansion of BM near the tips, I wonder whether the authors have explored possible structural differences of the basement membrane in different regions? Is the basement membrane near the tips thinner and/or does it have microperforations as reported in other systems? Looking into this may further support their observations, not only in control conditions but also in MMPi treated follicles. - 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, for possible structural changes, 3D rendering of fluorescence imaging as shown in Figure 1J may be sufficient.

Increasing sample number using existing mouse strains should also be feasible. It would take 2-3 weeks from setting up timed pregnant mice to imaging the embryonic skin explants. Adding image analysis and figure preparation, it should be doable within 1 month. - Are the data and the methods presented in such a way that they can be reproduced?

In Figure 2D/ Figure 5C, it is unclear how ROIs corresponding to tip/lower/upper stalk are being drawn for quantification of Ki67+ cells.

The images in 2B and 4C, 3A and 4E, are identical. Images should not be re-used in figures. This raised the concern that probably not sufficient samples were imaged to have different representative images. It should also be clarified where the data was re-used, for example, the control data in 2C and 4D, 3B and 4B. - Are the experiments adequately replicated and statistical analysis adequate?

A few experiments have low sample numbers while the data was quite variable. These include Figure 2G-H (n = 3 cells), Figure 3C (unknown sample number), Figure 4B (n = 3 hair follicles), Figure 5B (n = 3 hair follicles). More sample numbers (~10 total) should be included to solidify the findings.

For the mKikGR experiment in Figure 3C, quantification should be included. A ratiometric measurement of green/red fluorescence over time should be a good complementary way of demonstrating region-specific recovery.

In Figure 5B, the authors claim that the percentage of dividing cells in control follicles being different from that of MMPi-treated follicles. How are they extracting these percentages? From the plots, control and MMPi-treated columns do not appear to be normalized as 100% to make such comparisons. Moreover, having two mean+/-SD in each column makes these data confusing to interpret. The authors should consider replotting their data either by combining their data into a unique population per conditions and reporting the percentages, or alternatively, they may consider splitting each of these columns into two (i.e., dividing vs. non-dividing cells), and comparing both conditions as ratios of dividing versus/non-dividing cells.

Minor comments:

• Specific experimental issues that are easily addressable.

Already addressed above. - Are prior studies referenced appropriately?

I believe so. <br /> - Are the text and figures clear and accurate?

All plots measuring basement membrane length are labeled as 'increase in BM length', even when in some cases the BM length is reduced. The authors should consider relabeling these as 'BM length change' or something similar.

The second and third paragraphs of the discussion are too long and should be condensed into a single paragraph. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Use better color combination for visualization of multi-channel images. For instance, magenta/green is a better combination than red/green for the color blind. Color combinations are not consistent across figures in the manuscript.

Include movies for all data derived from live imaging.

Include statistical tests used for all plots, some are missing.

The authors should consider fitting their FRAP data in each condition and report percentages corresponding to the mobile and immobile fractions.

Examples of horizontal vs perpendicular cell division appear to be mislabeled in Video5.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
• The large molecular weight of extracellular proteins makes it challenging to generate genetically engineered versions of such proteins to investigate their function and dynamics in vivo. The present study has addressed such issues for Col4a2, a major component of the basement membrane. This study further provides insights towards the understanding of BM dynamics during embryonic organ development.
• Place the work in the context of the existing literature (provide references, where appropriate).
• Addressed above
• State what audience might be interested in and influenced by the reported findings.
• Cell and developmental biology, extracellular matrix biology, organ development and regeneration.
• 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.
• Tissue morphogenesis, extracellular matrix

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Referee #3

Evidence, reproducibility and clarity

This manuscript has potential interest as a preclinical study for glioblastoma treatment. There is a substantial amount of data that is promising, but there are numerous issues that will require additional experimental effort before publication.

Major concerns:

