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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors start by taking a previously published model of the plant circadian clock and implement five changes: 1) updating the network topology to reflect some recent experimental findings, 2) make a spatial model loosely based on a seedling template 3) introduce coupling between cells based on shared levels of CCA1/LHY 4) randomly rescale time in each cell to induce inter-cell differences in period, 5) include a light sensitivity that depends on the region considered.

For a certain configuration of light sensitivities/intensities, the different periods of oscillations in each seedling region roughly match that of experiments. With a sufficiently high coupling between cells, the system can also generate spatial waves, which are also observed in the experimental system.

With pulsed light inputs the spatial pattern is still produced. The authors then investigate the robustness to environmental noise by generating stochastic light signals and show that the global synchrony, as measured with a synchronisation index, increases with cell-to-cell coupling strength. The paper is overall well-written, and the background and details of the analysis are well presented.

Major comments:

For the first part of paper, the output of the model is certainly the focus. There is virtually no discussion of the inferred parameters and how much confidence the authors have in their values.

My main issue with the paper is about the section with noisy light signals, which is included in the title and is ultimately one of the main themes of the article.

Specifically, on line 224:

"This decrease in cell-to-cell variation revealed an underlying spatial structure (Fig 4D, middle and right, and S13 Fig), comparable to that observed under idealized LD cycles (Fig 4B, middle and right, and S12 Fig)."

Firstly, I don't feel these conclusions match with the data presented. Comparing figure 4D middle and right with figure 4B middle and right shows a clear and pronounced loss in spatial structure. In its current form, this statement has to change, but I believe there are at least two other major issues with this figure:

1) The figure is clearly designed to invite a comparison between the noise-free light cycles on the left with the noisy cycles on the right. However, due to how the noisy light is simulated, the variance of light signal increases AND the average intensity of light decreases by 50%. When comparing the left and the right, we therefore don't know whether the changes are due to differences in the average signal or differences from the stochasticity. I think the authors should simulate a noisy light signal with the same mean intensity level as the deterministic signal. . 2) The noise model for the light doesn't seem realistic. On line 484 is says:

"We made the simplifying assumption that each cell is exposed to an independent noisy LD cycle due to their unique positions in the environment. LD cycles were input to the molecular model through the parameter L".

In fact, this could be considered as an incredibly complex signal, because for 800 cells it means drawing 800 random light signals. The implication is that two adjacent cells receive statistically independent light signals. Depending on chance, one cell might receive tropical levels of light while its neighbour experiences a cloudy day. This affects the interpretation and conclusions from figures 4 and 5. I propose two different ways of improving the simulation of the noisy light signal:

a) In one extreme case, all cells receive the same noisy light signal, and the other extreme, they all receive independent signals. You could consider a mixture model of light signals, where each cell receives \lambda L_global(t) + (1-\lambda) L_individual(t), where L_global(t) is a global light signal that is shared by all cells and L_individual(t) is a light signal unique to an individual cell. The mixing parameter \lambda controls how similar the light signal is between cells

b) Clearly the light signal will differ depending on the region, but there will be some spatial correlation. You could also consider methods of simulating light such that neighbouring cells receive correlated signals, although this might be difficult.

Assuming that the problem with the mean signal is corrected, do you expect the average spatial pattern to be the same between figure 4 B and D with no coupling (J=0) (although an increase in the variance between cells)? Perhaps not (owing to nonlinearities in the system), but it would be interesting to comment.

The different periods in the different regions of the seedling are caused by differences in light sensitivity, which the authors claim is justified from refs 12-15. An alternative hypothesis is the that biochemical parameters such as degradation rates are different between regions. This is briefly alluded to in the introduction, but I think it would be interesting to discuss further. What would be the pros and cons of the two different mechanisms?

I understand that the authors used a pre-existing model, but I must say that I find the way that light is incorporated into the model a bit confusing.

On line 345 it says: "L(t) represents the input light signal (L = 0, lights off; L > 0, lights on) and D(t) denotes a corresponding darkness input signal (D = 1, lights off; D = 0, lights on)."

Surely the only thing that matters biophysically is the number of photons hitting the plant? Could you explain why the model needs to have a separate "darkness signal" compared to just a single light signal?

In the model, the light intensity changes depending on the region. It might make more sense for interpretability if instead there is an additional light-sensitivity coefficient that depends on the region, because at the moment I'm not sure what units L(t) is supposed to take.

Minor comments

Could you more explicitly describe a possible molecular mechanism through which the coupling acts?

In Figure 1C it looks like different genes are coupling to different genes, so you may need to rearrange it.

Line 103: "We found that regional differences persist even under LD cycles, but cell to-cell minimized differences between neighbor cells." Missing word.

Line 124: "The coupling strength was set to 2 (Methods)." This is meaningless in isolation, so it would be better to briefly explain what the coupling parameter is before mentioning its value.

Through the text, I think De Caluwe should be corrected to De Caluwé

Typo line 493

Code and data are not made available.

Significance

The authors motivate the paper by highlighting that their proposed model improves on phase-based models in that it describes underlying molecular mechanisms.

From an experimental side, it's interesting that a model is developed and directly compared with measured spatio-temporal waves of gene expression. From a theoretical side, the authors address questions relating to oscillations, multi-scale modelling and noise robustness that also generalise to other systems. I therefore expect that both experimental and theoretical audiences will be interested in the results.

There are many possible additions and modifications that could be made to the model, and so the model and analysis could provide a platform for future research. However, I can't comment on whether there are similar pre-existing models of the plant circadian clock that contain both a molecular description of the circadian clock as well as a spatial scale.

REFEREE'S CROSS-COMMENTING

Comments on Review #1:

The time is rescaled in each cell, meaning that each cell has a unique period, but the dynamics remain deterministic and hence the peak-to-peak times will be exactly the same for each cell. I imagine this isn't completely consistent with single-cell data (if available), where peak-to-peak times are very likely to be variable due to noisy gene expression. In a future paper it would be interesting to analyse the system using stochastic differential equations.

Comments on Review #2:

I agree on the following two points:

1) It would add value to discuss whether the different ranking of light sensitivities by organ matches any available experimental data.

2) As the Reviewers point out, there are many possibilities for testing the robustness of the system to light clues, including varying the length of the day. Although outside of the scope of this paper, I wonder if it's possible to find data from a light sensor measuring light intensity across an entire year? Plugging such data into the model and measuring how the amplitude and period changes would be really interesting, in my opinion.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The manuscript presents an improved model of the circadian clock network that accounts for tissue-specific clock behavior, spatial differences in light sensitivity, and local coupling achieved through intercellular sharing of mRNA. In contrast to whole-plant or "phase-only" models, the authors' approach enables them to address the mechanism behind coupling and how the clock maintains regional synchrony in a noisy environment. Using 34 parameters to describe clock activity and applying the properties mentioned above, the authors demonstrate that their model can recapitulate the spatial waves in circadian gene expression observed and can simulate how the plant maintains local synchrony with regional differences in rhythms under noisy LD cycles. Spatial models that incorporate cell-type-specific sensitivities to environmental inputs and local coupling mechanisms will be most accurate for simulating clock activity under natural environments.

We have the following major criticisms as follows

1) When assigning light sensitivities in different regions of the plant, the authors assign a higher sensitivity value to the root tip (L=1.03) than they do to the other part of the root (L=0.90). We are curious why the root tip would have higher light sensitivity than the rest of the root. Is this based on experimental data (if so, please cite in this section or methods)? It seems that these L values were assigned simply to make sure they recapitulated the period differences observed in Fig. 2A. Are these values based on PhyB expression in those organs? Or perhaps based on cell density in those locations?

2) In the discussion of the test where they set the "light inputs to be equal" in all regions to simulate the phyb-9 mutant, could the authors please clarify whether that means they set the L light sensitivity value equal in all regions? a. If they are referring to setting the L value equal to all regions, we suggest that this discussion be moved to the section about different light sensitivities instead of the local sharing of mRNA section. b. Additionally, is it possible to set the light sensitivity to zero for all parts of the plant? We think this would be more suitable to simulate the phyb-9 mutant phenotype.

3) Based on the recent Chen et al. (2020) paper showing ELF4 long-distance movement, we think it would be of great interest for the authors to model ELF4 protein synthesis/translation as the coupling factor, in addition to the modeling using CCA1/LHY mRNA sharing. We understand you may be saving this analysis for a future modeling paper, but this addition to the paper could increase the impact of this paper.

4) This model is able to simulate circadian rhythms under 12:12 LD cycles, which represents two days of the year-the equinoxes. We are curious if the model can simulate rhythms under short days and long days as well. We understand this analysis may be outside the scope of this paper and may require changing the values of the 34 parameters used but think it could be a useful addition here or in future work.

And minor criticisms as follows

1) In the first paragraph of the results section, it would be helpful for the authors to reference Table S1 when they mention the 34 parameters used to model oscillator function

2) In the first paragraph of the section titled "Local flexibility persists under idealized and noisy LD cycles", it would be helpful for the authors to reference S12 Fig after the last sentence that starts "However, ELF4/LUX appeared more synchronized..."

3) In the first paragraph of the section titled "Cell-to-cell coupling maintains global communication under noisy light-dark cycles", the authors refer to a "Table 1" but I think they mean to refer to Table S1"

4) In Fig. 1, panel C is described as demonstrating the cell-to-cell coupling through the "level of CCA1/LHY". This phrasing is vague and we think could be improved to the "mRNA level of CCA1/LHY".

Significance

This work would be broadly interesting to other researchers studying cell-to-cell signaling and coupling of circadian rhythms in plants and other species where spatial waves of gene expression have been observed (i.e., mice and humans). Additionally, the computational modeling aspect of this work was easily interpretable for someone outside this expertise. Our expertise lies in plant circadian biology.

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Referee #1

Evidence, reproducibility and clarity

A. Summary:

In this modeling study, the authors devised a multicellular model to investigate how circadian clocks in different parts (organs) of plants coordinate their timing. The model uses a plausible mechanism to explain how having a different sensitivity to light leads to different phase and period of circadian clock, which is observed in different plant organs. The model allows for entrainment in Light-Dark (LD) cycles and then a release in always-light (LL) environments. The model disentangles numerous factors that have confounded previous experiments. In one instance, the authors assigned different light sensitivities to the different organs (e.g., root tip, hypocotyl, etc.) which unambiguously show that this one element alone - spatially differing sensitivity to light - is sufficient for recapitulating experimentally observed differences in periods and phases between plant organs. The model also recapitulates the spatial waves of gene expression within and between organs that experimentalists reported. At the sub-tissue level, the model-produced waves have similar patterns as the experimentally observed waves. This confirmation further validates the model. By having the cells share clock mRNA, from any clock component genes, showed the same, experimentally observed spatial dynamics. The main conclusion of the study is that regional differences (e.g., between different organs) in light senilities, when combined with cell-to-cell sharing of clock-gene mRNAs, enables a robust, yet flexible, circadian timing under noisy environmental cycles.

B. Specific points:

1.Lines 125-127: "To simulate the variability observed in single cell clock rhythms, we multiplied the level of each mRNA and protein by a time scaling parameter that was randomly selected from a normal distribution." - Why not add a white (Gaussian) noise term to these equations? How does multiplying by a random variable (for rescaling time) different from my proposal? Some explanation should be given in the text here.

2.Does the spatial network model simplify calculations by assuming separations of timescales (e.g., for equilibration in concentrations of mRNAs that diffuse between cells)? If so, it would be good to spell these out in the beginning of the Results section (where the model is described).

3.Lines 161-162: "....in a phase only model by local...." should be "....in a phase model only by local...."

4.Lines 188-190: The authors observed that qualitatively similar/indistinguishable behaviors arose regardless of which elements are varied (e.g., global versus local cell-cell coupling, setting light input to be equal in all regions of the seedling, etc.). Then they claim here that "...these results show that the assumptions of local cell-to-cell coupling and differential light sensitivity between regions are the key aspects of our model that allow a match to experimental data." - I don't see how this follows from the observation almost any of the variations lead to the same behaviors in this section (spatial waves). Show the reasoning in the text here.

5.Pgs. 9 -10: Section on "Cell-to-cell coupling maintains global coordination under noisy light-dark cycles": The simulation results rigorously support the authors' main conclusion here, which is that local cell-to-cell coupling allows for global coordination under noisy LD cycles. But I'm missing an intuitive explanation (or just any explanation) for why this is. At the end of this section, the authors should provide some intuition or qualitative explanation for the observations that they produced using their model in this section.

6.Lines 261-262: Replace the present tenses with past tenses.

7.Is the main idea that cell-to-cell coupling allows for averaging of fluctuations, between organs or cells within the same organ, while allowing for coordination of the average quantities? Is this responsible for both the flexibility and robustness observed under noisy environmental cycles?

8.Line 304: Is it really true that the mammalian circadian rhythm is centralized? Don't some parts of our bodies have different circadian clock (e.g., slight differences in phase) than some other parts of our bodies?

Significance

Overall assessment:

I enthusiastically recommend this work for publication after the authors address my comments below (please see "Specific points").

The model's main strength is that the authors could vary each ingredient separately - light sensitivity of each cell/organ, which gene's mRNA diffuses between cells, cellular noise, local versus global cell-cell coupling, etc. Afterwards, the authors could determine which of these variations produces which experimentally observed behaviors. Another strength of the model is that it can reproduce not just one, but numerous, experimentally observed behaviors that are important for understanding circadian clocks in plants. Thus, the model is grounded in experimental truth and produces experimentally observed results. Crucially, since the authors could vary every single element in the model independently of the other elements, the authors are able to provide plausible explanations for why the experiments produced the results that they did (experimentally, a number of confounding factors prevented one from pinpointing to which element produced which observation).

Another strength of the model is also extendable, by other researchers to investigate other plant physiologies in the future (e.g., circadian clock's influence on cell division). The authors highlight these future uses in the discussion section. Therefore, I believe that this work will be valuable to plant biologists, non-plant biologists who are interested in circadian clocks, and systems biologists in general.

The manuscript is also well written and relatively easy to follow, even for non-plant biologists like myself.

REFEREE'S CROSS-COMMENTING

Comment on Reviewer #2:

I agree with his/her major criticism #3 (ELF4 long-distance movement). I find this to be a reasonable request. Fulfilling it would increase the paper's impact.

Comment on Reviewer #3:

The reviewer's point (1) asks for a reasonable request. Regarding his/her point (2): This is also reasonable. I'd recommend his/her suggestion (a). In the end, I'd be interested to see how the authors respond to this (what function they choose to let adjacent cells be subjected to some correlated light-input intensity. I'd be happy with something simple such as < intensity > + noise, where <intensity> is a deterministic term that, for example, decreases exponentially as one moves away from some central cell. Basically, I'd let the authors decide how to implement this and accept their current implementation - no correlation in light-intensity between adjacent cells - as an extreme scenario, as this reviewer points out.

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Reply to the reviewers

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

The authors generated and analyzed a great amount of single-cell RNA FISH data over time on circadian genes (Nr1d1, Cry1, Bmal1), and performed model selection/fitting to explain the observed mRNA distributions. They decomposed the mRNA variability into distinct sources, and showed that intrinsic noise (transcription burst) dominates the variance. Therefore, looking at transcript counts may not be feasible to estimate single-cell circadian phase. However, the study is quite descriptive and ends up being a bit dissatisfying, so if the authors could improve this aspect by perhaps analyzing a mechanism on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho), it would help quite a bit in this regard. The model selection/fitting itself was not really sufficient to compensate for this, as it stands .

We thank the reviewer for appreciating the new smFISH data, the analyses performed, and the consequences regarding phase inference from single cell snapshots.

The reviewer suggests “perhaps analyzing a mechanism on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho)”, and we have thus added a new Results paragraph (lines 281-316) and two new Supp Figures 13 and 14 to directly address this point.

Specifically, we have added a dynamic, stochastic model of the circadian clock in order to add mechanistic insight into the parameters of the preferred model M4. Concerning \rho, in the initial manuscript we suggested that the correlations of cell-specific burst sizes (described by the parameter \rho) in the preferred model M4 could result from the underlying network topology. To substantiate this claim, we have now added an analysis of a stochastic model of the clock that includes gene-gene interaction amongst the core-clock genes. The core-clock network involves variables (such as protein levels), parameters (such as mRNA/ protein half-lives) and additional genes (such as Clock) that are not directly measurable in our experiments; and thus offering a detailed mechanistic mathematical model for our data is therefore not realistic. We therefore developed a simplified mathematical model for the three measured genes to explore the underlying mechanisms that could control the parameter \rho, as the referee suggests. As a starting point, we used the circadian clock gene network topology for Nr1d1, Cry1 and Bmal1 as modelled in Relógio et al. (Relógio et al., 2011) (see new Supplementary Material). To keep the model close to the inference framework, we used oscillatory functions for the burst frequency while the transcription rate (and hence the burst size) for each gene is affected by the protein levels of the other genes in the network. Using stochastic simulations we show that, for particular configurations of feedback where the negative repression of Nr1d1 by CRY1 is high, the network can generate positive mRNA correlation between Bmal1/Cry1 mRNA and negative correlation between Nr1d1/Cry1mRNA, as observed in our data (Figure 2C). Furthermore, using the same inference framework as for our data on the simulated mRNA distributions, the obtained \rho is positive for Bmal1/Cry1 and negative for Nr1d1/Cry1, which was also found for our data (Figure 3C). Even though the model is clearly a simplified representation of the clock, these simulations give credence to the scenario that the \rho parameter obtained from the data is a signature of the underlying network topology.

While the emphasis of the paper is certainly on parameter inference of the single-cell RNA FISH data, we believe the addition of this dynamic model provides more mechanistic insight into the results of the model fitting and hence significantly more depth to the article.

\*Specific comments:** *

1.It is hard to distinguish the RNA FISH signals (Figure 1A, 2B). It is probably technically challenging as the mRNAs are of low abundance. I think it may help if they adjust the contrast for the cytoplasm stain or just delineate the cell boundaries.

Thank you for pointing this out, and we agree that our rendering of the FISH images was not optimal and have now significantly improved it (see new Figure 1A and 2B). Considering the other reviewers’ comments related to the images, we have now 1) added the cell contours as requested; 2) use red/green for the smFISH signal in the pairs of genes; 3) we have improved the contrast to make it easier to distinguish the RNA FISH signals.

2.In Figure 2C, the authors showed gene-pair correlations with cells of all sizes. Could the authors do a size-dependent extrinsic-noise filtering (Padovan-Merhar, Dev. Cell, 2015; Hansen et al., 2018, Cell Systems) to better dissect the correlations?

We used negative binomial distributions to directly model the number of mRNA in the cells, which is a natural choice given that the raw smFISH are integer counts. The model incorporates cell size dependencies in a unified framework, which predicts the joint distribution of raw counts, which is why we showed raw counts in the main figure. That being said, as the referee suggests, it can be useful for exploratory purposes to see the relationship between the measured genes while regressing out the contribution of cell area, and we have now added this analysis as Supp Figure 9. On line 156-161 we write:

“To also estimate the correlation between genes while accounting for cell area, we regressed out the area for each gene and recalculated the correlation coefficients [37,38]. Since all genes are positively correlated with area (Fig. 2A), this processing shifted the correlations for both pairs of genes. Specifically, the correlation coefficients for the area-filtered mRNA counts decreased but remained positive for Bmal1/Cry1 and became more negative for Nr1d1/Cry1(Supp Figure 9).”

3.For fitting model M3, as the authors pointed out, there are many local minima. Is the fitting score truly sufficient to eliminate the possibility for partial synchrony especially considering that the authors didn't show how effective the Dex treatment was to synchronize the circadian phase?

Thank you for this comment. In fact, we didn't mean to fully eliminate the possibility of imperfect synchronization, but have tried our best to address it both experimentally and with modeling.

Experimentally, in addition to the Dex treatment, we also compared with a condition in which we entrained the cells using temperature cycles, which is a standard in the field to achieve the best synchronization. We obtained a fold change of 2.1, which was in the range of previous studies (Saini, et al, 2012) and was slightly higher than with Dex synchronisation (1.6). Given that the improvement was not high and that it was important for us to study the system under free-running conditions and not in an entrained state (i.e. phase locking, which distorts the free dynamics and noise characteristics of the oscillator), we used the Dex protocol.