1. The title is overly general and uninformative. The authors should include the drug name (mubritinib) and the specific tumour type (glioblastoma).
2. The concept that mubritinib functions through metabolic effects is not surprising given recent publications (PMID: 37382244; PMID: 35429141; PMID: 33245718; PMID: 31287994) and that it impacts the blood-brain barrier (PMID: 36178590). However, there are limitations to the strength of this observation. Most of the experiments are associations between drug treatment and metabolic changes. The NDI1 partially rescue experiments in Figures 1h and 1i are nice but show that NDI1 expression itself increases OCR. This experiment is also performed over a very brief window of time. A better set of experiments would include measurement of cell number over a prolonged time course (Figure 2d has one time point) and to use a genetic targeting strategy against ETC complex 1.
3. The authors observe that EGFR expressing lines are more sensitive to mubritinib. As the rescue experiments are only partially effective and ERBB family members may be targeted by mubritinib, it is critical to address the effects of mubritinib on EGFR activation and perform rescue studies, as the application of mubritinib in patients may be guided by the EGFR mutational state.
4. The differences found with NSC responses is interesting but needs to be developed. Why are there differences in mubritinib responses? For example, do NSCs not require ETC complex 1 as much?
5. I would suggest that the authors also compare sensitivity of the BTSCs (I would suggest a change in nomenclature as these are only from GB) and differentiated tumour cells to determine if the stem cells have greater dependence. Please use similar culture conditions.
6. The differences in cell cycle are useful but the mechanism is lacking. The claim that self-renewal is drastically or markedly changed is overstated. The ELDAs are not striking. There is no evidence that stemness is a direct target.
7. The in vivo effects on cell biology need greater analysis in mechanism. I am also not sure why the authors switch lines tested in different assays.
8. The mechanism of interaction with radiation is not developed. What is happening here? Are there changes in DNA damage repair or simply growth? This is a nice observation that could be better developed.

Minor concerns:

1. Grammar needs attention.
2. Please remove the overuse of "strikingly", "drastically", "importantly", etc. Most of these descriptions are overstated.
3. The number of in vivo replicates needs to be addressed.
4. All gene expression data should be deposited. All raw data (numeric) should be made available.
5. Please replace all normalized data with raw data. The statistical testing was likely incorrectly performed, and this can give rise to false conclusions. I am particularly concerned about the normalization to cell numbers.

Significance

This manuscript has potential interest as a preclinical study for glioblastoma treatment. There is a substantial amount of data that is promising, but there are numerous issues that will require additional experimental effort before publication.

Major concerns:

1. The title is overly general and uninformative. The authors should include the drug name (mubritinib) and the specific tumour type (glioblastoma).
2. The concept that mubritinib functions through metabolic effects is not surprising given recent publications (PMID: 37382244; PMID: 35429141; PMID: 33245718; PMID: 31287994) and that it impacts the blood-brain barrier (PMID: 36178590). However, there are limitations to the strength of this observation. Most of the experiments are associations between drug treatment and metabolic changes. The NDI1 partially rescue experiments in Figures 1h and 1i are nice but show that NDI1 expression itself increases OCR. This experiment is also performed over a very brief window of time. A better set of experiments would include measurement of cell number over a prolonged time course (Figure 2d has one time point) and to use a genetic targeting strategy against ETC complex 1.
3. The authors observe that EGFR expressing lines are more sensitive to mubritinib. As the rescue experiments are only partially effective and ERBB family members may be targeted by mubritinib, it is critical to address the effects of mubritinib on EGFR activation and perform rescue studies, as the application of mubritinib in patients may be guided by the EGFR mutational state.
4. The differences found with NSC responses is interesting but needs to be developed. Why are there differences in mubritinib responses? For example, do NSCs not require ETC complex 1 as much?
5. I would suggest that the authors also compare sensitivity of the BTSCs (I would suggest a change in nomenclature as these are only from GB) and differentiated tumour cells to determine if the stem cells have greater dependence. Please use similar culture conditions.
6. The differences in cell cycle are useful but the mechanism is lacking. The claim that self-renewal is drastically or markedly changed is overstated. The ELDAs are not striking. There is no evidence that stemness is a direct target.
7. The in vivo effects on cell biology need greater analysis in mechanism. I am also not sure why the authors switch lines tested in different assays.
8. The mechanism of interaction with radiation is not developed. What is happening here? Are there changes in DNA damage repair or simply growth? This is a nice observation that could be better developed.

Minor concerns:

1. Grammar needs attention.
2. Please remove the overuse of "strikingly", "drastically", "importantly", etc. Most of these descriptions are overstated.
3. The number of in vivo replicates needs to be addressed.
4. All gene expression data should be deposited. All raw data (numeric) should be made available.
5. Please replace all normalized data with raw data. The statistical testing was likely incorrectly performed, and this can give rise to false conclusions. I am particularly concerned about the normalization to cell numbers.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript Burban et al explore the effect of the mitochondrial oxidative phosphorylation (OXPHOS) inhibitor Mubritinib on patient derived glioblastoma stem cells and murine xenografts. The authors first show that i) Mubritinib is an inhibitor of OXPHOS in brain tumor stem cells (BTSC), ii) that it impairs cell growth and self-renewal of patient-derived BTSC with different genetic background and iii) has an effect on the expression of genes related to stemness. In addition, the authors convincingly show that Mubritinib is a brain penetrant drug, and by transplanting luciferase expressing BTSC into the brain of immunodeficient mice they show it delays GB tumorigenesis and the animal lifespan (either alone, or more efficiently if combined with IR treatment). Finally, by performing toxicological and behavioral studies in mice models, Burban et al demonstrate that Mubritinib has a well-tolerated and safe profile and does not induce damage to healthy cells.