Model 3 was used as a computational approach to correct for the individual phases. In addition to the difficult optimisation landscape, the challenge with model M3 also resides in the difficulty of estimating an individual phase for each cell, as the two mRNA counts measured in each cell do not contain sufficient phase information. This could potentially be resolved by either measuring more genes simultaneously, but is, however, beyond the scope of the present manuscript. We have added discussion on this to the text on lines 244-248:

“Thus, it was apparently difficult to use model M3 to correct the individual phase for each cell, likely due to the fact that the two mRNA counts measured in each cell do not contain sufficient phase information, and that the global optimisation problem contains many local minima. This could potentially be improved by measuring more genes simultaneously.”

We have also added a new Results section (lines 305-316) and Supp Figure 14 to show that imperfect synchrony alone cannot explain the correlation structure observed in our data. Indeed, if two genes have a similarly phased oscillation, the expression of the two genes will be positively correlated (as shown in the new Supp Figure 14). Similarly, when the oscillations are in anti-phase, negative correlations will be found. Given that Nr1d1 and Cry1 are closer in phase than Bmal1 and Cry1, one would expect that the correlation between Nr1d1 and Cry1 (once accounting for area) would be more positive than for Bmal1 and Cry1, which was not found in the data (area-corrected correlations shown in Supp Figure 9). It therefore seems unlikely that the observed correlations could be caused by imperfect synchrony alone. Together with our simulations of the gene network (described above), we therefore argue that gene-gene interactions are a more plausible mechanistic explanation of the correlations observed in our measured bivariate mRNA distributions.

4.Regarding model M4, the authors added a cell-specific noise term without specifying the contributing factors. Typically adding degrees of freedom should improve fitting and make it easier for a model to fit, why not in this case? Can the authors provide some explanations/mechanisms.

We believe there has been a misunderstanding regarding model M4. By adding parameters, model M4 is indeed easier to fit. There is even a problem of overfitting whereby the burst frequency becomes unrealistically high and the model effectively fits a Poisson distribution to each individual cell. To avoid this, we lock the burst frequency values to the posterior mean values from model M2. After describing model M4, we write (lines 260-265):

“When all parameters are free, we noticed that the burst frequency can become unrealistically high due to a tendency to overfit to individual cells, and we therefore locked the burst frequency to the posterior mean values from model M2. The PSIS-LOO scores overall favoured model M4 (Fig. 3B), and the predicted joint probability density shows good similarity to the observed data (Fig. 3D) (all time points shown in Supp figure 11).”

Regarding the above comment in the reviewer’s summary on contributing factors of model M4 we added a simple dynamical model that attempts to explain at least one possible mechanism of generating correlations in cell-specific bursting parameters (see above).

5.The authors should include the number (range) of cells analyzed in the figure legends.

We have now added the number of cells used at each time point to the legend of Figure 1D. To respond to Reviewer #2 we have also added details on the number of smFISH replicates used at each time point. The number of cells for each replicate is shown in Supp Figures 2-5.

Reviewer #1 (Significance (Required)):

Overall, we felt conflicted about the manuscript. On one hand, the authors generated and analyzed a great amount of single-cell RNA FISH data over time on circadian genes. On the other hand, the manuscript was a bit dissatisfying/descriptive. If the authors could provide and analyze some sort of mechanisms on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho) it should help improve the manuscript.

We thank the review for the suggestion to expand on the mechanistic interpretation, which we have followed. In addition, we would like to emphasise that a similar smFISH analysis of the core circadian oscillator has never been done, and we believe our data represents a significant contribution to the field. Moreover, our quite generic probabilistic inference framework for smFISH using mixture models to describe intrinsic (transcriptional bursting) and extrinsic fluctuations is also novel and the code provided (written using the Stan probabilistic programming language) might find a wide applicability.

Concerning the mechanistic description, as described above, we added a stochastic, dynamic model of gene expression and propose that gene-gene interactions within the core-clock network topology represent a plausible mechanism for generating correlated burst parameters between genes, which are a feature of the preferred model M4 found during inference. We additionally added an explanatory figure to argue that, given the phase relationship between genes, imperfect synchronisation alone cannot explain the observed correlations that we observe between the pairs of genes. Together, this analysis provides more mechanistic insight into the underlying factors controlling the gene-gene relationships in our measured bivariate mRNA distributions.

\*Referees cross-commenting** *

I agree with Reviewer #3 regarding expanding the discussion to include the Shah & Tyagi and Raj et al citations on buffering. However caution should be exercised regarding ref 26 as it is quite controversial and subsequent analyses came to different conclusions (PMID: 30359620 and 30243562). The general consensus is that nuclear buffering of transcript noise (proposed in ref 26) is not a general phenomenon (ref 27 is specific to the calcium response pathway). In fact, the presence and evolution of specific pathways to buffer transcriptional noise, such as protein-protein mechanisms (Shah & Tyagi) or extended half-life proteins (Raj et al. and others), argues that transcript fluctuations are not probably buffered in general.

Following the suggestion of Reviewer #3, we have expanded the Discussion to include the references cited (Shah & Tyagi, Raj and others).

Previous work from our lab is also nuancing the conclusions from references 26 and 27. Specifically, buffering effects are expected to be highly gene-specific (3’UTR), and in fact we have not seen those with our unstable construct during live-cell imaging (Suter et al., 2011; Zoller et al., 2015). We have also added text in order to explicitly state that subsequent papers have nuanced the general claims in references 26 and 27. In the text we write (lines 335-342):

“One explanation for the low intrinsic fluctuation in these studies is that transcriptional fluctuations are filtered by nuclear retention, though other reports suggest that Fano factors (variance/mean, a measure of overdispersion compared to the Poisson distribution) can be even larger in the cytoplasm than in the nucleus [38]. In the cells used here, the strong signature of transcriptional bursting and high intrinsic noise is consistent with live imaging of a Bmal1transcriptional reporter in the same cell line under similar growth conditions, where intrinsic noise was estimated to be 4-times larger than extrinsic noise [23].”.

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

\*Summary:** *

The authors study experimentally and computationally the dynamic transcription of circadian clock genes over time in individual cells with single molecule RNA-FISH with the aim to understand how different noise sources contribute to single cell transcription variability and basic functions of circadian clocks. The authors integrate experiments with computational modeling to understand biology.

\*Major comments:** *

This study has some major limitations that need to be addressed to test the model usefulness, to understand noise sources and to gain biological insights into circadian clocks.

We thank this reviewer for the constructive feedback which enabled us to significantly strengthen the revised manuscript.

The limitations are on the experiments, the computational implementation of the modeling and the integration of experiments with models.

Although the experimental datasets contain several hundred cells per time point for multiple time points, only a single replica experiment is presented. From the presented data it is not clear how reproducible these temporal patterns are and if indeed differences between timepoints can be resolved if multiple biological replica experiments have been analyzed. To address this point at least three biological experiments needs to be presented and analyzed for each of the genes. Plotting the SEM on the means in figure 1B is misleading because several hundred cells have been measured which automatically makes the error small. The SEM just describes how well we can determine the mean from a distribution. Instead a mean and std from the biological replicas need to be plotted to show how experimental variability in experiments is resulting in the described expression pattern. This is similar to RNA-seq data or RT-PCR from multiple replica.

We certainly agree that demonstrating reproducibility is important. Note that our smFISH data is from three independent cell culture dishes and microscopy slides, which included independent cell synchronization. This was described in the Methods but we agree that the data presentation was not showing the individual replicas, which we have now added. In Figure 1B, we now show the mean of each replicate for each time point. While the reviewer suggested displaying the mean and standard deviation across replicates, we show all data points at each time point to make it even more transparent. The mRNA distribution of each replicate is also shown in Supp Figures 2-5, together with individual quantification of mean, coefficient of variation and number of cells.

In addition, to further demonstrate the reproducibility of the temporal patterns we have performed an additional independent experiment on four time points. This experiment shows that the oscillatory patterns for Nr1d1 and Cry1are clearly significant and reproducible (new Supp Figure 7). The combination of the replicates shown for the main experiment (Supp Figures 2-5) and the new replicate experiment (Supp Figure 7) shows that the oscillatory temporal patterns for the mean mRNA levels are robust and reproducible, and in fact similar as those found in bulk analyses (Ukai-Tadenuma et al., 2011; Hughes et al., 2009), which is expected.

It is also not clear how good the cell segmentation works and how does cell segmentation influence the analysis. In figure 1A show the segmentation of the cell boundary together with the membrane stain.

Thanks to this and other reviewers’ comments, we have now significantly improved the presentation of the FISH images. We have now 1) added the cell contours as requested; 2) used red/green for the smFISH signal in the pairs of genes; 3) we have improved the contrast to make it easier to distinguish the RNA FISH signals.

We have also added Supp Figure 1 to show that the cell segmentation we used is reliable. In fact, as we had described, we used the sum Z-stack projections of the red channel (Wu et al., 2018), which we found provides the most accurate cell segmentation. We now show in Supp Figure 1 that the obtained segmentation shows convincing agreement with the cell autofluorescence .

The authors use the RNA mean and RNA-FISH distributions and combine this data to build and compare different models. How do you know that the given data fulfils the central limit so that a model describing the mean is an adequate approach? To test this point, the authors should show through subsampling from the data and the model that indeed their data sets have enough cells to fulfil the central limit theorem.

This comment reflects a misunderstanding of our approach, which we now try to better explain. In our inference framework we use a negative binomial (NB) distribution (and mixtures of NBs) to model the full distribution of mRNA counts, and our approach is therefore not based exclusively on the mean of the distribution. The estimation of model parameters and comparison of models is performed using the PSIS-LOO optimisation procedure (see below). The mixture model of NB binomials makes a few assumptions which we had clearly stated. In fact it captures both bursty transcription (in the limit of short bursts as is biologically plausible, which yields the NB distribution), and cell-to-cell variability (extrinsic noise) captured by the mixture. The suitability of the NB to model bursty transcription is established (Raj et al., 2006), and it is parameterized by a mean and a dispersion coefficient, such that the CV of the distribution is the inverse of the burst frequency (Zoller et al., 2015). Therefore the mean is indeed an important parameter of the model, but we do not see the relationship with the CLT. The used probabilistic inference (PSIS-LOO: Pareto-Smoothed Importance Sampling Leave-One-Out, Vehtari et al. 2017, see below) is established and state-of-the-art for selecting models of the appropriate complexity and we are not aware of a similar previous quantitative model for smFISH analysis.

We have now added significantly more explanations both on the general approach as well as the methodological details in a fully-revised Methods section to avoid further misunderstanding.

A strength of the manuscript is that several competing and biologically meaningful models have been generated. However, the manuscript lacks rigor in terms of how fitting and model selection is performed. It is not clear how good the models fit the data. To address this point, the authors should visually compare the model fits to the data and plot their fit errors as a function of model complexity.

We fully agree that comparing different models using a model selection approach is a powerful methodology, in fact it is arguably the most systematic way to approach modeling problems in quantitative biology. Model selection is an active research area and there have been significant developments recently. Here, we used a state-of-the-art and established Bayesian approach (PSIS-LOO: Pareto-Smoothed Importance Sampling Leave-One-Out, Vehtari et al. 2017), which is certainly rigorous and more objective than visual comparison. The PSIS-LOO is conceptually similar to other approaches of model performance such as AIC or WAIC, and the entire field of model selection aims at establishing rigorous methods to assess the tradeoff between fit errors and model complexity. In PSIS-LOO, this is done by using pareto-smoothed importance sampling to estimate the expected log pointwise predictive density for a new dataset using leave-one-out cross-validation. The PSIS-LOO is the currently recommended metric for measuring model performance in Bayesian analysis (Vehtari et al., 2017) and is considered superior to other approaches such as computations of Bayes factors since it is less sensitive to model priors (Gelman et al. 2013). The performance of the models as measured with PSIS-LOO is shown in Figure 3B. As already mentioned, we have added further details as to how the fitting and model selection is performed in a revised Methods section. We agree that visual comparison is useful to gain intuition and this is why we showed the bivariate distributions in Figure 3D and in Supp Figure 11.

Regarding the comment on “fit error”, note also that we probabilistically model the full mRNA distribution for each gene. In each cell, there is a likelihood score that measures the likelihood of observing the measured mRNA count given the modelled probability distribution. As our approach is based on this likelihood, the notion of “fitting error” needs to be replaced by the log likelihood (‘fitting error’ is mathematically equivalent to a log-likelihood when the noise model is Gaussian, which is not the case here).

Another limitation is that the models have not been validated for example by using them to make predictions. One type of prediction could be to fit the model to one biological replica and then predict the other replica (cross validation). Another prediction would be to take the distribution fitted to the experimental data and then compare the model mean to the experimental mean.

Thank you for this comment. As explained above, we used the state-of-the-art PSIS-LOO to measure the predictive performance of the models, which approximates the result of leave-one-out cross-validation using the full data set. To further assess the predictive capabilities of the model, we have now also added a “leave-replicate-out” cross-validation, as the reviewer suggests (new Supp Figure 12). The aim of our “leave-replicate-out” cross-validation was to test how well the predictions of each model generalise to independent cells that are not in the training set. To do this, we trained each model while omitting the data from one gene on a test slide. We then calculated the likelihood score of the test slide using the parameters from the training set, and repeated this for all slides. Similarly to the PSIS-LOO, the results of the leave-replicate-out cross-validation convincingly show that model M4 has the highest predictive performance. This is now described in the updated text on lines 265-271.

The results from fitting and prediction should be plotted as a function of model complexity. This kind of analysis will illustrate how model complexity is supported by the data.

As already mentioned, we used state-of-the-art algorithms to analyze prediction vs. complexity. With the above addition, we now have two methods of calculating the predictive performance of each model: the approximate leave-one-out score as measured with PSIS-LOO and the leave-replicate-out cross-validation. For each model, the PSIS-LOO score is plotted in Figure 3B and the leave-replicate-out cross-validation score is shown in Supp Figure 12.

In the method section on models, a biological motivation must be presented to justify the different model assumption.

Thank you for pointing out that the biological justification of the models needed to be expanded. In addition to the improved justifications already provided in the Results section, we have now updated the Methods section such that a biological motivation is included for each model.

How do the models that fit the distributions describe the mean?

As explained above, the inference is performed on the entire distributions, using a family of distributions (mixtures of NBs) which are parameterized in a biologically relevant manner (transcriptional bursting + extrinsic noise). The mean and variance of the distribution are now described on lines 585-586 in addition to Figure 3A.

It is necessary to list model parameters for each of the models, their description, their parameter values, their parameter uncertainty and units of each parameter.

Thank you, this has now been added as Supplementary Tables 2-5.

It is not clear to me how the joint probability in figures 2,4, S2 and S4 have been used to fit the model.

Again, the joint distributions are modeled using mixtures of NBs and the inference is performed on the entire dataset at once using a log-likelihood approach. This uses all the data at once, and it is embedded in a Bayesian model selection method. The way that the joint probability is used is now clarified in the revised Methods section and in the Results section (lines 208-214):

“For both models M1 and M2, the likelihood of observing the data given the parameters of the model is evaluated using the model-specific NB distribution and the mRNA counts for both genes in each cell. This is performed for both Bmal1/Cry1 and Nr1d1/Cry1 pairs across all time points, and this likelihood is combined with model priors to define the posterior parameter distribution for each model (Methods). We applied Hamiltonian Monte Carlo sampling within the STAN probabilistic programming language to sample the posterior distribution and infer model parameters 40.”

How do the models make sense in the context of the fact that human genes exist as a diploids?

This is a good point, although note though that the 3T3 cells are from mice and not humans. 3T3 cells are tetraploid, and it turns out that under the justified assumption that the bursts are short (Zoller et al., 2015; Suter et al., 2011), the number of alleles rescales the burst frequency, i.e. the effective (observed) burst frequency equals the number of alleles times the burst frequency per allele, but it does not change the shape of the distributions. On line 580-582 we have now written: “Since 3T3 cells are tetraploid, and, again assuming that the bursts are short, the inferred burst frequency for tetraploid cells will be approximately four times that of a single allele.”

The variance decomposition is shortly described but no results are presented to show how this is done. This should be better explained.

The variance decomposition we used is not a new result; in fact, we used the analytical results of Bowsher, C. G. & Swain, P. S. “Identifying sources of variation and the flow of information in biochemical networks” (PNAS, 2012). The mathematical proofs of the formula we use are contained within that reference; however, we have re-written this section to make it clearer to the reader (lines 688-718).

\*Minor comments:** *

In figure 3A, it is not clear to me what these different plots relate to the models. It is also not clear what are equations that describe each model.

The Methods section has now been improved to show the full data-generating mechanism for each model, and each model has its own section title to make it easier to find. We have also improved the legend for Figure 3 to make the relationship to each model clearer.

The legends in figure 3 are not very informative. More details need to be presented to understand this figure.

Thank you for pointing this out, and we have now re-written the figure legend for Figure 3 to make the figure clearer.

Reviewer #2 (Significance (Required)):

This is an interesting and important topic with the potential to have general implication of how to model periodic single cell gene expression data and eventually better understand circadian clocks. This study will expand on other modeling studies of circadian clocks and has the potential to advance the field (PMCID: PMC7229691). I personally have done similar analysis and experiments in another system and biological context which has demonstrated the power of this approach if implemented rigorously. I am not an expert in circadian clocks in human cells.

We thank the reviewer for appreciating the implications for the circadian and single cell gene expression community. Note that to our knowledge, modeling smFISH counts using mixtures of negative binomials combined with Bayesian model selection has not been done. It is both highly relevant biologically (combines intrinsic and extrinsic fluctuations in a rigorous way), general and its applicability extends far beyond the circadian oscillator. Therefore, this approach for quantitative smFISH data analysis also fills an important methodological gap.

\*Referees Cross commenting** *

Reviewer #1:

I agree with the assessment that model fitting and model selection was not sufficient. But I disagreed that the data is enough. Although many cells and time points are analyzed, there is no evidence of how reproducible each mRNA distribution can be measured at each time point. I think reproducibility is key and will also help with the model fitting and identification.

Regarding the point on reproducibility, we have made the following four changes:

1. We have added an independent 4 time-point experiment to show that the oscillatory patterns of the distributions are reproducible (Supp Figure 7).
2. In Figure 1 we now also show the mean of each replicate for the main experiment (Figure 1B).
3. We also show the mRNA distributions of each replicate in Supp Figures 2-5.
4. We have added the “leave-replicate-out” cross-validation to show that that the model performance of the preferred model generalises to independent slides that were not included in training (Supp Figure 12). In responding to Reviewer #1 regarding the modeling, we have now also added a simplified dynamical model of circadian clock expression to add mechanistic insight into our proposed models. Overall, we have significantly expanded the description of the model selection approaches to help readers who are less familiar with Bayesian model selection methods.

Reviewer #3:

Regarding the red background, my understanding is that this comes from the probe hybridization. This is maybe because the probe concentration has not been optimized or the number of probes per gene is low and the signal to noise is not so good.Or it could be auto fluorescent background. In this case a different fluorophore needs to be used to avoid this problem.

Thank you for those comments, and we agree with all reviewers that the presentation of the images needed to be improved. It turned out that in Figure 1, we had shown the cell mask in red so it is clearly not related to probe concentration or autofluorescence. We have now removed the cell mask channel from the main images which allows highlighting better the smFISH signals. All smFISH images for Figures 1 and 2 have been much improved, and we’ve added a new Supp Figure 1 to show the performance of our cell segmentation.

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

In this paper Nicholas et al image mRNAs encoding the key controllers of circadian rhythms, Rev-erba, Cry and Bmal1 in single cells over time. It was shown earlier that single cells exhibit circadian rhythms using reporter genes. A large number of studies have shown that transcription is an inherently stochastic process, which raises a question as to how single cells are able to achieve their rhythms on the face of this noise. Their results show that the number of mRNAs for the three genes exhibit the expected periodicity, but this periodicity is associated with significant cell-to-cell variation. They also explore to what extent this variability derives from stochastic transcription vs other sources of variation that are extrinsic to the genes. The results are interesting and experimental and modeling results are important (however this reviewer is not able to judge the veracity of mathematics that underlay the models).

We thank this reviewer for appreciating the importance of our work.

\*Some of the concerns that arose are listed below:** *

1.The images show an annoying red background. If the red is HCS cell mask, it should be removed, and RNA presented on grey scale. This will make a better presentation. The red hue also appears in fig 2 b but here it is one of the RNA. I suggest in Fig 2 one RNA can be presented in green and the other in red, while the nuclei in blue.

Thank you for this comment. We had indeed shown the cell mask in the red channel and now removed it. Together with the other suggestions and comments from the reviewers, we implemented the following changes: 1) added the cell contours as requested; 2) use red/green for the smFISH signal in the pairs of genes; 3) we have improved the contrast to make it easier to distinguish the RNA FISH signals. The presentation of the images is now much improved.

2.This paper and a few others talk about the cell size contributing to the cell-to-cell variability in mRNA numbers. Where does it come from physically? One can imagine based on the cell cycle stage there could be more than two copies of then gene in a cell, which will yield more RNAs, but they say that their cells don't have much cell cycle variability. Perhaps a clearer discussion is called for rather than just being polite to other investigators.

The referee is right that several studies observed empirically that larger cells show more mRNA molecules in smFISH experiments (Padovan et al., 2015; Kempe et al., 2015). In Padovan et al. (2015), the authors found that transcriptional burst size changes with cell volume and burst frequency with cell cycle. The main theory for transcription scaling with cell volume is to maintain transcript concentration. Using cell fusion experiments, they showed that cellular size can directly and globally affect gene expression by modulating transcription. Furthermore, they proposed that the mechanism underlying the global regulation integrates both DNA content and cellular volume to produce the appropriate amount of RNA for a cell of a given size, which is consistent with a model whereby a factor limiting for transcription is sequestered to the DNA. We used these results to propose a model whereby burst size scales with area, and we found an increase in predictive performance (compare M2 with M1 in Figure 3B). While our model selection supported the inclusion of cell area, the variance decomposition showed that the fraction of variance due to cell area ranged from 4.2% for Nr1d1 to 17.6% for Bmal1. We have now expanded the introduction to discuss this in more depth (lines 73-80) as requested.

3.References 26 and 27 are cited for 10-80% of variance due to gene extrinsic sources. These references actually deny that there is a significant transcriptional noise in most genes. Again, stronger discussion is called for.

As mentioned in the reply to Reviewer 1, previous work from our lab is also nuancing the conclusions from references 26 and 27. Specifically, buffering effects are expected to be highly gene-specific (3’UTR), and in fact we have not seen those with our unstable construct during live-cell imaging (Suter et al., 2011; Zoller et al., 2015). We have also added text in order to explicitly state that subsequent papers have nuanced the general claims in references 26 and 27. In the text we write (lines 335-342):

“One explanation for the low intrinsic fluctuation in these studies is that transcriptional fluctuations are filtered by nuclear retention, though other reports suggest that Fano factors (variance/mean, a measure of overdispersion compared to the Poisson distribution) can be even larger in the cytoplasm than in the nucleus [38]. In the cells used here, the strong signature of transcriptional bursting and high intrinsic noise is consistent with live imaging of a Bmal1transcriptional reporter in the same cell line under similar growth conditions, where intrinsic noise was estimated to be 4-times larger than extrinsic noise [23].”.

4.The results raise a very important question, whether and to what extent the transcriptional noise propagates to the next step of gene regulation and are there buffering mechanisms in the cell. For example, Raj et al, Variability in gene expression underlies incomplete penetrance, Nature 2010, show that alternative pathways serve to buffer the impact of gene expression noise. Similarly, Shah and Tyagi, Barriers to transmission of transcriptional noise in a c-fos c-jun pathway, Mol Syst Biol, 2013, show that variability in mRNA is buffered at protein level and the level of protein-protein complexes. Furthermore, they show that to the extent those vary, the chromatin intrinsically buffers against the fluctuations in numbers of transcription factors. Mention of these and other studies will enrich the paper.

We have modified the Discussion section and now discuss these papers (and a few more). We thank the reviewer for the suggestions, which will help the reader to have a broader overview of noise buffering in gene expression and indeed enrich the paper.

Reviewer #3 (Significance (Required)):

Significance is high. Quality is high.

\*Referees Cross-Commenting** *

I agree with the comments made by other reviewers particularly about references 26 and 27. The major conclusions of reference 26 were questioned by Hansen et al 2018. At the bottom of page 7 the authors are qualifying their results in the light of references 26 and 27. Perhaps now there is less of a need to do so.

As mentioned above, we have added the following sentence citing the Hansen paper to make it clear to the reader that key conclusions of the references 26 and 27 are disputed (lines 335-342):

“One explanation for the low intrinsic fluctuation in these studies is that transcriptional fluctuations are filtered by nuclear retention, though other reports suggest that Fano factors (variance/mean, a measure of overdispersion compared to the Poisson distribution) can be even larger in the cytoplasm than in the nucleus [38].

References

Gelman A, Carlin JB, Stern HS, Dunson DB, Vehtari A, Rubin DB. 2013. Bayesian Data Analysis, 3rd edn. CRC Press, London.

Hughes ME, DiTacchio L, Hayes KR, Vollmers C, Pulivarthy S, Baggs JE, Panda S, Hogenesch JB. 2009. Harmonics of circadian gene transcription in mammals. PLoS Genet 5. doi:10.1371/journal.pgen.1000442

Kempe H, Schwabe A, Cremazy F, Verschure PJ, Bruggeman FJ. 2015. The volumes and transcript counts of single cells reveal concentration homeostasis and capture biological noise. Mol Biol Cell 26:797–804. doi:10.1091/mbc.E14-08-1296

Padovan-Merhar O, Nair GP, Biaesch AG, Mayer A, Scarfone S, Foley SW, Wu AR, Churchman LS, Singh A, Raj A. 2015. Single Mammalian Cells Compensate for Differences in Cellular Volume and DNA Copy Number through Independent Global Transcriptional Mechanisms. Mol Cell 58:339–352. doi:10.1016/j.molcel.2015.03.005

Raj A, Peskin CS, Tranchina D, Vargas DY, Tyagi S. 2006. Stochastic mRNA synthesis in mammalian cells. PLoS Biol4:e309. doi:10.1371/journal.pbio.0040309

Relógio A, Westermark PO, Wallach T, Schellenberg K, Kramer A, Herzel H. 2011. Tuning the mammalian circadian clock: Robust synergy of two loops. PLoS Comput Biol 7:1–18. doi:10.1371/journal.pcbi.1002309

Saini C, Morf J, Stratmann M, Gos P, Schibler U. 2012. Simulated body temperature rhythms reveal the phase-shifting behavior and plasticity of mammalian circadian oscillators. Genes Dev 26:567–580. doi:10.1101/gad.183251.111

Suter DM, Molina N, Gatfield D, Schneider K, Schibler U, Naef F. 2011. Mammalian Genes Are Transcribed with Widely Different Bursting Kinetics. Science (80- ) 332:472–474. doi:10.1126/science.1198817

Ukai-Tadenuma M, Yamada RG, Xu H, Ripperger JA, Liu AC, Ueda HR. 2011. Delay in feedback repression by cryptochrome 1 Is required for circadian clock function. Cell 144:268–281. doi:10.1016/j.cell.2010.12.019

Vehtari A, Gelman A, Gabry J. 2017. Practical Bayesian model evaluation using leave-one-out cross-validation and WAIC. Stat Comput 27:1413–1432. doi:10.1007/s11222-016-9696-4

Wu C, Simonetti M, Rossell C, Mignardi M, Mirzazadeh R, Annaratone L, Marchiò C, Sapino A, Bienko M, Crosetto N, Nilsson M. 2018. RollFISH achieves robust quantification of single-molecule RNA biomarkers in paraffin-embedded tumor tissue samples. Commun Biol 1:1–8. doi:10.1038/s42003-018-0218-0

Zoller B, Nicolas D, Molina N, Naef F. 2015. Structure of silent transcription intervals and noise characteristics of mammalian genes. Mol Syst Biol 11:823. doi:10.15252/msb.20156257

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Referee #3

Evidence, reproducibility and clarity

In this paper Nicholas et al image mRNAs encoding the key controllers of circadian rhythms, Rev-erba, Cry and Bmal1 in single cells over time. It was shown earlier that single cells exhibit circadian rhythms using reporter genes. A large number of studies have shown that transcription is an inherently stochastic process, which raises a question as to how single cells are able to achieve their rhythms on the face of this noise. Their results show that the number of mRNAs for the three genes exhibit the expected periodicity, but this periodicity is associated with significant cell-to-cell variation. They also explore to what extent this variability derives from stochastic transcription vs other sources of variation that are extrinsic to the genes. The results are interesting and experimental and modeling results are important (however this reviewer is not able to judge the veracity of mathematics that underlay the models).

Some of the concerns that arose are listed below:

1.The images show an annoying red background. If the red is HCS cell mask, it should be removed, and RNA presented on grey scale. This will make a better presentation. The red hue also appears in fig 2 b but here it is one of the RNA. I suggest in Fig 2 one RNA can be presented in green and the other in red, while the nuclei in blue.

2.This paper and a few others talk about the cell size contributing to the cell-to-cell variability in mRNA numbers. Where does it come from physically? One can imagine based on the cell cycle stage there could be more than two copies of then gene in a cell, which will yield more RNAs, but they say that their cells don't have much cell cycle variability. Perhaps a clearer discussion is called for rather than just being polite to other investigators.

3.References 26 and 27 are cited for 10-80% of variance due to gene extrinsic sources. These references actually deny that there is a significant transcriptional noise in most genes. Again, stronger discussion is called for.

4.The results raise a very important question, whether and to what extent the transcriptional noise propagates to the next step of gene regulation and are there buffering mechanisms in the cell. For example, Raj et al, Variability in gene expression underlies incomplete penetrance, Nature 2010, show that alternative pathways serve to buffer the impact of gene expression noise. Similarly, Shah and Tyagi, Barriers to transmission of transcriptional noise in a c-fos c-jun pathway, Mol Syst Biol, 2013, show that variability in mRNA is buffered at protein level and the level of protein-protein complexes. Furthermore, they show that to the extent those vary, the chromatin intrinsically buffers against the fluctuations in numbers of transcription factors. Mention of these and other studies will enrich the paper.

Significance

Significance is high. Quality is high.

Referees Cross-Commenting

I agree with the comments made by other reviewers particularly about references 26 and 27. The major conclusions of reference 26 were questioned by Hansen et al 2018. At the bottom of page 7 the authors are qualifying their results in the light of references 26 and 27. Perhaps now there is less of a need to do so.

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Referee #2

Evidence, reproducibility and clarity

Summary: The authors study experimentally and computationally the dynamic transcription of circadian clock genes over time in individual cells with single molecule RNA-FISH with the aim to understand how different noise sources contribute to single cell transcription variability and basic functions of circadian clocks. The authors integrate experiments with computational modeling to understand biology.

Major comments:

This study has some major limitations that need to be addressed to test the model usefulness, to understand noise sources and to gain biological insights into circadian clocks.

The limitations are on the experiments, the computational implementation of the modeling and the integration of experiments with models.

Although the experimental datasets contain several hundred cells per time point for multiple time points, only a single replica experiment is presented. From the presented data it is not clear how reproducible these temporal patterns are and if indeed differences between timepoints can be resolved if multiple biological replica experiments have been analyzed. To address this point at least three biological experiments needs to be presented and analyzed for each of the genes. Plotting the SEM on the means in figure 1B is misleading because several hundred cells have been measured which automatically makes the error small. The SEM just describes how well we can determine the mean from a distribution. Instead a mean and std from the biological replicas need to be plotted to show how experimental variability in experiments is resulting in the described expression pattern. This is similar to RNA-seq data or RT-PCR from multiple replica.

It is also not clear how good the cell segmentation works and how does cell segmentation influence the analysis. In figure 1A show the segmentation of the cell boundary together with the membrane stain.

The authors use the RNA mean and RNA-FISH distributions and combine this data to build and compare different models. How do you know that the given data fulfils the central limit so that a model describing the mean is an adequate approach? To test this point, the authors should show through subsampling from the data and the model that indeed their data sets have enough cells to fulfil the central limit theorem.

A strength of the manuscript is that several competing and biologically meaningful models have been generated. However, the manuscript lacks rigor in terms of how fitting and model selection is performed. It is not clear how good the models fit the data. To address this point, the authors should visually compare the model fits to the data and plot their fit errors as a function of model complexity.

Another limitation is that the models have not been validated for example by using them to make predictions. One type of prediction could be to fit the model to one biological replica and then predict the other replica (cross validation). Another prediction would be to take the distribution fitted to the experimental data and then compare the model mean to the experimental mean.

The results from fitting and prediction should be plotted as a function of model complexity. This kind of analysis will illustrate how model complexity is supported by the data.

In the method section on models, a biological motivation must be presented to justify the different model assumption.

How do the models that fit the distributions describe the mean?

It is necessary to list model parameters for each of the models, their description, their parameter values, their parameter uncertainty and units of each parameter.

It is not clear to me how the joint probability in figures 2,4, S2 and S4 have been used to fit the model.

How do the models make sense in the context of the fact that human genes exist as a diploids?

The variance decomposition is shortly described but no results are presented to show how this is done. This should be better explained.

Minor comments:

In figure 3A, it is not clear to me what these different plots relate to the models. It is also not clear what are equations that describe each model.

The legends in figure 3 are not very informative. More details need to be presented to understand this figure.

Significance

This is an interesting and important topic with the potential to have general implication of how to model periodic single cell gene expression data and eventually better understand circadian clocks. This study will expand on other modeling studies of circadian clocks and has the potential to advance the field (PMCID: PMC7229691). I personally have done similar analysis and experiments in another system and biological context which has demonstrated the power of this approach if implemented rigorously. I am not an expert in circadian clocks in human cells.

Referees Cross commenting

Reviewer #1: I agree with the assessment that model fitting and model selection was not sufficient. But I disagreed that the data is enough. Although many cells and time points are analyzed, there is no evidence of how reproducible each mRNA distribution can be measured at each time point. I think reproducibility is key and will also help with the model fitting and identification.

Reviewer #3: Regarding the red background, my understanding is that this comes from the probe hybridization. This is maybe because the probe concentration has not been optimized or the number of probes per gene is low and the signal to noise is not so good. Or it could be auto fluorescent background. In this case a different fluorophore needs to be used to avoid this problem.

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Referee #1

Evidence, reproducibility and clarity

The authors generated and analyzed a great amount of single-cell RNA FISH data over time on circadian genes (Nr1d1, Cry1, Bmal1), and performed model selection/fitting to explain the observed mRNA distributions. They decomposed the mRNA variability into distinct sources, and showed that intrinsic noise (transcription burst) dominates the variance. Therefore, looking at transcript counts may not be feasible to estimate single-cell circadian phase. However, the study is quite descriptive and ends up being a bit dissatisfying, so if the authors could improve this aspect by perhaps analyzing a mechanism on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho), it would help quite a bit in this regard. The model selection/fitting itself was not really sufficient to compensate for this, as it stands .

Specific comments:

1.It is hard to distinguish the RNA FISH signals (Figure 1A, 2B). It is probably technically challenging as the mRNAs are of low abundance. I think it may help if they adjust the contrast for the cytoplasm stain or just delineate the cell boundaries.

2.In Figure 2C, the authors showed gene-pair correlations with cells of all sizes. Could the authors do a size-dependent extrinsic-noise filtering (Padovan-Merhar, Dev. Cell, 2015; Hansen et al., 2018, Cell Systems) to better dissect the correlations?

3.For fitting model M3, as the authors pointed out, there are many local minima. Is the fitting score truly sufficient to eliminate the possibility for partial synchrony especially considering that the authors didn't show how effective the Dex treatment was to synchronize the circadian phase?

4.Regarding model M4, the authors added a cell-specific noise term without specifying the contributing factors. Typically adding degrees of freedom should improve fitting and make it easier for a model to fit, why not in this case? Can the authors provide some explanations/mechanisms.

5.The authors should include the number (range) of cells analyzed in the figure legends.

Significance

Overall, we felt conflicted about the manuscript. On one hand, the authors generated and analyzed a great amount of single-cell RNA FISH data over time on circadian genes. On the other hand, the manuscript was a bit dissatisfying/descriptive. If the authors could provide and analyze some sort of mechanisms on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho) it should help improve the manuscript.

Referees cross-commenting

I agree with Reviewer #3 regarding expanding the discussion to include the Shah & Tyagi and Raj et al citations on buffering. However caution should be exercised regarding ref 26 as it is quite controversial and subsequent analyses came to different conclusions (PMID: 30359620 and 30243562). The general consensus is that nuclear buffering of transcript noise (proposed in ref 26) is not a general phenomenon (ref 27 is specific to the calcium response pathway). In fact, the presence and evolution of specific pathways to buffer transcriptional noise, such as protein-protein mechanisms (Shah & Tyagi) or extended half-life proteins (Raj et al. and others), argues that transcript fluctuations are not probably buffered in general.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)): **Summary:** In this study, the authors investigate the role of hedgehog signaling and lipid metabolism in the neural stem cell niche of the Drosophila larvae. They demonstrate that Hedgehog localizes to lipid droplets in glial cells and show that Hh is necessary but not sufficient for elaboration of glial membranes and normal rates of glial proliferation during development. In addition, they provide an extensive set of results in support of a model that FGF signaling functions upstream of lipid metabolism and hh in glial cells as well as a parallel ROS mediated pathway in glial cells to promote neuroblast proliferation. In general, the results provide strong support for the conclusions. Specifically, the approaches are sound, the images clearly demonstrate the phenotypes described, and the effects are quantified and tested for statistical significance. **Major comments:** 1.Since Hh RNAi decreases the glial compartment (which slows NB proliferation) and increases the frequency of pH3+ NBs, it is unclear why it would decrease the number of EdU+ NBs (Fig. S3C). 2.If overexpression of htl[ACT] slows the NB cell cycle (as evidenced by reduced pH3 and EdU positive cells), it unclear why it does not reduce the number of NBs (Fig. 4L). 3.What is the justification for presenting the EdU quantifications as an EdU index in which the experimental values are normalized to the average number of positive cells in the control? In many cases, the comparison is to the same w[1118] line so it does not control for a specific genetic backgrounds and yet this method may be obscuring experimental variation present between datasets. Likewise, why is glial number presented as a fold-change but NB number is presented as raw counts (e.g. 2D vs S3E)? **Minor comments:** On the top of P.14, "Figure S7A-C" should probably be "Figure S6A-C" Reviewer #1 (Significance (Required)): The cell autonomous regulation of growth and proliferation of neuroblasts in the larval brain have been well-studied, but much less is known about the non-cell autonomous signals. This paper significantly moves forward knowledge in this area by describing multiple steps of a molecular mechanism for glial regulation of the neuroblast cell cycle. These findings would be of interest not only to the study of Drosophila neuroblasts, but also to the broader adult stem cell field. My expertise is in Drosophila stem cell biology and genetics. Reviewer #2 (Evidence, reproducibility and clarity (Required)): **Summary:** The study by Dong et al., investigates the role of Hedgehog in the glial niche during larval neurogenesis in Drosophila. The authors describe the expression of Hh in cortex glia and its association with lipid droplets. They show that Hh expression in cortex glia is required for cortex glial proliferation, cell autonomously, and for maintenance of the normal cell cycle in neuroblasts. They go on to use a well characterised Drosophila glioma model, activation of FGF signalling, to investigate the requirement for Hh during cortex glial overgrowth. They show that FGF-activated cortex glial overproliferation requires Hh for modulation of neuroblast cell cycle, although Hh does not regulate cortex glial proliferation in this context. Finally, they show that inhibition of lipid modification of Hh rescues the neuroblast proliferation cell cycle defect caused by FGF activation in cortex glia. **Major comments:** 1.From the data in presented in Fig. 2H-K and Fig. S3C, I am very confused about role of Hh in the non-cell autonomous regulation of neuroblast cell cycle. Both RNAi and overexpression of Hh with Repo-Gal4 cause a reduction in the neuroblast EdU index (Fig. 2H-K and S3C). The authors conclude this section on p.7 saying "Together, our data suggests that high levels of glial Hh expression restricts NB cell cycle progression." This statement is not consistent with data. What is the normal physiological role of Hh if both decreased and increased levels of cortex glial Hh expression reduce neuroblast cell cycle? The discussion of p.15 does not clarify this issue. The model in Fig.7J relates to the role of Hh in the context of cortex glial FGF activation and does not illustrate the normal physiological role of Hh in the regulation of neuroblast cell cycle. 2.P.8 "Analysis of the total glial cell number indicates overexpression of htlACT, but not InRwt or EgfrACT, led to an increase in the number of cortex glial cells (Figure 4E-G, I-K)." This statement is confusing as Repo staining was used to quantify total glial numbers (including perineural, sub-perineural and cortex glia) but these data are then taken to represent and increase specifically in cortex glia. This should be clarified. 3.It should be mentioned on p.8 that the data in Fig.4A-K reproduce the findings of Avet-Rochex et al., 2012 and Read et al., 2009. 4.Figure 6F. Presumably due to the increase in glia cell number and dramatic increase in glial cell volume, any gene that is specific to, or enriched in, cortex glia will have increased expression levels in RepoGal4>htlACT larval CNS. Can the authors provide evidence that the increase in the expression of these genes is specific to FGF transcriptional regulation and not just a relative increase in the levels of these genes due to an increase in cortex glia as proportion of total CNS volume? Is there any evidence that Hh, fasn1 and lsd2 are direct transcriptional targets of FGF signalling in glia? 5.FGF signalling has been shown to be necessary and sufficient for cortex glial proliferation. So does knockdown of Htl, or expression of dominant negative Htl, cause a reduction in Hh, fasn1 and lsd2 expression in cortex glia? If so, does how does reduction of cortex glial numbers independent of FGF signalling, using for example knockdown of String or expression of Decapo, affect the expression of Hh, fasn1 and lsd2 in cortex glia? 6.Can the authors speculate on why and how increased levels of Hh in cortex glia, in the context of FGF activation, inhibit neuroblast cell cycle? Is this a physiological mechanism to limit neuroblast proliferation in the face of increased gliogenesis, or is it simply an indirect result of 'spillover' of excess Hh from cortex glia onto neuroblasts (which are autonomously regulated by Hh and so sensitive to this ligand) by due to increased cortex glia cells? **Minor comments:** -Figure 1C' some lipid droplets are extremely large, is this consistent with previous literature? -Including a profile plot of relative fluorescence intensity in Figure 1C',F',H' to illustrate colocalization of lipidTOX and Hh, would be helpful. -Figure S3A,B quantify Hh protein level and CNS size phenotypes with Hh RNAi. -p.6 include data showing overexpression of Hh does not cause glial overgrowth. -Top of p.14 should be FigS6A-C. -Include quantification of glial overgrowth and lipid droplet phenotypes with HtlACT plus catalase and SOD1 overexpression (Fig. S6D-K). Reviewer #2 (Significance (Required)): The is a novel and very interesting study, well written and the data are very clearly presented. It builds on and adds to the emerging literature on the glial niche and its role in neural stem cell regulation. It will be of great interest to Drosophila neurobiologists but also to the broader field of neural stem cell biology. My expertise is Drosophila neurobiology.