The manuscript is well written and organized and the data is clearly presented. The results are convincing, but a few additional experiments and controls would be beneficial to support the claims of the paper, most of which are easily addressable.

Main comments:

• Finding suitable control cells for BTSC experiments is a widely acknowledged challenge in the field. However, in line with other studies, it is recommended that the authors consider using a non-oncogenic NSC as control line to demonstrate that the effects reported in Figure 1 and Figure 2 are more pronounced in BTSC compared to NSC (as it was done in Suppl Fig3).
• Figure 5 presents a significant finding indicating that Mubritinib enhances the sensitivity of GB tumors to IR. Considering that Temozolomide (TMZ) is the primary chemotherapy drug for GB patients, it would be crucial to investigate the potential outcomes of a combined treatment involving Mubritinib and TMZ. This will help determine if the combination exhibits promising results, comparable to what is demonstrated in Figures 5d, 5g, and 5i for Mubritinib and IR. Such experiment would reinforce the drug's potential for clinical trials in GB treatment.

Minor comments:

• The authors should specify early in the paper what is the number of samples of patient-derived BTSC they use and the fact that their genetic mutations are known (this information is summarized in the supplemental table 1, but only reported later in the manuscript). This information is important and should be clearly stated at the beginning of the manuscript.
• In Figure 2a the inhibition at 20nM is significant but not very pronounced. Based on Figure 1 I would have expected to see a stronger effect at this concentration range. Can the authors comment/provide an explanation for this discrepancy?
• The EdU incorporation experiment presented in Figure2h-I should be repeat with lower concentrations of the drug (in most of the assays the effect of Mubritinib is detectable at much lower concentrations).
• Since the authors have done RNA-seq on the samples why don't they report the specific subtypes of their samples in the text and in Suppl Table 1 (Proneural, Neural, Classical or Mesenchymal) ? It is known that different molecular subtypes respond differently to treatments; therefore this information would be essential to understand if Mubritinib is effective on a wide range of GB subtypes.
• In Figure2b and Supplemental Figure1b-c : instead of correlating the effect with genetic mutations, it would be more relevant if the authors could correlate the data with the molecular subtypes inferred by RNA-seq (see my comment above)
• Regarding the RNA-seq experiment the authors should report what is the percentage (and numbers) of genes that change expression. Is there for example a preference for up- or down- regulation? It would be interesting to see a Gene Ontology (GO) analysis for the up-regulated genes versus a GO analysis of the down-regulated genes to confirm that the relevant categories show dysregulation as expected (e.g. enrichment for cell cycle and stemness genes in the down-regulated list, etc ).
• In Figure2 m-o the difference between CTL and Mubritinib treated cells do not seem substantial, although it is shown as statistically relevant. Can the authors specify the percentage to be able to better assess the differences?
• Add p-value for Figure3a-c
• In the western blot in Supplemental Figure 3b Vinculin shows twice
• Change" Given that Mubritinib is already completed a phase I clinical trial" into "...has completed..."

Referees cross-commenting

I agree with other reviewers that more data is needed to determine if mubritinib could be an effective treatment for various GB subtypes. The models used in this study do not encompass the full spectrum of GBM genetics. The authors should repreat the experiments using models that represent the major genetic/transcriptional subtypes of GBMs and clearly label and identify them in the study. Specifically, the authors should include models like 'classical/EGFR-amplified', 'mesenchymal', 'proneural/PDGFR amplified'. Alternatively, it is advisable to refrain from asserting that mubritinib is effective across genetic alterations in the manuscript.

Significance

Considering the limited effectiveness of existing treatments, it is crucial to explore alternative approaches to improve patient outcomes. This study demonstrates promising potential for the clinical translation of Mubritinib in GB treatment.

A major limitation of this study is the narrow numbers of patient-derived samples used and absence of a proper control cell line. Unfortunately, as evidenced by the existing literature in the field, selecting a control cell line for glioma stem cells research is challenging due to the unknown cell-of-origin for this type of tumor. In addition, all the toxicity/safety tests were performed in mice models and it is difficult to predict how this would translate into human patients. However, the fact that a phase I clinical trial has already been completed for Mubritinib (in the context of a different type of tumor) is encouraging.