Dear editor

Below is our response to the reviewer’s comments and our experimental plan in addressing these concerns.

Reviewer #1

Major comments:

1.Since Hh RNAi decreases the glial compartment (which slows NB proliferation) and increases the frequency of pH3+ NBs, it is unclear why it would decrease the number of EdU+ NBs (Fig. S3C).

Our experimental data suggests that accompanying glial niche disruption and downregulation of glia-derived signals, NBs are stalled in M phase (we detected an increase in the percentage of pH3+ NBs). As a consequence, less NBs are in G1 and S phase. Therefore, when we conducted a 15-min EdU incorporation, we observed a reduction in EdU incorporation. This NB phenotype (increase in pH3 index and decrease in EdU index) was also observed by Speder and Brand, 2018, when they induced glial niche impairment by inhibiting the PI3K signaling pathway (discussed in P7 of this ms).

To address whether glial-Hh knockdown reduces the ability of NBs to produce progeny, we plan to carry out two experiments:

• We will assess the total number of neurons in the CB by assessing Elav+ neurons.

• We will conduct two EdU pulse-chase experiments. First, we will assess the total number of EdU+ neurons produced within a 4-hr time window (neurons marked with Elav); and the secondly, we will mark the NB lineage (with either nerfin-1-GFP or pros-GFP) and quantify the number of EdU+ neurons produced per lineage during a 4-hr time window.

Together, these experiments should allow us to assess the consequence of glial-Hh knockdown on NB proliferation.

If overexpression of htl[ACT] slows the NB cell cycle (as evidenced by reduced pH3 and EdU positive cells), it unclear why it does not reduce the number of NBs (Fig. 4L).

The number of NBs in the larval CNS is specified at the beginning of post-embryonic neurogenesis, when quiescent NBs re-enter the cell cycle (reviewed by Homem and Knoblich, 2012). Once NBs re-enter the cell cycle, the number of NBs remain constant. NBs undergo asymmetric division to produce one daughter NB and a GMC, which divides once to generate two neurons. With each round of NB-division, the number of NBs remain constant. Therefore, changes in NB cell cycle speed does not alter the overall NB number, only the number of neurons produced.

To clarify this, we will add a schematic depicting NB asymmetric division to Figure 1.

3.What is the justification for presenting the EdU quantifications as an EdU index in which the experimental values are normalized to the average number of positive cells in the control?

EdU index is calculated as number of EdU+ NBs normalised to control EdU+ NBs. The number of EdU+ NBs reflects the NBs that progress through S phase in a 15-min time relative to the control. A similar method was used in Kanai et al., 2018. This method would not be valid only if NB number varied between control and experimental data sets, however, the number of NBs in all our genetic manipulations are not significantly altered relative to their control. We present the quantification of some key manipulations in Reviewer_Figure 1A, B.

As regards to why we normalise to control in each of these experiments, this is because in-vitro EdU incorporation rely on Click-IT chemistry, which is inherently variable due to incubation conditions. To overcome this, we always incubate control and experimental brains in the same tube and imaged them with the same confocal setting, and each experiment is normalised to its control done in parallel. We have now included Table 1 which includes all the raw data from these experiments (Table 1)

In the revised manuscript, we will clarify our methodology in greater detail in the Methods section, and we are happy to include Table 1in the supplementary data.

In many cases, the comparison is to the same w [1118] line so it does not control for a specific genetic backgrounds and yet this method may be obscuring experimental variation present between datasets.

We have used three different controls in our experiments, namely GAL4 or lexA >w1118, or UAS-mcherryRNAi, or UAS-luc. We detect no significant difference in terms of raw EdU+ NB numbers between the controls used in our experiments, as demonstrated below (Reviewer_Figure 1C). In our revised manuscript, we will include a sentence “As UAS-mcherryRNAi or UAS-luc are indistinguishable from the > w1118 control, we have used GAL4 driver > w1118 as control in place of UAS-luc in our results”.

Reviewer_Figure 1. Total NB number and Edu+ NB number quantification

1. A) Hh knockdown or overexpression in glia does not significantly alter NB number compared to control.
2. B) htlACT overexpression in glia does not significantly alter NB number compared to control.
3. C) EdU+ NB number is not significantly different within the controls GAL4 or lexA > w1118, or UAS-mcherryRNAi, or UAS-luc. P-value was obtained performing student t-test in A, B and One-way ANOVA in C.

Likewise, why is glial number presented as a fold-change but NB number is presented as raw counts (e.g. 2D vs S3E)?

Glial number quantification was carried out using Fiji 3D object counter and a plug-in called “DeadEasy Larval Glia” (Forero et al., 2012), where the threshold of detection is dependent on the brightness of Repo staining in each experiment, this data is presented as fold-change, as control and experiment stained in the same tube are compared to each other. We represented this data as fold-change to allow easy comparison between experiments. The raw data is presented in Table 2. NB number is counted manually and is therefore presented as raw counts.

**Minor comments:**

On the top of P.14, "Figure S7A-C" should probably be "Figure S6A-C"

We will correct this.

Reviewer #1 (Significance (Required)):

The cell autonomous regulation of growth and proliferation of neuroblasts in the larval brain have been well-studied, but much less is known about the non-cell autonomous signals. This paper significantly moves forward knowledge in this area by describing multiple steps of a molecular mechanism for glial regulation of the neuroblast cell cycle. These findings would be of interest not only to the study of Drosophila neuroblasts, but also to the broader adult stem cell field.

My expertise is in Drosophila stem cell biology and genetics.

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

**Major comments:**

1.From the data in presented in Fig. 2H-K and Fig. S3C, I am very confused about role of Hh in the non-cell autonomous regulation of neuroblast cell cycle. Both RNAi and overexpression of Hh with Repo-Gal4 cause a reduction in the neuroblast EdU index (Fig. 2H-K and S3C). The authors conclude this section on p.7 saying "Together, our data suggests that high levels of glial Hh expression restricts NB cell cycle progression." This statement is not consistent with data. What is the normal physiological role of Hh if both decreased and increased levels of cortex glial Hh expression reduce neuroblast cell cycle? The discussion of p.15 does not clarify this issue. The model in Fig.7J relates to the role of Hh in the context of cortex glial FGF activation and does not illustrate the normal physiological role of Hh in the regulation of neuroblast cell cycle.

With repo-GAL4>hhRNAi, the cortex glial niche enwrapping NBs is dramatically disrupted, which indirectly alters NB cell cycle progression, indicated by an increase in pH3 index and a decrease in EdU index. From these two pieces of data, it is likely that NBs are stuck in M phase, thus resulting in less NBs in G1 and S phase that are capable to incorporate EdU within a 15-min incubation time window. We will firm up this data with experiments proposed to address concerns of Reviewer 1, Point 1.

Both RNAi and overexpression of Hh with repo-GAL4 causes a reduction in NB EdU index is seemingly contradictory. However, it is consistent with a previous report from Speder and Brand, 2018, where it was shown that that glial niche impairment induced by the PI3K pathway inhibition also causes a similar NB phenotype (an increase in pH3 index and a decrease in EdU incorporation). Furthermore, with repo-GAL4>htlDN, which caused a similar glia niche impairment (data not shown), we observed a similar phenotype (an increase in pH3 index and a slight decrease in EdU incorporation). Therefore, we concluded that the NB cell cycle progression defects is due to a general cortex glial niche disruption rather than a direct effect of Hh inhibition on NBs. We are happy to include the repo-GAL4>htlDN data in the supplementary data if required.

With regards to the physiological role of Hh, we can only conclude from the data at hand that Hh is required for the development of cortex glial niche, which is required to maintain NB activities. In terms of how glial niche impairment impedes NB cell cycle progression, we observed that without a proper niche chamber, NBs cluster together instead of residing in separate niches (Figure 2F-G). Therefore, it is possible that the localization of other cell types (i.e. GMCs and neurons) are also altered as a result of NB clustering, which can potentially affect the NB cell cycle. While these questions will be interesting to explore in the future, they are beyond the scope of this current study.

In contrast, we robustly showed Hh signals, when overexpressed in glial niche, were capable of making contact with NBs (Figure 7C-C’) and triggering a slow-down of NB S-phase progression. Therefore, it is fair to conclude that “high levels of glial Hh expression restricts NB cell cycle progression”.

In the revised manuscript, we will discuss these findings in greater detail.

2.P.8 "Analysis of the total glial cell number indicates overexpression of htlACT, but not InRwt or EgfrACT, led to an increase in the number of cortex glial cells (Figure 4E-G, I-K)." This statement is confusing as Repo staining was used to quantify total glial numbers (including perineural, sub-perineural and cortex glia) but these data are then taken to represent and increase specifically in cortex glia. This should be clarified.

We thank the reviewer for picking this up. Our intention was to quantify the number of cortex glia cells in glial-specific htlACT, InRwt and EgfrACT manipulations. However, two reported cortex glial antibodies (PntP2 from Avet-Rochex et al., 2012 and SoxN described in Read, 2018), showed unspecific labelling of other cell types (Reviewer_Figure 2, arrows, neurons and NBs). As an alternative, we quantified the total glial cell number (Repo+) in htlACT, InRwt or EgfrACT overexpressed using a cortex glial driver (NP2222-GAL4). We expect that the alterations in glial cell number would be primarily attributed to cortex glial-specific gene manipulation. We agree that we should say that “overexpression of htlACT, but not InRwt or EgfrACT, led to an increase in the number of glial cell”.

In the revised manuscript, we will clarify this in the results section.

Reviewer_Figure 2: PntP2 staining in the larval CNS.

A-B) Representative images showing that PntP2 antibody stains cortex glial cells (marked by NP2222-GAL4>mGFP, yellow arrows), NBs (white arrows) and neurons (blue arrows). B) is the zoomed in image of A). Scale bar = 50 mm.

It should be mentioned on p.8 that the data in Fig.4A-K reproduce the findings of Avet-Rochex et al., 2012 and Read et al., 2009.

We will correct this.

4.Figure 6F. Presumably due to the increase in glia cell number and dramatic increase in glial cell volume, any gene that is specific to, or enriched in, cortex glia will have increased expression levels in RepoGal4>htlACT larval CNS. Can the authors provide evidence that the increase in the expression of these genes is specific to FGF transcriptional regulation and not just a relative increase in the levels of these genes due to an increase in cortex glia as proportion of total CNS volume? Is there any evidence that Hh, fasn1 and lsd2 are direct transcriptional targets of FGF signalling in glia?

We agree that FGF activation causes a dramatic increase in glial cell number, thus will cause a relative increase in the level of hh, fasn1 and lsd2s. However, with RT-qPCR, the same amounts of total RNA (1μg) were extracted from control vs repo-GAL4> htlACT and reverse transcribed into cDNA for qPCR. Therefore, the mRNA level described in Figure 6 F are already normalized to the total amount of genetic material.

In the literature, it is not reported that hh, fasn1 and lsd2 are direct transcriptional targets of FGF signalling. However, lipid metabolism rewiring is well known as a hallmark of glioblastoma. For example, high levels of FASN has been linked with high grade glioblastoma (Grube et al., 2014). Furthermore, FGF signalling has also been shown to modulate lipid metabolism and alter the transcription of the Lsd-2 homologue called Plin2 in a mouse model (Ye et al., 2016).

To figure out whether hh, fasn1 and lsd2 are direct transcriptional targets of FGF signalling. we will have to first find out which TFs are altered in the glia upon altered FGF signalling via cortex glia specific RNA-seq, and then conduct DamID to identify their target genes. This would be interesting to follow-up but is however beyond the scope this current study.

We will add a section on this in the discussion section of the revised ms.

FGF signalling has been shown to be necessary and sufficient for cortex glial proliferation. So does knockdown of Htl, or expression of dominant negative Htl, cause a reduction in Hh, fasn1 and lsd2 expression in cortex glia?

In response to glial htlDN overexpression, we observed a significant reduction in total glial number and overall Hh expression. However, RT-qPCR showed that mRNA levels of hh, fasn1 or lsd-2 were not altered upon htlDNoverexpression (Reviewer_Figure 3).

This data will be included in the supplementary data in the revised ms.

Reviewer_Figure 3. Glial htlDN overexpression doesn’t alter the expression of hh, fasn1 and lsd2. The mRNA levels of hh, fasn1 and lsd2 are normalized to the reference gene rpl32.

Continued: If so, how does reduction of cortex glial numbers independent of FGF signalling, using for example knockdown of String or expression of Decapo, affect the expression of Hh, fasn1 and lsd2 in cortex glia?

To address this question, we plan to assess the expression levels of hh, fasn1 and lsd-2 using glia specific expression of an inhibitor of the PI3K (delta p60), which has been shown by Speder and Brand, 2018 to cause a reduction in cortex glial number. We will also ascertain whether Decapo overexpression causes cortex glial niche impairment. If so, we will also assess the expression levels of hh, fasn1 and lsd-2 in this setting.

6.Can the authors speculate on why and how increased levels of Hh in cortex glia, in the context of FGF activation, inhibit neuroblast cell cycle? Is this a physiological mechanism to limit neuroblast proliferation in the face of increased gliogenesis, or is it simply an indirect result of 'spillover' of excess Hh from cortex glia onto neuroblasts (which are autonomously regulated by Hh and so sensitive to this ligand) by due to increased cortex glia cells?

We favour the model that excess Hh in the glia compartment “spills over” to reduce NB proliferation, which are autonomously regulated by Hh and therefore are sensitive to this ligand. We can add this to the discussion.

**Minor comments:**

-Figure 1C' some lipid droplets are extremely large, is this consistent with previous literature?

These large lipid droplets are caused by lipid droplet fusion due to the use of detergent in this experiment. When we perform antibody staining together with lipid droplet staining, PBST detergent is required for antibody staining to work. However, this created the artefact of large lipid droplets, due to lipid droplet fusion. This has previously been reported by Bailey et al., 2015, and we have explained this in P19 of the Method section.

-Including a profile plot of relative fluorescence intensity in Figure 1C',F',H' to illustrate colocalization of lipidTOX and Hh, would be helpful.

We will include this in the revised ms.

-Figure S3A,B quantify Hh protein level and CNS size phenotypes with Hh RNAi.

We will include this in the revised ms.

-p.6 include data showing overexpression of Hh does not cause glial overgrowth.

We will include this in the revised ms.

-Top of p.14 should be FigS6A-C.

We will correct this.

-Include quantification of glial overgrowth and lipid droplet phenotypes with HtlACT plus catalase and SOD1 overexpression (Fig. S6D-K).

We will include this in the revised ms.

Reviewer #2 (Significance (Required)):

The is a novel and very interesting study, well written and the data are very clearly presented. It builds on and adds to the emerging literature on the glial niche and its role in neural stem cell regulation. It will be of great interest to Drosophila neurobiologists but also to the broader field of neural stem cell biology.

My expertise is Drosophila neurobiology.

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Table 1. EdU+ NB numbers for each genotype described in each Figure

Figure

Genotype

EdU incubation time

Average EdU+ NB number

SEM

Number of samples

Figure 2J

repo-GAL4>w1118

15 min

66.63

1.79

16

Figure 2J

repo-GAL4>UAS-hh

15 min

57.35

1.35

20

Figure 2K

NP2222-GAL4>w1118

15 min

67.91

1.44

11

Figure 2K

NP2222-GAL4>UAS-hh

15 min

60.79

0.79

14

Figure 2P

dnab-GAL4>w1118

15 min

70.5

1.44

12

Figure 2P

dnab-GAL4>ciACT

15 min

60.1

1.48

10

Figure S3C

repo-GAL4>dcr2; mcherryRi

10 min

57.42

0.63

12

Figure S3C

repo-GAL4>dcr2; hhRi43255

10 min

48.56

2.65

9

Figure 3K

NP2222-GAL4>w1118

The same dataset as Figure 2K

Figure 3K

NP2222-GAL4>UAS-hh

Figure 3K

NP2222-GAL4>UAS-hh; mcherryRi

15 min

57.44

1.41

16

Figure 3K

NP2222-GAL4>UAS-hh; lsdRi34617

15 min

63.36

1.34

14

Figure 3K

NP2222-GAL4>UAS-hh; mcherryRi

15 min

58.83

2.61

6

Figure 3K

NP2222-GAL4>UAS-hh; lsdRi32846

15 min

64.5

1.2

14

Figure 5E

repo-GAL4>w1118

15 min

71.6

1.28

15

Figure 5E

repo-GAL4>UAS-htlACT

15 min

56

1.59

14

Figure 5E

NP2222-GAL4>w1118

15 min

70.2

1.58

10

Figure 5E

NP2222-GAL4>UAS-htlACT

15 min

54.75

1.24

16

Figure 6G

NP2222-GAL4>w1118

The same dataset as Figure 5E

Figure 6G

NP2222-GAL4>UAS-htlACT

Figure 6G

NP2222-GAL4>UAS-htlACT;mcherryRi

15 min

60

1.24

7

Figure 6G

NP2222-GAL4>UAS-htlACT;hhRi43255

15 min

67.17

1.13

12

Figure 6G

NP2222-GAL4>UAS-htlACT;mcherryRi

15 min

59.29

1.79

14

Figure 6G

NP2222-GAL4>UAS-htlACT;hhRi25794

15 min

68.55

1.68

11

Figure 6H

dnab-GAL4>mcherryRi

10 min

49.13

1.6

8

Figure 6H

dnab-GAL4>ciRi2125-R2

10 min

56.54

1.27

13

Figure 6H

repo-lexA>w1118

15 min

68.5

1.1

10

Figure 6H

repo-lexA>lexAop-htlACT

15 min

55.7

2.15

10

Figure 6H

repo-lexA>lexAop-htlACT; GFPRi

15 min

52

1.58

30

Figure 6H

repo-lexA>lexAop-htlACT; ciRiHMJ23860

15 min

62.4

1.79

15

Figure 6H

repo-lexA>lexAop-htlACT; GFPRi

15 min

56.33

1.49

12

Figure 6H

repo-lexA>lexAop-htlACT; ciRi2125-R2

15 min

62.86

1.81

7

Figure 6J

NP2222-GAL4>w1118

The same dataset as Figure 5E

Figure 6J

NP2222-GAL4>UAS-htlACT

Figure 6J

NP2222-GAL4>UAS-htlACT;mcherryRi

15 min

58.64

0.99

14

Figure 6J

NP2222-GAL4>UAS-htlACT;fasn1Ri3523R2

15 min

65

2.41

9

Figure 6J

NP2222-GAL4>UAS-htlACT;mcherryRi

The same dataset as Figure 6G control of NP2222-GAL4>UAS-htlACT;hhRi25794

Figure 6J

NP2222-GAL4>UAS-htlACT;lsd2Rikk102269

15 min

68.13

1.08

8

Figure S5H

NP2222-GAL4>mcherryRi

15 min

66.4

1.71

10

Figure S5H

NP2222-GAL4>fasn1Ri3523R6

15 min

65.5

1.38

10

Figure S5H

NP2222-GAL4>mcherryRi

15 min

66.4

1.13

15

Figure S5H

NP2222-GAL4>lsd2Rikk102269

15 min

64.2

0.94

10

Figure S5H

NP2222-GAL4>UAS-luc

15 min

65

1.07

10

Figure S5H

NP2222-GAL4>UAS-lsd2

15 min

64.9

1.51

10

Figure S5I

NP2222-GAL4>w1118

The same dataset as Figure 5E

Figure S5I

NP2222-GAL4>UAS-htlACT

Figure S5I

NP2222-GAL4>UAS-htlACT;mcherryRi

15 min

57.93

0.9

14

Figure S5I

NP2222-GAL4>UAS-htlACT;fasn1Ri3523R6

15 min

63.79

1.25

14

Figure S5I

NP2222-GAL4>UAS-htlACT;mcherryRi

15 min

50.25

2.52

8

Figure S5I

NP2222-GAL4>UAS-htlACT;lsd2Ri32846

15 min

59.3

1.2

10

Figure 7B

NP2222-GAL4>mcherryRi

15 min

65

0.93

10

Figure 7B

NP2222-GAL4>raspRi11495R2

15 min

65.13

1.29

15

Figure 7B

NP2222-GAL4>w1118

The same dataset as Figure 5E

Figure 7B

NP2222-GAL4>UAS-htlACT

Figure 7B

NP2222-GAL4>UAS-htlACT;mcherryRi

15 min

58.33

1.06

18

Figure 7B

NP2222-GAL4>UAS-htlACT;raspRi11495R1

15 min

63.95

1.05

21

Figure 7B

NP2222-GAL4>UAS-htlACT;mcherryRi

15 min

59.04

1.019

26

Figure 7B

NP2222-GAL4>UAS-htlACT;raspRi11495R2

15 min

63.07

0.92

29

Figure 7D

NP2222-GAL4>w1118

15 min

69.46

1.02

13

Figure 7D

NP2222-GAL4>UAS-hh.N.EGFP

15 min

52.25

1.9

12

Figure 7F

repo-GAL4>UAS-hh.N.EGFP;mcherryRi

15 min

54.4

1.18

15

Figure 7D

repo-GAL4>UAS-hh.N.EGFP;fasn1Ri3523R2

15 min

65.69

1.43

13

Figure S6L

NP2222-GAL4>UAS-htlACT; UAS-LacZ

15 min

59.17

1.18

12

Figure S6L

NP2222-GAL4>UAS-htlACT; UAS-Cat.A

15 min

64

1.31

12

Figure S6L

NP2222-GAL4>UAS-htlACT; UAS-LacZ

15 min

53.6

2.32

10

Figure S6L

NP2222-GAL4>UAS-htlACT; UAS-Sod.1

15 min

62.7

1.76

10

Table 2. Raw data on glial number

Figure

Genotype

Average Repo+glial number

SEM

Number of samples

Figure 2D

repo-GAL4>dcr2; mcherryRi

843

44.29

7

Figure 2D

repo-GAL4>dcr2; hhRi43255

666.5

46.77

8

Figure 4K

NP2222-GAL4>w1118

1165

20.55

10

Figure 4K

NP2222-GAL4>htlACT

2325

107.5

10

Figure 4K

NP2222-GAL4>InRwt

1189

85.92

10

Figure 4K

wrapper-GAL4>w1118

1305

51.78

7

Figure 4K

wrapper-GAL4>EgfrACT

1192

38.16

12

Reference:

Avet-Rochex, A., Kaul, A.K., Gatt, A.P., McNeill, H., and Bateman, J.M. (2012). Concerted control of gliogenesis by InR/TOR and FGF signalling in the Drosophila post-embryonic brain. Development 139, 2763-2772.

Bailey, A.P., Koster, G., Guillermier, C., Hirst, E.M., MacRae, J.I., Lechene, C.P., Postle, A.D., and Gould, A.P. (2015). Antioxidant Role for Lipid Droplets in a Stem Cell Niche of Drosophila. Cell 163, 340-353.

Forero, M.G., Kato, K., and Hidalgo, A. (2012). Automatic cell counting in vivo in the larval nervous system of Drosophila. J Microsc 246, 202-212.

Grube, S., Dunisch, P., Freitag, D., Klausnitzer, M., Sakr, Y., Walter, J., Kalff, R., and Ewald, C. (2014). Overexpression of fatty acid synthase in human gliomas correlates with the WHO tumor grade and inhibition with Orlistat reduces cell viability and triggers apoptosis. J Neurooncol 118, 277-287.

Homem, C.C., and Knoblich, J.A. (2012). Drosophila neuroblasts: a model for stem cell biology. Development 139, 4297-4310.

Kanai, M.I., Kim, M.J., Akiyama, T., Takemura, M., Wharton, K., O'Connor, M.B., and Nakato, H. (2018). Regulation of neuroblast proliferation by surface glia in the Drosophila larval brain. Sci Rep 8, 3730.

Read, R.D. (2018). Pvr receptor tyrosine kinase signaling promotes post-embryonic morphogenesis, and survival of glia and neural progenitor cells in Drosophila. Development 145.

Speder, P., and Brand, A.H. (2018). Systemic and local cues drive neural stem cell niche remodelling during neurogenesis in Drosophila. Elife 7.

Ye, M., Lu, W., Wang, X., Wang, C., Abbruzzese, J.L., Liang, G., Li, X., and Luo, Y. (2016). FGF21-FGFR1 Coordinates Phospholipid Homeostasis, Lipid Droplet Function, and ER Stress in Obesity. Endocrinology 157, 4754-4769.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The study by Dong et al., investigates the role of Hedgehog in the glial niche during larval neurogenesis in Drosophila. The authors describe the expression of Hh in cortex glia and its association with lipid droplets. They show that Hh expression in cortex glia is required for cortex glial proliferation, cell autonomously, and for maintenance of the normal cell cycle in neuroblasts. They go on to use a well characterised Drosophila glioma model, activation of FGF signalling, to investigate the requirement for Hh during cortex glial overgrowth. They show that FGF-activated cortex glial overproliferation requires Hh for modulation of neuroblast cell cycle, although Hh does not regulate cortex glial proliferation in this context. Finally, they show that inhibition of lipid modification of Hh rescues the neuroblast proliferation cell cycle defect caused by FGF activation in cortex glia.

Major comments:

1.From the data in presented in Fig. 2H-K and Fig. S3C, I am very confused about role of Hh in the non-cell autonomous regulation of neuroblast cell cycle. Both RNAi and overexpression of Hh with Repo-Gal4 cause a reduction in the neuroblast EdU index (Fig. 2H-K and S3C). The authors conclude this section on p.7 saying "Together, our data suggests that high levels of glial Hh expression restricts NB cell cycle progression." This statement is not consistent with data. What is the normal physiological role of Hh if both decreased and increased levels of cortex glial Hh expression reduce neuroblast cell cycle? The discussion of p.15 does not clarify this issue. The model in Fig.7J relates to the role of Hh in the context of cortex glial FGF activation and does not illustrate the normal physiological role of Hh in the regulation of neuroblast cell cycle.

2.P.8 "Analysis of the total glial cell number indicates overexpression of htlACT, but not InRwt or EgfrACT, led to an increase in the number of cortex glial cells (Figure 4E-G, I-K)." This statement is confusing as Repo staining was used to quantify total glial numbers (including perineural, sub-perineural and cortex glia) but these data are then taken to represent and increase specifically in cortex glia. This should be clarified.

3.It should be mentioned on p.8 that the data in Fig.4A-K reproduce the findings of Avet-Rochex et al., 2012 and Read et al., 2009.

4.Figure 6F. Presumably due to the increase in glia cell number and dramatic increase in glial cell volume, any gene that is specific to, or enriched in, cortex glia will have increased expression levels in RepoGal4>htlACT larval CNS. Can the authors provide evidence that the increase in the expression of these genes is specific to FGF transcriptional regulation and not just a relative increase in the levels of these genes due to an increase in cortex glia as proportion of total CNS volume? Is there any evidence that Hh, fasn1 and lsd2 are direct transcriptional targets of FGF signalling in glia?

5.FGF signalling has been shown to be necessary and sufficient for cortex glial proliferation. So does knockdown of Htl, or expression of dominant negative Htl, cause a reduction in Hh, fasn1 and lsd2 expression in cortex glia? If so, does how does reduction of cortex glial numbers independent of FGF signalling, using for example knockdown of String or expression of Decapo, affect the expression of Hh, fasn1 and lsd2 in cortex glia?

6.Can the authors speculate on why and how increased levels of Hh in cortex glia, in the context of FGF activation, inhibit neuroblast cell cycle? Is this a physiological mechanism to limit neuroblast proliferation in the face of increased gliogenesis, or is it simply an indirect result of 'spillover' of excess Hh from cortex glia onto neuroblasts (which are autonomously regulated by Hh and so sensitive to this ligand) by due to increased cortex glia cells?

Minor comments:

-Figure 1C' some lipid droplets are extremely large, is this consistent with previous literature?

-Including a profile plot of relative fluorescence intensity in Figure 1C',F',H' to illustrate colocalization of lipidTOX and Hh, would be helpful.

-Figure S3A,B quantify Hh protein level and CNS size phenotypes with Hh RNAi.

-p.6 include data showing overexpression of Hh does not cause glial overgrowth.

-Top of p.14 should be FigS6A-C.

-Include quantification of glial overgrowth and lipid droplet phenotypes with HtlACT plus catalase and SOD1 overexpression (Fig. S6D-K).

Significance

The is a novel and very interesting study, well written and the data are very clearly presented. It builds on and adds to the emerging literature on the glial niche and its role in neural stem cell regulation. It will be of great interest to Drosophila neurobiologists but also to the broader field of neural stem cell biology.

My expertise is Drosophila neurobiology.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study, the authors investigate the role of hedgehog signaling and lipid metabolism in the neural stem cell niche of the Drosophila larvae. They demonstrate that Hedgehog localizes to lipid droplets in glial cells and show that Hh is necessary but not sufficient for elaboration of glial membranes and normal rates of glial proliferation during development. In addition, they provide an extensive set of results in support of a model that FGF signaling functions upstream of lipid metabolism and hh in glial cells as well as a parallel ROS mediated pathway in glial cells to promote neuroblast proliferation. In general, the results provide strong support for the conclusions. Specifically, the approaches are sound, the images clearly demonstrate the phenotypes described, and the effects are quantified and tested for statistical significance.

Major comments:

1.Since Hh RNAi decreases the glial compartment (which slows NB proliferation) and increases the frequency of pH3+ NBs, it is unclear why it would decrease the number of EdU+ NBs (Fig. S3C).

2.If overexpression of htl[ACT] slows the NB cell cycle (as evidenced by reduced pH3 and EdU positive cells), it unclear why it does not reduce the number of NBs (Fig. 4L).

3.What is the justification for presenting the EdU quantifications as an EdU index in which the experimental values are normalized to the average number of positive cells in the control? In many cases, the comparison is to the same w[1118] line so it does not control for a specific genetic backgrounds and yet this method may be obscuring experimental variation present between datasets. Likewise, why is glial number presented as a fold-change but NB number is presented as raw counts (e.g. 2D vs S3E)?

Minor comments:

On the top of P.14, "Figure S7A-C" should probably be "Figure S6A-C"

Significance

The cell autonomous regulation of growth and proliferation of neuroblasts in the larval brain have been well-studied, but much less is known about the non-cell autonomous signals. This paper significantly moves forward knowledge in this area by describing multiple steps of a molecular mechanism for glial regulation of the neuroblast cell cycle. These findings would be of interest not only to the study of Drosophila neuroblasts, but also to the broader adult stem cell field.

My expertise is in Drosophila stem cell biology and genetics.

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Reply to the reviewers

We thank the three reviewers for providing valuable feedback on our original manuscript. A point-by-point response to all of these comments is provided below. [Note that figures are not added in-line because of text-only limitations.]

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

The submitted manuscript entitled 'Predicting cell health phenotypes using image-based morphology profiling' (RC-2020-00394) by Way et al. presents a set of seven dyes/staining (as two separate panels) to microscopically screen cell viability. For automatic classification a training/test set of 119 CRISPR (approximately 2 sgRNAs per gene) perturbations on 3 cancer cell lines were generated (lung A549, ovarian ES2, lung HCC44). After segmentation of cell nuclei a set of morphological cell measurements were extracted from each perturbation (total 952 features). The nature of these feature spanning cell cycle and viability phenotypes, enabled the authors to define 70 different phenotype classes, which are used to model a classifier by elastic linear regression. Specific definitions (cell cycle and ROS) were partly predicted/validated in an independent existing image data set (Drug Repurposing Hub project). The data is available as web-based application/visualization and the supplementary method is well described.

We thank the reviewer for their constructive comments and helpful feedback.

There is one subtle point that is worth raising given this description: The images we use to measure the cell cycle and viability phenotypes (two different staining panels in the Cell Health assays) are not the same images we use to extract morphology measurements (Cell Painting assay). This lack of connection, which is based on a light wavelength limitation present in all microscopes that limits the number of stains in a single assay, prevents us from developing a method that analyzes the same cells across the three assays. This distinction will become important later in the review, and we have made specific changes in the manuscript to increase clarity.

**Major concerns:**

(1)The only fundamental argument of this manuscript not to apply state-of-the-art deep learning (DL) machine-learning (mentioned in McCain et al. 2018), which does not require segmentation, feature extraction, abstraction, manual gating is the 'interpretability' of the predictions. However, performance, precision, scalability (by modern GPUs) with DL should clearly outperform 'manual' regression models. All recent machine vision benchmarks in microscopy confirm this, but also clearly shows 'real world' translational applications, e.g.

https://www.nature.com/articles/s43018-020-0085-8,

https://www.biorxiv.org/content/10.1101/2020.07.02.183814v1.full.pdf,

In other words, the presented methodology is not compared to DL, and is not convincing in terms of interpretability benefits.

(We’ve copied a similar critique from __Significance sectio__n from Reviewer #1 in order to reduce redundancy) The author/co-authors have been instrumental/pioneered with their past work on cell-based image processing (CellProfiler software), but the presented methodology is simply outdated. Therefore, a revision towards a comparison and benchmarking with DL will also not help.

Ref (DL with MIL): https://academic.oup.com/bioinformatics/article/32/12/i52/2288769

We agree that deep learning approaches are exciting; much of our laboratory’s work focuses on their application (see https://doi.org/10.1073/pnas.2001227117, https://doi.org/10.1038/s41592-019-0612-7; https://doi.org/10.1002/cyto.a.23863, https://doi.org/10.1109/CVPR.2018.00970), and we agree that they are likely to outperform simpler regression models trained using so-called hand-engineered features. We thank the reviewer for highlighting our failure to accurately and fully describe our rationale.

We intentionally did not use deep learning for this problem given (a) data limitations (b) the primary goal of the manuscript, which is to demonstrate feasibility.

Data limitations. There is no mechanism to link the cells of the assays (Cell Health and Cell Painting) together, which greatly reduces the available sample size. In the two referenced manuscripts, which each propose an exciting approach, the dataset is much larger (~17,000 and ~1,000 images respectively). Our dataset is only 357 perturbations that can only be linked between assays at the perturbation level rather than a single-cell level. Therefore, a deep learning approach is likely to produce models that don’t generalize to other datasets. Furthermore, reviewer 3 commented in favor of the approach we presented: “Using elastic net regression models is well-suited to the problem due to the low number of observations.”

Primary goal of the manuscript is to demonstrate feasibility. In addition, the primary goal of the manuscript is to add cell health annotations as functional readouts to perturbations. Our aim was to demonstrate feasibility of predicting cell health states, not to optimize performance. Optimizing performance would require collecting much more data, or developing new deep learning or data collection methods to account for the lack of matched single cell readouts.

To make this rationale more clear and concise, we have made the following changes in the manuscript:

In the first paragraph of page 3, we make some minor contextual updates (”To demonstrate proof of concept, we collected a small pilot dataset of 119 CRISPR knockout perturbations…”) and replaced “We used simple machine learning methods, which are relatively easy to interpret compared to deep learning” with:

We used simple machine learning methods instead of a deep learning approach because of our limited sample size of 119 perturbations and the inability to increase the sample size by linking single cell measurements across assays.

We have also amended the Conclusions section to emphasize our primary goal and note possible deep learning extensions as future directions. The Conclusions now reads:

We have demonstrated feasibility that information in Cell Painting images can predict many different Cell Health indicators even when trained on a small dataset. The results motivate collecting larger datasets for training, with more perturbations and multiple cell lines. These new datasets would enable the development of more expressive models, based on deep learning, that can be applied to single cells. Including orthogonal imaging markers of CRISPR infection would also enable us to isolate cells with expected morphologies. More data and better models would improve the performance and generalizability of Cell Health models and enable annotation of new and existing large-scale Cell Painting datasets with important mechanisms of cell health and toxicity.

(2)One aforementioned point of the methodology is cryptically/not described: Why it should be less expensive compared with other (which?) approaches (see introduction)?

We thank the reviewer for bringing up this point. We believe that part of this confusion stems from a slight misunderstanding about how images from the three assays (two Cell Health and one Cell Painting) are collected. The Cell Health assays are two distinct panels of targeted reagents that are separately prepared as two physically distinct assays. The Cell Painting assay is already an established assay used by many labs and companies around the world to mark cell morphology in an unbiased and relatively cheap way. We are comparing the expenses between the two Cell Health assays vs. the Cell Painting assay.

We believe that this misunderstanding likely results from our somewhat cryptic and inconsistent language when describing the Cell Health assays in the abstract and introduction. We’ve updated the third sentence of the abstract from “We developed two customized microscopy assays that use seven reagents to measure 70 specific cell health phenotypes...” to now read:

We developed two customized microscopy assays, one using four targeted reagents and the other three targeted reagents, to collectively measure 70 specific cell health phenotypes including proliferation, apoptosis, reactive oxygen species (ROS), DNA damage, and cell cycle stage.

For consistency, we have also updated the penultimate paragraph in the introduction to now read:

To do this, we first developed two customized microscopy assays, which collectively report on 70 different cell health indicators via a total of seven reagents applied in two reagent panels. Collectively, we call these assays “Cell Health”.

With these clarifications in mind, we believe that the question of comparing monetary costs is more clear. We are comparing the costs of the targeted reagents in the two Cell Health assays to the unbiased reagents in the single Cell Painting assay. We’ve also modified the last two sentences in the first paragraph of the introduction to strengthen the connection between Cell Health assays, targeted reagents, and high cost:

Cell health is normally assessed by eye or measured by specifically targeted reagents, which are either focused on a single Cell Health parameter (ATP assays) or multiple, in combination, via FACS-based or image-based analyses, which involves a manual gating approach, complicated staining procedures, and significant reagent cost. These traditional approaches limit the ability to scale to large perturbation libraries such as candidate compounds in academic and pharmaceutical screening centers.

(3)Generalizability and/or training data size is essential for any model-based classification, but not evaluated or validated in the current manuscript. The independent validation on a A549 cell line only data might be not sufficient/convincing.

We separately address the two distinct points raised by the reviewer of 1) generalizability and 2) training data size:

Generalizability We agree that any model-based classification must demonstrate generalizability. For this reason, we have taken careful consideration to assess the generalizability of all 70 models in two contexts. First, we assessed model performance in a single held out test set (15% of all data). All results we report in the main text (e.g. Figure 2) report performance on this test set. We see high performance in many (but not all) models, and we observe much better model performance compared to a negative control baseline (New Supplementary Figure S5). High performance in the test set indicates that, for some cell health indicators, the models generalize well.

Second, we also demonstrate that these models generalize to data from an entirely different experiment using a fundamentally different perturbation (CRISPR vs. drug compounds). We demonstrate generalizability to this external validation data in four different ways: 1) Validating a relatively simple model (“Number of Live Cells”) with an orthogonal viability readout from the PRISM assay (barcoding-based cell viability; updated Figure 4); 2) Demonstrating that proteasome inhibitors, which are known to produce reactive oxygen species, are predicted to do so; 3) Demonstrating that PLK inhibitors, which are known to reduce entry to G1, show a robust dose response in the "G1 Cell Count" model; and 4) Demonstrating that aurora kinase and tubulin inhibitors are predicted to induce high DNA damage (gH2AX) in G1 cells. These two drug classes are known to cause “mitotic slippage” and double stranded DNA breaks. The fourth example was added in response to a comment by reviewer 3.