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Referee #1

Evidence, reproducibility and clarity

The authors report the use of mubritinib, a drug targeting complex I of the mitochondrial electron transport chain, to halt the proliferation of brain tumor stem cells (BTSCs) isolated as neurospheres from glioblastomas. They demonstrate that mubritinib crosses the blood-brain barrier, and show that this drug delays GBM tumorigenesis and extends lifespan in mouse models that were generated by transplantation of human BTSCs or mouse cell lines. They also provide evidence that this potentially harmful drug is well-tolerated by mice.

The ability of mubritinib (initially conceived as a ERBB2 inhibitor) to block complex I of the electron transport chain was previously identified in acute myeloid leukemia, where this drug proved to selectively inhibit a subset of cases relying on oxidative phosphorylation (OXPHOS). However, the use of mubritinib is novel in GBM, a lethal malignancy for which a few therapeutic options are available, and no substantial progress has been reported since 2005. In addition, the authors show that accumulation of mubritinib in the brain tissue allows for the use of a reduced dose of mubritinib, thereby reducing the risk of the deleterious effects that blunt enthusiasms about targeting of mitochondrial respiration.

However, this manuscript presents significant weaknesses that are detailed below. In particular, the models used appear insufficient to support the conclusion, stated in the abstract, that the drug can be effective in GBMs with different oncogenic mutations. Based on the provided evidence, the claim that 'mubritinib potently impairs stemness and growth of patient-derived BTSCs harboring different oncogenic mutations' should be removed, or supported by using BTSCs that adequately represent the major GBM subtypes identified by genetic and transcriptional analysis. Specifically, BTSCs harboring EGFR amplification (displayed by 40% of GBMs) would need to be added. Equally, it is inappropriate to conclude (Discussion, page 14) that the models used, displaying EGFR mutations, are representative of widespread EGFR alterations: indeed the EGFR alteration observed in 40-50% of patients is EGFR amplification, whose pathogenic effects can not be recapitulated by the EGFR mutation harbored in the models used. If models harboring EGFR amplification are unavailable to these authors, making unrealistic to repeat the experiments in at least two different EGFR-amplified BTSCs in the timeframe allowed for revision, not only the claim that mubritinib inhibits BTSCs harboring different oncogenic mutations should be removed, but lack of experiments in EGFR-amplified BTSCs should be discussed as a limitation of this study. In addition, as detailed below, in vitro experiments should be expanded to corroborate mechanistic aspects of the drug, safety should be better demonstrated and some aspects of in vivo experiments should be clarified. Overall, the methodology seems sufficiently detailed to allow reproduction. The experiments are adequately repeated and the statistical analysis is appropriate, but in one case detailed below.

Major Point N.1

Figure 2a and 2c. Although statistically significant, the effect of mubritinib at 20 nM is biologically of limited significance in a subset of BTSCs, where the drug reduces viability by less than 25% (Fig. 2a). Therefore, the correlation between oxygen consumption rate (OCR) and mubritinib sensitivity (% of live cells), shown in Fig. 2c, should be presented for all mubritinib doses, and particularly for the dose of 500 nM, which is utilized in subsequent experiments. Additionally, it would be useful to display the correlation not only between viability and basal OCR but also with maximal OCR. This analysis could identify varying levels of sensitivity to ECT inhibition, aligning with the expectation that different BTSCs may exhibit varying degrees of dependency on mitochondrial OXPHOS. This would suggest that different GBMs may require different dosages of the drug. In all the experiments presented in the manuscript, the authors use the lines exhibiting the highest mubritinib sensitivity (BTSC 53, BTSC73), which might not be representative of all GBMs. This selection bias need explicit clarification in the text.

Major Point N.2.

In Fig. 2b, the statistics is significantly biased as it is calculated based on technical replicates, rather than on a significant number of independent models featuring either wild-type or mutated EGFR. Presented in this manner, this analysis is unacceptable. Additionally, as noted previously, the models used in this manuscript do not represent the overall GBM genetics, particularly due to lack of EGFR amplified models, which correspond to 40% of cases, and cannot be recapitulated by EGFR mutations. In general, the number of models is too small to draw any conclusion regarding the relationship between genetics and mubritinib sensitivity (including conclusions concerning TP53, or the MGMT status, shown in supplementary figures 1b-c). If the authors intend to claim that GBMs are sensitive to mubritinib independently of the genetic status, they should repeat their experiments by using models representative of the major genetic/transcriptional subtypes of GBMs, by clearly characterizing and identifying them in the experiments: e.g. 'classical/EGFR-amplified'; 'mesenchymal'; 'proneural/PDGFR amplified'. Otherwise (more realistically), it is suggested to remove claims that mubritinib is effective independently of genetic alterations throughout the manuscript (including the abstract and the discussion).