We’ve also added a series of enrichment tests, as described in the following new text:

We also chose to validate three additional models: ROS, G1 cell count, and Number of gH2AX spots in G1 cells. We observed that the two proteasome inhibitors (bortezomib and MG-132) in the Drug Repurposing Hub set yielded high ROS predictions (OR = 76.7; p -15) (Figure 4C). Proteasome inhibitors are known to induce ROS (Han and Park, 2010; Ling et al., 2003). As well, PLK inhibitors yielded low G1 cell counts (OR = 0.035; p = 3.9 x 10-8) (Figure 4C). The PLK inhibitor HM-214 showed an appropriate dose response (Figure 4D). PLK inhibitors block mitotic progression, thus reducing entry into the G1 cell cycle phase (Lee et al., 2014). Lastly, we observed that aurora kinase and tubulin inhibitors were enriched for high Number of gH2AX spots in G1 cells predictions (OR = 11.3; p -15) (Figure 4E). In particular, we observed a strong dose response for the aurora kinase inhibitor barasertib (AZD1152) (Figure 4F). Aurora kinase and tubulin inhibitors cause prolonged mitotic arrest, which can lead to mitotic slippage, G1 arrest, DNA damage, and senescence (Orth et al. 2011; Cheng and Crasta 2017; Tsuda et al. 2017).

The updated methods section describing our approach to assess generalizability perform the enrichment tests now states:

Assessing generalizability of cell health models applied to Drug Repurposing Hub data

We used our cell health webapp (https://broad.io/cell-health-app) to identify compounds with high predictions for three models with high or intermediate performance: ROS, Number of G1 cells, and Number of gH2AX spots in G1 cells. For each model, we identified classes of compounds with consistently high scores, then tested for statistical enrichment: for proteasome inhibitors in the ROS model, PLK inhibitors in the Number of G1 cells model, and aurora kinase and tubulin inhibitors in the Number of gH2AX spots in G1 cells model. We used one-sided Fisher’s exact tests to quantify differences in expected proportions between high and low model predictions. For each case, we determined high and low predictions based on the 50% quantile threshold for each model independently.

We acknowledge that prospectively making predictions and measuring Cell Health readouts directly in a new experiment would be more convincing, but we note that our existing assessment of generalizability in an external experiment is already unusual in machine learning publications. Additionally and unfortunately, collecting a second validation dataset for this manuscript is not currently feasible given experiments backlogged from COVID.

1. Training data size

We also agree that a more comprehensive analysis on training data size would be an important indicator of model limitations. Therefore, we performed a sample titration analysis in which we randomly dropped samples from the training procedure, and tracked performance of the held out test set. We add the following figure, figure legend, and results text to describe and interpret the results.

Supplementary Figure S13: Dropping samples from training reduces test set model performance in high, mid, and low performing models. We determined model performance stratification by taking the top third, mid third, and bottom third of test set performance when using all data. We performed the sample titration analysis with 10 different random seeds and visualized the median test set performance for each model.

We updated the results section to introduce and discuss this result:

Lastly, we performed a sample size titration analysis in which we randomly removed a decreasing amount of samples from training. For the high and mid performing models, we observed a consistent performance drop, suggesting that increasing sample size would result in better overall performance (Supplementary Figure 13).

Finally, the updated methods section describing our sample titration analysis now reads:

Machine learning robustness: Investigating the impact of sample size

We performed an analysis in which we randomly dropped an increasing amount of samples from the training set before model training. After dropping the predefined number of samples, we retrained all 70 cell health models and assessed performance on the original holdout test set. We performed this procedure ten times with ten unique random seeds to mirror a more realistic scenario of new data collection and to reduce the impact of outlier samples on model training.

All software updates introducing this analysis can be viewed at https://github.com/broadinstitute/cell-health/pull/143

**Minor concerns:**

(1)Highest test performance comprises that precision is mainly driven by cell cycle/count and live status and could be probably derived from DRAQ7 (Fig. 2) and DNA granularity (Fig. 3, bottom right) and would argue for rigid feature selection across channels and features.

We believe that clarifying the confusion between the two Cell Health assays we developed and the well-established Cell Painting assay addresses part of this concern. The DRAQ7 dye marks dead cells, and is measured in Cell Health. In other words, readouts from this reagent are what we aim to predict, not what we use for training. Indeed, DRAQ7-based phenotypes are among the top predicted models, which is a result we present in Supplementary Figure S7 - this figure uncovers which Cell Health phenotypes are more easily predicted by Cell Painting.

The DNA granularity morphology measurements are collected from the Cell Painting assay and thus are available for training, and, as noted by the reviewer, encode a high proportion of signal in predicting the various cell health phenotypes. In our most common processing workflows for other projects, we do apply a rigid feature selection pipeline to all Cell Painting profiles before analysis, but we do not do this in this analysis since we were using a model with a sparsity-inducing penalty (elastic net).

To directly answer the question of how channels and feature groups influence model performance, we’ve performed a systematic experiment removing different channel, compartment, and feature groups and retraining all models with the specific group dropped. We now include the following supplementary figure:

Supplementary Figure S12: Systematically removing classes of features has little impact on most models’ performance. We retrained all 70 cell health models after dropping features associated with specific (a) feature groups, (b) channels, and (c) compartments. Each dot is one model (predictor), and the performance difference between the original model and the retrained model after dropping features is shown on the x axis. Any positive change indicates that the models got worse after dropping the feature group. (d) Individual model differences in performance after dropping features. Each dot is one class of features removed (as in a-c).

Additionally, we updated the results section to introduce and discuss this result:

We also performed a systematic feature removal analysis, in which we retrained cell health models after dropping features that are measured from specific groups, compartments, and channels. We observed that most models were robust to dropping entire feature classes during training (Supplementary Figure 12). This result demonstrates that many Cell Painting features are highly correlated, which might permit prediction “rescue” even if the directly implicated morphology features are not measured. Because of this, we urge caution when generating hypotheses regarding causal relationships between readouts and individual Cell Painting features.

And we add the following to the methods section:

Machine learning robustness: Systematically removing feature classes

We performed an analysis in which we systematically dropped features measured in specific compartments (Nuclei, Cells, and Cytoplasm), specific channels (RNA, Mito, ER, DNA, AGP), and specific feature groups (Texture, Radial Distribution, Neighbors, Intensity, Granularity, Correlation, Area Shape) and retrained all models. We omitted one feature class and then independently optimized all 70 cell health models as described in the Machine learning framework results section above. We repeated this procedure once per feature class.

All software updates introducing this analysis can be viewed at https://github.com/broadinstitute/cell-health/pull/143

(2)Any H2AX and 'polynuclear' would probably fail in any cell line with this size of training data.

Indeed we would expect certain cell health phenotype models to fail if they had few hits and a relatively low variance of output values. This hit rate is directly associated with the phenotypes that the CRISPR perturbations induce, which is why we intentionally selected them to span multiple gene pathways in an attempt to maximize morphology diversity (see Supplementary Table S1).

We did indeed observe that the polynuclear model had few hits in the training data and relatively poor performance. We did not expect this result, given that DNA stains are captured in the Cell Health and Cell Painting assays. We suspect the poor performance in this model is likely because so few cells were classified as polynuclear in our gating strategy, making it perhaps an inconsistently measured readout.

By contrast, some gH2AX models did have relatively good performance. In the conclusion, we note that increased training data size using more perturbations is likely to improve model performance:

The results motivate collecting larger datasets for training, with more perturbations and multiple cell lines. These new datasets would enable the development of more expressive models, based on deep learning, that can be applied to single cells. Including orthogonal imaging markers of CRISPR infection would also enable us to isolate cells with expected morphologies. More data and better models would improve the performance and generalizability of Cell Health models and enable annotation of new and existing large-scale Cell Painting datasets with important mechanisms of cell health and toxicity.

(3)To what refers the 'weights' of the model in Fig. 1c?

We thank the reviewer for pointing out that we never defined this term in the Figure 1 legend. We use “weights” to refer to the coefficients from the regression model. To make this more clear, we have updated the legend to now read: “Model coefficient weights” and the text in Figure 1C to now read “model weights”.

Reviewer #1 (Significance (Required)):

This manuscript is not advanced in the context of latest improvements/developments of cell-based microscopic classification. Rationale in the introduction and the conclusion are not linked (interpretability, generalizability, costs). It seems to be unfinished or unformatted to this end?

Since responding to these reviews, we believe that our primary motivation - to demonstrate proof-of-concept of predicting cell health phenotypes directly from Cell Painting data - is now much clearer, holistically. We provide below an updated introduction, which improves rationale.

Perturbing cells with specific genetic and chemical reagents in different environmental contexts impacts cells in various ways (Kitano, 2002). For example, certain perturbations impact cell health by stalling cells in specific cell cycle stages, increasing or decreasing proliferation rate, or inducing cell death via specific pathways (Markowetz, 2010; Szalai et al., 2019). Cell health is normally assessed by eye or measured by specifically targeted reagents, which are either focused on a single Cell Health parameter (ATP assays) or multiple, in combination, via FACS-based or image-based analyses, which involves a manual gating approach, complicated staining procedures, and significant reagent cost. These traditional approaches limit the ability to scale to large perturbation libraries such as candidate compounds in academic and pharmaceutical screening centers.

Image-based profiling assays are increasingly being used to quantitatively study the morphological impact of chemical and genetic perturbations in various cell contexts (Caicedo et al., 2016; Scheeder et al., 2018). One unbiased assay, called Cell Painting, stains for various cellular compartments and organelles using non-specific and inexpensive reagents (Gustafsdottir et al., 2013). Cell Painting has been used to identify small-molecule mechanisms of action (MOA), study the impact of overexpressing cancer mutations, and discover new bioactive mechanisms, among many other applications (Caicedo et al., 2018; Christoforow et al., 2019; Hughes et al., 2020; Pahl and Sievers, 2019; Rohban et al., 2017; Simm et al., 2018; Wawer et al., 2014). Additionally, Cell Painting can predict mammalian toxicity levels for environmental chemicals (Nyffeler et al., 2020) and some of its derived morphology measurements are readily interpreted by cell biologists and relate to cell health (Bray et al., 2016). However, no single assay enables discovery of fine-grained cell health readouts.

We hypothesized that we could predict many cell health readouts directly from the Cell Painting data, which is already available for hundreds of thousands of perturbations. This would enable the rapid and interpretable annotation of small molecules or genetic perturbations. To do this, we first developed a customized microscopy assays, which collectively report on 70 different cell health indicators via a total of seven reagents applied in two reagent panels. Collectively, we call these assay panels “Cell Health”.

To demonstrate proof of concept, we collected a small pilot dataset of 119 CRISPR knockout perturbations in three different cell lines using Cell Painting and Cell Health. We used the Cell Painting morphology readouts to train 70 different regression models to predict each Cell Health indicator independently. We used simple machine learning methods instead of a deep learning approach because of our limited sample size and the inability to increase it by linking single cell measurements from both assays. We predicted certain readouts, such as the number of S phase cells, with high performance, while performance on other readouts, such as DNA damage in G2 phase cells, was low. We applied and validated these models on a separate set of existing Cell Painting images acquired from 1,571 compound perturbations measured across six different doses from the Drug Repurposing Hub project (Corsello et al., 2017). We provide all predictions in an intuitive web-based application at http://broad.io/cell-health-app, so that others can extend our work and explore cell health impacts of specific compounds.

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

This report from Way et al describes a method of extending a very popular screening technology called Cell Painting developed by the Carpenter Lab. The authors are contending with an important issue and as such this paper potentially will be of great interest to the community. Cell Painting provides quantitative fingerprints of cell phenotypes in response to changes in the molecular or physiological status of cells. However the molecular basis or even the candidate pathways for those changes is not always clear. Here, the authors take specific markers of cell physiology, e.g., DNA damage, ROS production, cell cycle progression etc. and relate them to Cell Painting features. The authors are trying to address the issue that running many probes of cell physiology is expensive and time consuming and that identifying proxies for these assays using much simpler Cell Painting technologies would be a useful and potentially powerful approach. The overall goal is to develop some type of regression model that can link the state of cells (the "health") to Cell Painting fingerprints.

The authors use three separate cell lines and CRISPR knockouts delivered through lentivirus that target 59 genes to establish a range of cell physiologies that they directly measure (the "Cell Health") and then relate to similar assays performed by Cell Painting. Ultimately they aim to use Cell Painting models to predict Cell Health.

We thank the reviewer for their succinct summary of our goals and rationale for this manuscript, and for the constructive and valuable comments herein.

**Major Issues:**

It appears that the phenotypes that are detected at a high enough level of significance (see Fig. 2), e.g DNA damage (gH2Ax), apoptosis (Caspase 3/7), dead cells, ROS (CellROX), etc. are probably most easily detected by simply monitoring DAPI signal in these screens. To detect many of the phenotypes, the authors have presented a fairly complex method of doing much simpler assays. The authors correctly highlight in Fig. 3 that the phenotypes they are detecting go beyond pure signals from DAPI. They report power in their models from Radial Distribution across many different components of the Cell Painting feature set.

We agree that the two assays we’re collectively calling “Cell Health” are indeed fairly complex - we use two different panels of multiplexed stains and a series of gating strategies to measure phenotypes in various cell subpopulations. However, the fundamental message in the manuscript is that we may no longer need to perform these complex assays if we get this information from the simpler Cell Painting assay.

We agree that our machine learning approach to predict the various cell health phenotypes uses signals beyond nucleus-based stains. However, even if we are predicting just DAPI signals, this reinforces our argument that the specific stains in the Cell Health assays (which are commonly used in targeted experiments) are not necessary to measure specifically. Instead, in certain circumstances, a scientist should just use unbiased stains to capture their biology of interest, since the stains are cheaper at scale and one has access to much more information.

It is also worth noting that the DNA damage phenotypes in specific cell subpopulations (e.g. DNA Damage in G1 cells) would not be possible to measure with high precision without EdU co-staining.

However these appear to give outputs that won't be that useful. It is hard to tell whether this is simply because they don't have enough images or whether their signal is confounded by using cell lines where the lentivirus CRISPR knockouts are working less efficiently.

(Reviewer 2 introduced a similar critique below, which we now move here) A fundamental issue that the authors mention but do not address is the efficiency of the CRISPR KOs. The authors should measure the efficiency of representative guides and present these data to help support the interpretation of their models.

We definitely agree that sample size is a limitation in this manuscript. Our primary goal with this paper was to demonstrate feasibility of the approach to predict the targeted Cell Health readouts using a simpler (and more affordable/scalable) assay in Cell Painting. The promising results we observed, especially given this sample size limitation, motivates collecting a larger dataset using more perturbations.

Potentially confounded signal by low efficiency CRISPR knockouts is also an interesting topic. We do provide Supplementary Figure S8 to describe a subtle relationship that we observed regarding CRISPR infection efficiency. We also discuss this in the results as: “We observed overall better predictivity in ES2 cells, which had the highest CRISPR infection efficiency (Supplementary Figure 8), suggesting that stronger perturbations provide better information for training and that training on additional data should provide further benefit.”

Additionally, we made a substantial effort to maximize CRISPR efficiency by independently optimizing lentivirus volumes for each sgRNA. In general, we observed that some cell lines are easier to CRISPR, probably based on more factors beyond Cas9 expression. However, we note that CRISPR is being used simply as a perturbation to elicit a variable morphology response. In other words, the type, efficacy, and even accuracy of perturbation does not matter as long as it satisfies two constraints: 1) induces a morphology response for a sufficient number of perturbations, and 2) is consistent between the two assays (Cell Health and Cell Painting). Our setup satisfies both constraints.

However, this experiment (and data from the experiment) can be used in other contexts in which the CRISPR efficiency is extremely important. Therefore, we added three columns to Supplementary Table 1 providing the efficiency readouts for the three cell lines. (This information was already present in GitHub, but we moved it to a more obvious location in Supplementary Table 1). Code describing this change can be viewed here: https://github.com/broadinstitute/cell-health/pull/142

In regards to the first sentence of this concern: “However these appear to give outputs that won’t be that useful” - indeed, we fully expected that many cell health readouts would be difficult to predict. In the original submission, we included the following explanation for potential sources of low performing models: ”Performance differences might result from random technical variation, small sample sizes for training models, different number of cells in certain Cell Health subpopulations (e.g. mitosis or polynuclear cells), fewer cells collected in the viability panel (see methods), or the inability of Cell Painting reagents to capture certain phenotypes.”

It seems misleading (or perhaps the explanation lacks clarity) to describe in the same paragraph the need to validate the model by applying it to new datasets, namely the Drug Repurposing Hub project, then describe gradients in cell health features across UMAP coordinates.

We thank the reviewer for pointing out this source of confusion and for providing an opportunity to improve the clarity of this section. Our major revisions here are as follows: 1) Introduce the Drug Repurposing Hub as an external dataset for validation; 2) Validate a high performing and simple model (number of live cells) by comparing model readout predictions from the Drug Repurposing Hub Cell Painting profiles against orthogonal PRISM viability readouts (in compounds with slightly different doses); 3) Validate three additional models: enrichment of proteasome inhibitors in the ROS model, enrichment of PLK inhibitors in the G1 cell count model, and enrichment of tubulin-destabilizing compounds in the Number of gH2Ax spots in G1 cells model; 4) Display a global structure of Cell Health predictions in UMAP space for select models. Note that for the fourth point, we are using the UMAP gradients to observe patterns, and not to validate models.

In order to encapsulate the updated flow, we’ve pasted below the entire Drug Repurposing Hub results/discussion section, which introduces two additional analyses and new text in response to various other reviewer comments. We feel that the updated section improves clarity and purpose.

The updated section now reads:

“Predictive models of cell health would be most useful if they could be trained once and successfully applied to data sets collected separately from the experiment used for training. Otherwise one could not annotate existing datasets that lack parallel Cell Health results, and Cell Health assays would have to be run alongside each new dataset. We therefore applied our trained models to a large, publicly-available Cell Painting dataset collected as part of the Drug Repurposing Hub project (Corsello et al., 2017). The data derive from A549 lung cancer cells treated with 1,571 compound perturbations measured in six doses.

We first chose a simple, high-performing model to validate. The number of live cells model captures the number of cells that are unstained by DRAQ7. We compared model predictions to orthogonal viability readouts from a third dataset: Publicly available PRISM assay readouts, which count barcoded cells after an incubation period (Yu et al., 2016). Despite measuring perturbations with slightly different doses and being fundamentally different ways to count live cells (Figure 4A), the predictions correlated with the assay readout (Spearman's Rho = 0.35, p -3; Figure 4B).

We also chose to validate three additional models: ROS, G1 cell count, and Number of gH2AX spots in G1 cells. We observed that the two proteasome inhibitors (bortezomib and MG-132) in the Drug Repurposing Hub set yielded high ROS predictions (OR = 76.7; p -15) (Figure 4C). Proteasome inhibitors are known to induce ROS (Han and Park, 2010; Ling et al., 2003). As well, PLK inhibitors yielded low G1 cell counts (OR = 0.035; p = 3.9 x 10-8) (Figure 4C). The PLK inhibitor HM-214 showed an appropriate dose response (Figure 4D). PLK inhibitors block mitotic progression, thus reducing entry into the G1 cell cycle phase (Lee et al., 2014). Lastly, we observed that aurora kinase and tubulin inhibitors yielded high Number of gH2AX spots in G1 cells predictions (OR = 11.3; p Figure 4E). In particular, we observed a strong dose response for the aurora kinase inhibitor barasertib (AZD1152) (Figure 4F). Aurora kinase and tubulin inhibitors cause prolonged mitotic arrest, which can lead to mitotic slippage, G1 arrest, DNA damage, and senescence (Orth et al. 2011; Cheng and Crasta 2017; Tsuda et al. 2017).

We applied uniform manifold approximation (UMAP) to observe the underlying structure of the samples as captured by morphology data (McInnes et al., 2018). We observed that the UMAP space captures gradients in predicted G1 cell count (Supplementary Figure S14A) and in predicted ROS (Supplementary Figure S14B). We also observed similar gradients in the ground truth cell health readouts in the CRISPR Cell Painting profiles used for training cell health models (Supplementary Figure S15). Gradients in our data suggest that cell health phenotypes manifest in a continuum rather than in discrete states.

Lastly, we observed moderate technical artifacts in the Drug Repurposing Hub profiles, indicated by high DMSO profile dispersion in the Cell Painting UMAP space (Supplementary Figure 14C). This represents an opportunity to improve model predictions with new batch effect correction tools. Additionally, it is important to note that the expected performance of each Cell Health model can only be as good as the performance observed in the original test set (see Figure 2), and that all predictions require further experimental validation.“

Updated Figure 4:

Figure 4: Validating Cell Health models applied to Cell Painting data from The Drug Repurposing Hub. The models were not trained using the Drug Repurposing Hub data. (a) The results of the dose alignment between the PRISM assay and the Drug Repurposing Hub data. This view indicates that there was not a one-to-one matching between perturbation doses. (b) Comparing viability estimates from the PRISM assay to the predicted number of live cells in the Drug Repurposing Hub. The PRISM assay estimates viability by measuring barcoded A549 cells after an incubation period. (c) Drug Repurposing Hub profiles stratified by G1 cell count and ROS predictions. Bortezomib and MG-132 are proteasome inhibitors and are used as positive controls in the Drug Repurposing Hub set; DMSO is a negative control. We also highlight all PLK inhibitors in the dataset. (d) HMN-214 is an example of a PLK inhibitor that shows strong dose response for G1 cell count predictions. (e) Tubulin and aurora kinase inhibitors are predicted to have high Number of gH2AX spots in G1 cells compared to other compounds and controls. (f) Barasertib (AZD1152) is an aurora kinase inhibitor that is predicted to have a strong dose response for Number of gH2AX spots in G1 cells predictions.

Updated Supplementary Figure:

Supplementary Figure S14: Applying a Uniform Manifold Approximation (UMAP) to Drug Repurposing Hub consensus profiles of 1,571 compounds across six doses. The models were not trained using the Drug Repurposing Hub data. (a) The point color represents the output of the Cell Health model trained to predict the number of cells in G1 phase (G1 cell count). (b) The same UMAP dimensions, but colored by the output of the Cell Health model trained to predict reactive oxygen species (ROS). (c) In the UMAP space, we highlight DMSO as a negative control, and Bortezomib and MG-132 as two positive controls (proteasome inhibitors) in the Drug Repurposing Hub set. We observe moderate batch effects in the negative control DMSO profiles, based on their spread in this visualization. The color represents the predicted number of live cells. The positive controls were acquired with a very high dose and are expected to result in a very low number of predicted live cells.

All software updates required to update these figures can be viewed at https://github.com/broadinstitute/cell-health/pull/145

Is it surprising that cell health phenotypes and gradients therein are present in a dataset describing cell health perturbations?

This was not surprising to us, and we thank the reviewer for asking the question. We have now added a new Supplementary Figure to present a UMAP with ground truth cell health measurements in the CRISPR dataset (pasted below). By adding the figure, we show how Cell Health predictions are expected to show gradients in UMAP space. In fact, for any lower-dimensional embedding that is able to preserve local neighborhoods of the high-dimensional space, we should expect all linear transformations of the input data (in the high-dimensional space) to vary smoothly across the lower-dimensional embedding. However, it is still informative to observe where the specific Cell Health phenotype predictions manifest in relation to global morphology structure. We add the following sentence in the Drug Repurposing Hub paragraph juxtaposed to the other UMAP gradient observations:

We applied uniform manifold approximation (UMAP) to observe the underlying structure of the samples as captured by morphology data (McInnes et al., 2018). We observed that the UMAP space captures gradients in predicted G1 cell count (Supplementary Figure S14A) and in predicted ROS (Supplementary Figure S14B). We also observed similar gradients in the ground truth cell health readouts in the CRISPR Cell Painting profiles used for training cell health models (Supplementary Figure S15). Gradients in our data suggest that cell health phenotypes manifest in a continuum rather than in discrete states.

Supplementary Figure S15: Applying a Uniform Manifold Approximation (UMAP) to the Cell Painting consensus profile data of CRISPR perturbations. UMAP coordinates visualized by (a) cell line, (b) ground truth G1 cell counts, and (c) ground truth ROS counts. (d) Visualizing the distribution of ground truth ROS compared against G1 cell count. The two outlier ES2 profiles are CRISPR knockdowns of GPX4, which is known to cause high ROS.

We have also added the option to explore the CRISPR profile Cell Health ground truth in our shiny app https://broad.io/cell-health (screenshot pasted below)

Modifications to the software introducing these changes can be viewed at https://github.com/broadinstitute/cell-health/pull/141.

The actual test of the model's performance is in the paragraph below, but the data associated with the Spearman correlation is hidden in Fig. S10b. The data is not convincing by eye, and the artifactually low p value suggests that proper statistical corrections were not applied.

We have moved the Spearman correlation figure (previously Supplementary Figure S10B) into a main figure, along with a complete restructuring of the results and discussion in the Drug Repurposing Hub section.

We appreciate the careful observations and interpretations, and confirm the statistical test performed here is sound and the p value is correct (there is no need to account for multiple testing since there is only one test being applied, a test of correlation between two variables).

We add this rationale to the “Comparing viability predictions to an orthogonal readout” methods section:

We performed the non-parametric Spearman correlation test because 1) the doses were not aligned between the datasets we compared, and 2) it is possible that a strong nonlinear correlation exists between readouts from two fundamentally different ways to measure viability.

It is definitely valid to critique the scatter plot relationship to understand that the mean squared error is quite high (i.e. if two datasets had viability measurements using the two approaches, it would be wrong to assume that lower measurements in one assay automatically could be compared to lower measurements of the other assay). This level of variability would be lost if all we did was report the test statistic, which is the reason why we included the scatter plot as a figure.

It may also be important to mention that the authors of the PRISM paper also noted high variation in their estimates (from Corsello et al https://doi.org/10.1038/s43018-019-0018-6): "At the level of individual compound dose–responses, we note that the PRISM Repurposing dataset tends to be somewhat noisier, with a higher standard error estimated from vehicle control measurements (Extended Data Fig. 5c and Extended Data Fig. 6a–c)."

Nevertheless, we agree that the current way we report this p value is distracting and potentially misleading, depending on how the p value is interpreted. Therefore, we have updated the reporting of all p values to say that they are less than a predefined cutoff. The figure now states that p

Fig 1A and associated methods are not sufficient information to describe the manual gating strategy and any variability found across iterations in these gates. Effort should be taken to quantify where these manual boundaries were set and why.

We describe the manual gating strategies in much detail in the methods section “Cell Health assay: Image analysis”. However, we agree that a description of measurement variability and experimental approach requires more detail, and we agree that the manuscript would benefit from a visual example of these gates. These improvements required us to rearrange Figure 1.

With a goal of increasing reproducibility in the cell health assay, we’ve (1) moved example images of the Cell Health assay to Figure 1A; (2) Moved the existing gating strategies drawing to Supplementary Figure 1; (3) Added real data examples of the manual gating strategy as a new Supplementary Figure 2. We show all updates below:

Updated Figure 1:

Figure 1. Data processing and modeling approach. (a) Example images and workflow from the Cell Health assays. We apply a series of manual gating strategies (see Methods) to isolate cell subpopulations and to generate cell health readouts for each perturbation. (top) In the “Cell Cycle” panel, in each nucleus we measure Hoechst, EdU, PH3, and gH2AX. (bottom) In the “Cell Viability” panel, we capture digital phase contrast images, measure Caspase 3/7, DRAQ7, and CellROX. (b) Example Cell Painting image across five channels, plus a merged representation across channels. The image is cropped from a larger image and shows ES2 cells. Below are the steps applied in an image-based profiling pipeline, after features have been extracted from each cell’s image. (c) Modeling approach where we fit 70 different regression models using CellProfiler features derived from Cell Painting images to predict Cell Health readouts.

Updated Supplementary Figure S1:

Supplementary Figure S1: Illustration of the gating strategy in the Cell Health assays. We extract 70 different readouts from the Cell Health imaging assay. The assay consists of two customized reagent panels, which use measurements from seven different targeted reagents and one channel based on digital phase contrast (DPC) imaging; shown are five toy examples to demonstrate that individual cells are isolated into subpopulations by various gating strategies to define the Cell Health readouts.

Updated Supplementary Figure S2 (Example gating strategies):

Supplementary Figure S2: Real data of manual gating in the Cell Health assays.

For each cell line, we apply a series of manual gating strategies defined by various stain measurements in single cells to define cell subpopulations. (a) In the cell cycle panel, we first select cells that are useful for cell cycle analysis based on nucleus roundness and Hoechst intensity measurements. We also identify polyploid and “large not round” (polynuclear) cells. (b) We then subdivide the cells used for cell cycle to G1, G2, and S cells based on total Hoechst intensity (DNA content) and EdU incorporation signal intensity. (c) We use Hoechst and PH3 nucleus intensity to define mitotic cells. The points are colored by EdU intensity in the nucleus in both (b) and (c). (d) Example gating in the viability panel. We use DRAQ7 and CellEvent (Caspase 3/7) to distinguish alive and dead cells, and categorize early or late apoptosis. See Methods for more details about how the Cell Health measurements are made.

We’ve also added the following to the methods section:

Additionally, we set these gates for each cell subpopulation using a set of random wells from each cell line and experiment independently. We observed that the intensity measurements used to form the gates were consistent across wells and plates, and generally formed distinct cell subpopulation clusters. After using the random wells to set the gates, we used the Harmony microscope software to apply the gates to the remaining wells and plates.

In general however, the need to clearly define this process further emphasizes a strength in our approach: There is great potential for inconsistencies when different humans draw gates. We aim to reduce these inconsistencies by predicting these readouts from Cell Painting images directly.

The authors conclude that their results motivate further data acquisition and model training, and that this will improve model performance. This is only true if their lack of predictive power comes from the data volume itself, and not in larger problems of data quality, variability and the core assumptions of their method. The authors note the better predictability in ES2 cells, likely due to higher CRISPR efficiency and therefore stronger phenotypes. It is possible, as I believe the authors suggest, that the ES2 cells provide information that improves the predictive power of cells with poor infection efficiency. It is instead possible that only the ES2 cells with strong phenotypes yield predictive power, pulling the average of the dataset up. Authors could train the cell line specific datasets independently and compare relative changes in predictive performance. Otherwise, is it possible that subtle or highly complex phenotypes simply cannot be detected by this method and more data will be unlikely to improve predictability in modest perturbations.

We thank the reviewers for raising this possibility. To explore this, we performed a cell-line holdout analysis in which we retrained (and individually reoptimized) all 70 cell health models on every combination of two cell lines and predicted readouts from the held out third cell line.

Despite there being fewer samples in the training set in the cell line holdout test compared to the original test set (66% vs. 85%) and the fact that each model had never seen the held out cell line before, many cell health phenotypes could still be predicted. We add the following results in a new Supplementary Figure:

Supplementary Figure S11: Results from a cell line holdout analysis. We trained and evaluated all 70 cell health models in three different scenarios using each combination of two cell lines to train, and the remaining cell line to evaluate. For example, we trained all 70 models using data from A549 and ES2 and evaluated performance in HCC44. We bin all cell health models into 14 different categories (see Supplementary Table S3 and https://github.com/broadinstitute/cell-health/6.ml-robustness for details about the categories and scores). We also provide the original test set (15% of the data, distributed evenly across all cell types) performance in the last row, as well as results after training with randomly permuted data. This cross-cell-type analysis yields worse performance overall. Nevertheless, despite the models never encountering certain cell lines, and having fewer training data points, many models still have predictive power across cell line contexts. Note that we truncated the y axis to remove extreme outliers far below -1. The raw scores are available on https://github.com/broadinstitute/cell-health.

We’ve also performed a sample size titration analysis, which suggests that more data would indeed improve model performance. More data would also enable a deep learning approach, which is also likely to improve performance.

Supplementary Figure S13: Dropping samples from training reduces test set model performance in high, mid, and low performing models. We determined model performance stratification by taking the top third, mid third, and bottom third of test set performance when using all data. We performed the sample titration analysis with 10 different random seeds and visualized the median test set performance for each model.

We also update the results section to introduce and discuss this result:

Lastly, we performed a sample size titration analysis in which we randomly removed a decreasing amount of samples from training. For the high and mid performing models, we observed a consistent performance drop, suggesting that increasing sample size would result in better overall performance (Supplementary Figure 13).

And an updated methods describing this analysis now reads:

Machine learning robustness: Investigating the impact of sample size

We performed an analysis in which we randomly dropped an increasing amount of samples from the training set before model training. After dropping the predefined number of samples, we retrained all 70 cell health models and assessed performance on the original holdout test set. We performed this procedure ten times with ten unique random seeds to mirror a more realistic scenario of new data collection and to reduce the impact of outlier samples on model training.

All software updates introducing this analysis can be viewed at https://github.com/broadinstitute/cell-health/pull/143

Although the authors argue that the Cell Painting assay is capturing complex health phenotypes using a variety of morphological features, there is a clear overweighting of a particular few (in fact two...). It would be interesting to systematically retrain with exclusion of particular features to determine if equalizing the weight across features changes performance. These are also notably the feature groups with the fewest features-- how many individual features within these feature groups are pulling all the weight?

We agree that an additional computational analysis including a systematic feature removal would be interesting and valuable. We’ve included this analysis as part of a new results subsection in which we assess where classification improvements are likely to come from by testing robustness of the ML models.

Specifically, we’ve systematically removed individual features that belong to specific feature groups, channels, and compartments to determine how much their absence negatively affects model performance. The added supplementary figure is pasted below.

Supplementary Figure S12: Systematically removing classes of features has little impact on most models’ performance. We retrained all 70 cell health models after dropping features associated with specific (a) feature groups, (b) channels, and (c) compartments. Each dot is one model (predictor), and the performance difference between the original model and the retrained model after dropping features is shown on the x axis. Any positive change indicates that the models got worse after dropping the feature group. (d) Individual model differences in performance after dropping features. Each dot is one class of features removed (as in a-c).

We conclude that the majority of cell health models are robust to missing feature groups. Some models actually improve with a reduction in the feature space. Combined with the feature heatmap presented in Figure 3, these results tell us that a lot of the morphology signal is redundant across Cell Painting features.

We add the following text to the results:

We also performed a systematic feature removal analysis, in which we retrained cell health models after dropping features that are measured from specific groups, compartments, and channels. We observed that most models were robust to dropping entire feature classes during training (Supplementary Figure 12). This result demonstrates that many Cell Painting features are highly correlated, which might permit prediction “rescue” even if the directly implicated morphology features are not measured. Because of this, we urge caution when generating hypotheses regarding causal relationships between readouts and individual Cell Painting features.

And the following to the methods:

Machine learning robustness: Systematically removing feature classes

We performed an analysis in which we systematically dropped features measured in specific compartments (Nuclei, Cells, and Cytoplasm), specific channels (RNA, Mito, ER, DNA, AGP), and specific feature groups (Texture, Radial Distribution, Neighbors, Intensity, Granularity, Correlation, Area Shape) and retrained all models. We omitted one feature class and then independently optimized all 70 cell health models as described in the Machine learning framework results section above. We repeated this procedure once per feature class.

All software updates introducing this analysis can be viewed at https://github.com/broadinstitute/cell-health/pull/143

In summary there is a very interesting concept here, but for several possible, currently undefined reasons, the authors are reporting a very weak measurement. The authors allude to these limitations, but it would be great if the authors could address these issues and provide a stronger dataset.

We thank the reviewers for their encouraging remarks. We believe that with the added robustness analyses and with increased clarity about the motivation behind the paper, we’ve successfully demonstrated a proof of concept for the approach to predict cell health phenotypes from Cell Painting images. We believe that we’ve provided sufficient evidence to a reader to demonstrate the benefits of the prediction approach. As well, given the additional details describing the Cell Health assay reproducibility, that the paper also successfully introduces a new assay paradigm.

Furthermore, while many of the cell health measurements are definitely weak (and unreliable), it is not fair to generalize all predictions as weak (especially given the sample size limitations).

It is also worth noting that, under the current circumstances, separating the one dataset we have into a train/test set and validating the model in an external set is the best we could do; we do not have additional budget to run further wet lab experiments (which would also face a COVID backlog in our chemical screening group). We agree that additional datasets would benefit the field; our current data is now public, all of our future data will be public (to the extent possible), and we hope that others building on our work will make their data public too to address these questions.

Lastly, in response to the “currently undefined reasons” comment, as well as other comments throughout, we’ve now included a new subsection in the Results/Discussion subsection to more directly answer some of the reasons why many models may have underperformed. Specifically, and as mentioned previously in this response, we perform three distinct robustness analyses: 1) Cell line holdout; 2) feature holdout; 3) sample size titration.

Authors should include representative images of their Cell Health assay in the main figures. A full figure of all labels and examples of manual gating should be included (S1 is too limited)

Scale bars need to be included in all images, some are missing in S1

We thank the reviewers for this suggestion. We have since substantially updated figure 1 and supplementary figure S1. We have also added a new supplementary figure S2 as an example of the manual gating strategies, and we have updated all scale bars appropriately. We’ve attached the specific figure updates in an earlier response.

"20x water objective in confocal mode" is not a sufficient level of detail on image acquisition parameters especially considering the lack of representative images. At the very least, NA and if appropriate pinhole size should be reported. Similarly, "9 FOV per well" is not sufficient. Pixel size and FOV area/dimensions are necessary.

We have added these necessary details in their representative methods sections:

We acquired all cell images using an Opera Phenix High Content Imaging Instrument (PerkinElmer) with a 20X water objective (a numerical aperture (NA) of 1.0), in confocal mode (a pinhole size of 50µm). The effective pixel size was 0.65µm/pixel. We acquired images in four channels using default excitation / emission combinations: for the blue channel (Hoechst) 405/435-480; for the green channel (Alexa 488 and CellEvent) 488/500-550; for the orange channel (Alexa 568 and CellRox Orange) 561/570-630 and for the far-red channel (Alexa 647 and DRAQ7) 640/650-760. We applied the Cell Health reagents for cell viability and for cell cycle in two separate plates.

The legends for the different parts of Fig S10 are transposed which makes the figure quite confusing.The authors should amend or clarify the language of "guide perturbation" and "guide profile".

Wow! We thank the reviewers for pointing out this oversight, and for their careful attention to detail. This figure is now completely different after the restructuring of the Drug Repurposing Hub results/discussion section. The legends for all figures are now correct.

EdU is defined after it is abbreviated in methods

We thank the reviewers for noting this. We’ve now fixed where these acronyms are abbreviated in the methods section and removed their definition in later sections where redundant:

The authors should address the following image processing reproducibility concerns:

Segmentation and feature extraction parameters are not included in the Supplementary Information. Either attach the CellProfiler pipeline or add a table with parameters and settings used for each module.

CellProfiler and Harmony versions are missing.

We thank the reviewers for pointing out these very important omissions. We have since rectified in the methods section:

We built a CellProfiler image analysis and illumination correction pipeline (version 2.2.0) to extract these image-based features (McQuin et al., 2018). We include the CellProfiler pipelines in our github repository.

We developed and ran two distinct image analysis pipelines in Harmony software (version 4.1; PerkinElmer) for each of the Cell Health plates.

We also add the CellProfiler pipelines to our GitHub repository. A pull request introducing this change can be viewed here: https://github.com/broadinstitute/cell-health/pull/149

Subpopulation definition (page 14) should be defined in a way that the algorithms (pipelines) could be reproduced, e.g.: "unusually high intensity of Hoechst max" requires a stricter definition.

These definitions are subjective by nature. Gating decisions will be different depending on the scientist performing the image analysis. We feel that the sentence: “We excluded outlier nuclei with unusually high intensity of Hoechst max” conveys this subjectivity well. One of the strengths of the proposed approach to predict cell health phenotypes directly from the Cell Painting images is the removal of gating subjectivity.

Why is the nucleus roundness calculated in PE Harmony and not in the CellProfiler pipeline itself?

We used the nucleus roundness measurements as calculated in PE Harmony to define the “cells selected for cell cycle” subpopulation in the first panel of the Cell Health assay. I.e. this measurement was integral to the Cell Health assay itself. We believe that the addition of example gates (in supplementary figure 2) clears up this confusion.

Reviewers:

Jason Swedlow

Melpi Platani

Erin Diel

Emil Rozbicki

Reviewer #2 (Significance (Required)):

Nature and Significance: This study aims to demonstrate how phenotypic studies using different markers can be combined and linked to deliver wider application and value.

Relationship to Published Work: This study extends previous work from the same group and attempts a novel extension. The approach is a useful concept and potentially important.

Audience: The method this paper proposes will be of interests to scientists involved with drug discovery and/or computational biology.