Major Point N.3

Fig. 2k-l present a transcriptional analysis with questionable representativeness as it is performed on the single line BTSC147 from a recurrent GBM, which is unlikely to represent primary GBMs. The analysis appears overly descriptive and fails to add significant information beyond the observation that mubritinib induces a proliferative arrest, as assessed in biological experiments. Additionally, the claim that the Neftel 'Neural Progenitor Cell' signature is altered in a biologically significant manner after only 24 hours of mubritinib treatment seems questionable. As such, this analysis should be moved to supplementary information. A more intriguing alternative would be to compare groups of BTSCs that exhibit high or low sensitivity to mubritinib and attempt to identify gene sets that can correlate with and possibly contribute to explain differences in drug sensitivity.

Major point N. 4

Figure 3. LDA need to be measured at longer timepoints (14-21 days vs. 7 days shown).

Major point N. 5

Supplementary Figure 3c aims to demonstrate that neural stem cells are unaffected by mubritinib merely by showing stem markers in western blots, which is insufficient. To provide convincing evidence, an LDA should be performed using human Neural Progenitor Cells.

Major Point N. 6

Page 9. The mechanistic nexus between OXPHOS inhibition and radiosensitization described by the authors remains unclear. In particular, the link between enrichment in OXPHOS proteins observed in recurrent vs.primary GBMs on the one hand, and downregulation of homologous recombination related-pathways on the other hand is difficult to grasp. The authors should endeavor to more clearly explain how mubritinib can interfere with the adaptive response to ionizing radiation, thereby providing a rationale for experiments combining the two treatments. As noted in the discussion (page 14), 'targeting mitochondrial respiration is an emerging strategy to overcome radioresistance in the tumour hypoxic areas'. Thus, a plausible mechanism of mubritinib-induced radiosensitization may involve reducing oxygen consumption, thereby leaving more oxygen available for diffusion and improving radiation response (by increasing generation of reactive oxygen species). To provide convincing mechanistic evidence, the authors should include in vitro experiments assessing the ability of mubritinib to radiosensitize BTSC in both normoxic and hypoxic conditions. LDA or radiobiological clonogenic assays showing the effect of combination treatment on stem cell frequency are recommended.

Major Point N. 7

Fig. 5d. Concerning the scheme of in vivo treatment, it is unclear why irradiation is administered 5 days after the beginning of mubritinib treatment, considering that mubritinib reaches its peak brain concentration much earlier, as shown in Fig. 4d. Furthermore, if mubritinib alone is effective against the tumor, comparing tumors that have been treated with IR alone at the same time-point as those treated with IR + mubritinib seems inappropriate. This is because, in the latter scenario, IR is applied to tumors that are likely reduced in volume compared to those treated with vehicle prior to IR. This discrepancy could introduce bias in the evaluation of the combined treatment's efficacy.

Major Point N. 8.

Figure 6b. The methodology employed to measure the effect of mubritinib on human neural progenitor cells should be the same as that used for BTSC. Moreover, a positive control (a treatment inducing death, such as bosentan for hepatocytes) needs to be added.

Minor points

Minor point N.1

Please use consistent units (nM or uM) for mubritinib.

Minor point N.2

ND1 expression in transduced cells should be shown by western blot (in Supplementary Figures).

Significance

This manuscript reports preclinical results on the use of mubritinib, a drug targeting the mithochondrial electron chain transport complex 1, to halt proliferation of glioblastoma (GBM) stem cells in vitro and treat experimental GBMs generated by stem cell transplantation. Given that the standard therapy for GBM still relies on a limited number of conventional options, evidence demonstrating the preclinical effectiveness of mubritinib could exert a significant translational impact. Mubritinib has not yet been proposed for GBM treatment, but there is convincing evidence that the drug may be effective in subsets of acute myeloid leukemia that rely on oxidative phosphorylation (Baccelli et al., Cancer Cell 36:84, 2019. PMID: 31287994). Data provided in this manuscript on potential effectiveness of mubritinib are overall convincing. However, in its current form, the manuscript present major limitations regarding the representativeness of models used, which do not support the claim that mubritinib could be universally useful in GBM, and regarding mechanistic aspects of mubritinib combination with radiotherapy. These and other aspects could be addressed through additional experiments.

The audience interested in the reported findings includes preclinical and clinical neuro-oncologists. My field of expertise is biology and genetics of glioblastoma stem cells and generation of in vitro and in vivo GBM preclinical models.