Reviewer's Expertise: Cell Biology, Imaging, Imaging Informatics, Machine Learning, Computer Vision

We would like to again express thanks to these reviewers for their careful read, very helpful comments, and encouraging remarks.

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

The authors present a novel idea on predicting various cell health readouts based on a general set of markers and cell painting assay. The cell health readouts are based on more specific markers performed in different assays measuring cell proliferation and death. The authors suggest that such an approach can reduce the number of experiments needed. The paper is well written, and the figures are clear and comprehensive.

We thank the reviewer for their helpful comments and encouragement!

**Major comments:**

Some of the health readouts are based on general morphology (cell and nucleus) which can be obtained based on cell painting assay. Although some of these models perform well, it is surprising that the model of nuclear roundness did not perform very well especially for HCC4 (R-square reaching zero). This is surprising as these data can be extracted from cell painting assays. Can the author elaborate on why this is the case?

We agree that the performance of the live cell roundness and nucleus roundness models were unexpectedly low. One would expect that these shape features as measured by PerkinElmer Harmony software, would be easily predicted from CellProfiler readouts from the Cell Painting assay.

The roundness property was used in Harmony versions,

2*sqrt(π)*sqrt(Area-BorderArea/2.0)/BorderArea-0.1)

where Area is object area in pixels and BorderArea is border area in pixels (we thank Joe Trask, Olavi Ollikainen, Hartwig Preckel, and Kaupo Palo at PerkinElmer for this information.)

No single feature in the CellProfiler readouts measures roundness directly; instead, CellProfiler will measure a combination of shape features that together could synthesize the idea of “roundness”. However, given that the elastic net approach is well-suited for this type of synthesis, it remains unclear why roundess is not predicted well.

One possible explanation is that shape features are the most different measurements across cell lines and they are measured precisely in both assays. Precise measurements coupled with our training strategy of using all three lines together, might lead to poor performance in predicting certain cell-line intrinsic features.

We tested this shape result directly (and also generally to the other cell health features) in a “cell line holdout” analysis, which we describe in more detail in response to the next comment. In this analysis, we tested how well models generalized to cell lines not encountered in the training process. In this analysis, we trained on every combination of two cell lines and applied the trained models to the third. We observed that cell line intrinsic features, like shape, are predicted poorly if a model was not trained using the cell line.

Using elastic net regression models is well-suited to the problem due to the low number of observations. However, there is a significant difference between the performance of different cell lines. Does the performance of the models improve if different models were trained for every cell line? Leave one out approach can be used to accommodate the scarcity of samples.

We thank the reviewer for this important question. We also appreciate how different certain models behaved with certain cell lines. We would like to stress that the results presented here represent a small pilot study that is not meant to optimize model performance. Instead, the motivation of the manuscript is to demonstrate proof-of-concept of the approach to predict specific cell health phenotypes directly from Cell Painting images. We believe that the current results demonstrate positive proof, which warrants an expansion of data collection and an improvement of the classification methodology.

Nevertheless, with our current data, we can answer an important question about the feasibility of signal transfer between cell lines. Therefore, we performed an additional “cell line holdout” analysis. We believe that the cell line holdout analysis tells us that signals can be transferred across contexts, but that any leading observations must be followed up with experiments performed directly in the cell line of interest. This signal transfer is diluted compared to the original test set performance, but it is also worth noting that the models presented in Supplementary Figure 11 (pasted below) were trained on only 66% of the data in the holdout cell line analysis and 85% of the data in the original analysis.

Supplementary Figure S11: Results from a cell line holdout analysis. We trained and evaluated all 70 cell health models in three different scenarios using each combination of two cell lines to train, and the remaining cell line to evaluate. For example, we trained all 70 models using data from A549 and ES2 and evaluated performance in HCC44. We bin all cell health models into 14 different categories (see Supplementary Table S3 and https://github.com/broadinstitute/cell-health/6.ml-robustness for details about the categories and scores). We also provide the original test set (15% of the data, distributed evenly across all cell types) performance in the last row, as well as results after training with randomly permuted data. This cross-cell-type analysis yields worse performance overall. Nevertheless, despite the models never encountering certain cell lines, and having fewer training data points, many models still have predictive power across cell line contexts. Note that we truncated the y axis to remove extreme outliers far below -1. The raw scores are available on https://github.com/broadinstitute/cell-health.

And we add the following text to the results section:

We performed a series of analyses to determine certain parameters and options that are likely to improve models in the future. First, we performed a “cell line holdout” analysis, in which we trained models on two of three cell lines and predicted cell health readouts on the held out cell line. We observed that certain models including those based on viability, S phase, early mitotic and death phenotypes could be moderately predicted in cell lines agnostic to training (Supplementary Figure 11). Not surprisingly, shape-based phenotypes could not be predicted in holdout cell lines, which emphasizes the limitations of transferring certain cell-line specific measurements across cell lines.

All software updates introducing this analysis can be viewed at https://github.com/broadinstitute/cell-health/pull/143

The authors chose to validate based on the number of live cells as it is one of the best models. However, this readout can be obtained using simple viability assays. It would be more convincing to validate on a more complex phenotype that can only be attained using imaging such as #gH2AX spots.

It is worth noting that we do also show generalizability in the Drug Repurposing Hub for two other models: ROS and G1 cell count. We show that proteasome inhibitors significantly induce high ROS and PLK inhibitors restrict entry to G1. We have also added enrichment tests demonstrating high statistical significance for these compound mechanisms.

While we recognize that these two examples provide anecdotal evidence, they suggest the ability and power of the approach to assign phenotypes to Cell Painting images.

Nevertheless, we thank the reviewer for bringing up this critical point and certainly appreciate the benefit of validating a gH2AX model. Therefore, we’ve added a similar analysis in which we demonstrate generalizability of the top performing gH2Ax model: Number of gH2AX spots in G1 cells. We discuss these changes in an updated section:

We also chose to validate three additional models: ROS, G1 cell count, and Number of gH2AX spots in G1 cells. We observed that the two proteasome inhibitors (bortezomib and MG-132) in the Drug Repurposing Hub set yielded high ROS predictions (OR = 76.7; p -15) (Figure 4C). Proteasome inhibitors are known to induce ROS (Han and Park, 2010; Ling et al., 2003). As well, PLK inhibitors yielded low G1 cell counts (OR = 0.035; p = 3.9 x 10-8) (Figure 4C). The PLK inhibitor HM-214 showed an appropriate dose response (Figure 4D). PLK inhibitors block mitotic progression, thus reducing entry into the G1 cell cycle phase (Lee et al., 2014). Lastly, we observed that aurora kinase and tubulin inhibitors yielded high Number of gH2AX spots in G1 cells predictions (OR = 11.3; p Figure 4E). In particular, we observed a strong dose response for the aurora kinase inhibitor barasertib (AZD1152) (Figure 4F). Aurora kinase and tubulin inhibitors cause prolonged mitotic arrest, which can lead to mitotic slippage, G1 arrest, DNA damage, and senescence (Orth et al. 2011; Cheng and Crasta 2017; Tsuda et al. 2017).

We also modify the abstract summarizing this result:

For Cell Painting images from a set of 1,500+ compound perturbations across multiple doses, we validated predictions by orthogonal assay readouts, and by confirming mitotic arrest, ROS, and DNA damage phenotypes via PLK, proteasome, and aurora kinase/tubulin inhibition, respectively.

And we add this analysis to an updated Figure 4:

Figure 4: Validating Cell Health models applied to Cell Painting data from The Drug Repurposing Hub. The models were not trained using the Drug Repurposing Hub data. (a) The results of the dose alignment between the PRISM assay and the Drug Repurposing Hub data. This view indicates that there was not a one-to-one matching between perturbation doses. (b) Comparing viability estimates from the PRISM assay to the predicted number of live cells in the Drug Repurposing Hub. The PRISM assay estimates viability by measuring barcoded A549 cells after an incubation period. (c) Drug Repurposing Hub profiles stratified by G1 cell count and ROS predictions. Bortezomib and MG-132 are proteasome inhibitors and are used as positive controls in the Drug Repurposing Hub set; DMSO is a negative control. We also highlight all PLK inhibitors in the dataset. (d) HMN-214 is an example of a PLK inhibitor that shows strong dose response for G1 cell count predictions. (e) Tubulin and aurora kinase inhibitors are predicted to have high Number of gH2AX spots in G1 cells compared to other compounds and controls. (f) Barasertib (AZD1152) is an aurora kinase inhibitor that is predicted to have a strong dose response for Number of gH2AX spots in G1 cells predictions.

All software updates required to update these figures can be viewed at https://github.com/broadinstitute/cell-health/pull/145

It is also worth noting that collecting more data for this manuscript is not currently feasible given the amount of projects backlogged from COVID. We feel that given that the motivation of the project is to demonstrate feasibility of the approach, with our current training/testing machine learning framework and the application to Drug Repurposing Hub data is sufficient.

The text would benefit from expanding the discussion to include the advantages and limitations of their approach.

We thank the reviewer for bringing up this concern, and we agree that it is worth an increased discussion about advantages and limitations of the approach. Indeed, we’ve added a full new results/discussion subsection directly testing many of the assumptions for why some models performed well and others didn’t. The new section introduces many model limitations:

We performed a series of analyses to determine certain parameters and options that are likely to improve models in the future. First, we performed a “cell line holdout” analysis, in which we trained models on two of three cell lines and predicted cell health readouts on the held out cell line. We observed that certain models including those based on viability, S phase, early mitotic and death phenotypes could be moderately predicted in cell lines agnostic to training (Supplementary Figure 11). Not surprisingly, shape-based phenotypes could not be predicted in holdout cell lines, which emphasizes the limitations of transferring certain cell-line specific measurements across cell lines. We also performed a systematic feature removal analysis, in which we retrained cell health models after dropping features that are measured from specific groups, compartments, and channels. We observed that many models were robust to dropping entire feature classes during training (Supplementary Figure 12). This result demonstrates that many Cell Painting features are highly correlated, which might permit prediction “rescue” even if the directly implicated morphology features are not measured. Because of this, we urge caution when generating hypotheses regarding causal relationships between phenotypes and individual Cell Painting features. Lastly, we performed a sample size titration analysis in which we randomly removed a decreasing amount of samples from training. For the high and mid performing models we observed a consistent performance drop, suggesting that increasing sample size would result in better overall performance (Supplementary Figure 13).

**Minor comments**

Page 8: The authors visualize the predicted G1 cell count and ROS when overlayed on a UMAP based on cell painting data from Drug Repurposing Hub. How these visualisations look like if applied to the original CRISPR training data.

We address this comment by adding a supplementary figure showing ground truth G1 cell count and ROS readouts.

We applied uniform manifold approximation (UMAP) to observe the underlying structure of the samples as captured by morphology data (McInnes et al., 2018). We observed that the UMAP space captures gradients in predicted G1 cell count (Supplementary Figure S14A) and in predicted ROS (Supplementary Figure S14B). We also observed similar gradients in the ground truth cell health readouts in the CRISPR Cell Painting profiles used for training cell health models (Supplementary Figure S15). Gradients in our data suggest that cell health phenotypes manifest in a continuum rather than in discrete states.

Where Supplementary Figure 15 is pasted below:

Supplementary Figure S15: Applying a Uniform Manifold Approximation (UMAP) to the Cell Painting consensus profile data of CRISPR perturbations. UMAP coordinates visualized by (a) cell line, (b) ground truth G1 cell counts, and (c) ground truth ROS counts. (d) Visualizing the distribution of ground truth ROS compared against G1 cell count. The two outlier ES2 profiles are CRISPR knockdowns of GPX4, which is known to cause high ROS.

We have also added the option to explore the CRISPR profile Cell Health ground truth in our shiny app https://broad.io/cell-health (screenshot pasted below)

Modifications to the software introducing these changes can be viewed at https://github.com/broadinstitute/cell-health/pull/141.

The second part of the last paragraph on page 8 is confusing as it is not related to the first part using the PRISM data.

We thank the reviewer for noting this. We agree that the clarity of this section could be improved. We have now completely reworked the final section of applying the cell health models to the Drug Repurposing Hub data.

In particular, we’ve moved the PRISM data section as the first, most simple model to validate, and moved these results to Figure 4. We then describe validation for three other models: ROS, G1 cell count and Number of gH2Ax spots in G1 cells. And we end with the UMAP discussion, which is the original second part of the last paragraph on page 8.

The PRISM section now reads:

We first chose a simple, high-performing model to validate. The number of live cells model captures the number of cells that are unstained by DRAQ7. We compared model predictions to orthogonal viability readouts from a third dataset: Publicly available PRISM assay readouts, which count barcoded cells after an incubation period (Yu et al., 2016). Despite measuring perturbations with slightly different doses and being fundamentally different ways to count live cells (Figure 4A), the predictions correlated with the assay readout (Spearman's Rho = 0.35, p -3; Figure 4B).

Reviewer #3 (Significance (Required)):

This approach can be of wide interest as it is easy to implement, cost-effective and lead to interpretable models. It would be interesting to see if the results improve when increasing the sample size. Another aspect that can be useful to investigate in the future is whether including a separate marker that indicates infected cells only in the more detailed assays would result in better accuracies.

We thank the reviewer for their enthusiasm and for this concluding idea. Indeed, we also feel that including a separate marker to indicate infected cells could lead to improved accuracy. We add this thought to the concluding section as a future direction. The full updated conclusion reads as follows:

We have demonstrated feasibility that information in Cell Painting images can predict many different Cell Health indicators even when trained on a small dataset. The results motivate collecting larger datasets for training, with more perturbations and multiple cell lines. These new datasets would enable the development of more expressive models, based on deep learning, that can be applied to single cells. Including orthogonal imaging markers of CRISPR infection would also enable us to isolate cells with expected morphologies. More data and better models would improve the performance and generalizability of Cell Health models and enable annotation of new and existing large-scale Cell Painting datasets with important mechanisms of cell health and toxicity.

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Referee #3

Evidence, reproducibility and clarity

The authors present a novel idea on predicting various cell health readouts based on a general set of markers and cell painting assay. The cell health readouts are based on more specific markers performed in different assays measuring cell proliferation and death. The authors suggest that such an approach can reduce the number of experiments needed. The paper is well written, and the figures are clear and comprehensive.

Major comments:

Some of the health readouts are based on general morphology (cell and nucleus) which can be obtained based on cell painting assay. Although some of these models perform well, it is surprising that the model of nuclear roundness did not perform very well especially for HCC4 (R-square reaching zero). This is surprising as these data can be extracted from cell painting assays. Can the author elaborate on why this is the case?

Using elastic net regression models is well-suited to the problem due to the low number of observations. However, there is a significant difference between the performance of different cell lines. Does the performance of the models improve if different models were trained for every cell line? Leave one out approach can be used to accommodate the scarcity of samples.

The authors chose to validate based on the number of live cells as it is one of the best models. However, this readout can be obtained using simple viability assays. It would be more convincing to validate on a more complex phenotype that can only be attained using imaging such as #gH2AX spots.

The text would benefit from expanding the discussion to include the advantages and limitations of their approach.

Minor comments

Page 8: The authors visualize the predicted G1 cell count and ROS when overlayed on a UMAP based on cell painting data from Drug Repurposing Hub. How these visualisations look like if applied to the original CRISPR training data.

The second part of the last paragraph on page 8 is confusing as it is not related to the first part using the PRISM data.

Significance

This approach can be of wide interest as it is easy to implement, cost-effective and lead to interpretable models. It would be interesting to see if the results improve when increasing the sample size. Another aspect that can be useful to investigate in the future is whether including a separate marker that indicates infected cells only in the more detailed assays would result in better accuracies.

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Referee #2

Evidence, reproducibility and clarity

This report from Way et al describes a method of extending a very popular screening technology called Cell Painting developed by the Carpenter Lab. The authors are contending with an important issue and as such this paper potentially will be of great interest to the community. Cell Painting provides quantitative fingerprints of cell phenotypes in response to changes in the molecular or physiological status of cells. However the molecular basis or even the candidate pathways for those changes is not always clear. Here, the authors take specific markers of cell physiology, e.g., DNA damage, ROS production, cell cycle progression etc. and relate them to Cell Painting features. The authors are trying to address the issue that running many probes of cell physiology is expensive and time consuming and that identifying proxies for these assays using much simpler Cell Painting technologies would be a useful and potentially powerful approach. The overall goal is to develop some type of regression model that can link the state of cells (the "health") to Cell Painting fingerprints.

The authors use three separate cell lines and CRISPR knockouts delivered through lentivirus that target 59 genes to establish a range of cell physiologies that they directly measure (the "Cell Health") and then relate to similar assays performed by Cell Painting. Ultimately they aim to use Cell Painting models to predict Cell Health.

Major Issues:

It appears that the phenotypes that are detected at a high enough level of significance (see Fig. 2), e.g DNA damage (gH2Ax), apoptosis (Caspase 3/7), dead cells, ROS (CellROX), etc. are probably most easily detected by simply monitoring DAPI signal in these screens. To detect many of the phenotypes, the authors have presented a fairly complex method of doing much simpler assays. The authors correctly highlight in Fig. 3 that the phenotypes they are detecting go beyond pure signals from DAPI. They report power in their models from Radial Distribution across many different components of the Cell Painting feature set. However these appear to give outputs that won't be that useful. It is hard to tell whether this is simply because they don't have enough images or whether their signal is confounded by using cell lines where the lentivirus CRISPR knockouts are working less efficiently.

It seems misleading (or perhaps the explanation lacks clarity) to describe in the same paragraph the need to validate the model by applying it to new datasets, namely the Drug Repurposing Hub project, then describe gradients in cell health features across UMAP coordinates. Is it surprising that cell health phenotypes and gradients therein are present in a dataset describing cell health perturbations? The actual test of the model's performance is in the paragraph below, but the data associated with the Spearman correlation is hidden in Fig. S10b. The data is not convincing by eye, and the artifactually low p value suggests that proper statistical corrections were not applied.

Fig 1A and associated methods are not sufficient information to describe the manual gating strategy and any variability found across iterations in these gates. Effort should be taken to quantify where these manual boundaries were set and why.

A fundamental issue that the authors mention but do not address is the efficiency of the CRISPR KOs. The authors should measure the efficiency of representative guides and present these data to help support the interpretation of their models.

The authors conclude that their results motivate further data acquisition and model training, and that this will improve model performance. This is only true if their lack of predictive power comes from the data volume itself, and not in larger problems of data quality, variability and the core assumptions of their method. The authors note the better predictability in ES2 cells, likely due to higher CRISPR efficiency and therefore stronger phenotypes. It is possible, as I believe the authors suggest, that the ES2 cells provide information that improves the predictive power of cells with poor infection efficiency. It is instead possible that only the ES2 cells with strong phenotypes yield predictive power, pulling the average of the dataset up. Authors could train the cell line specific datasets independently and compare relative changes in predictive performance. Otherwise, is it possible that subtle or highly complex phenotypes simply cannot be detected by this method and more data will be unlikely to improve predictability in modest perturbations.

Although the authors argue that the Cell Painting assay is capturing complex health phenotypes using a variety of morphological features, there is a clear overweighting of a particular few (in fact two...). It would be interesting to systematically retrain with exclusion of particular features to determine if equalizing the weight across features changes performance. These are also notably the feature groups with the fewest features-- how many individual features within these feature groups are pulling all the weight?

In summary there is a very interesting concept here, but for several possible, currently undefined reasons, the authors are reporting a very weak measurement. The authors allude to these limitations, but it would be great if the authors could address these issues and provide a stronger dataset.

Minor issues: Authors should include representative images of their Cell Health assay in the main figures. A full figure of all labels and examples of manual gating should be included (S1 is too limited) Scale bars need to be included in all images, some are missing in S1

"20x water objective in confocal mode" is not a sufficient level of detail on image acquisition parameters especially considering the lack of representative images. At the very least, NA and if appropriate pinhole size should be reported. Similarly, "9 FOV per well" is not sufficient. Pixel size and FOV area/dimensions are necessary.

The legends for the different parts of Fig S10 are transposed which makes the figure quite confusing.The authors should amend or clarify the language of "guide perturbation" and "guide profile".

EdU is defined after it is abbreviated in methods

The authors should address the following image processing reproducibility concerns:

Segmentation and feature extraction parameters are not included in the Supplementary Information. Either attach the CellProfiler pipeline or add a table with parameters and settings used for each module.

CellProfiler and Harmony versions are missing.

Subpopulation definition (page 14) should be defined in a way that the algorithms (pipelines) could be reproduced, e.g.: "unusually high intensity of Hoechst max" requires a stricter definition.

Why is the nucleus roundness calculated in PE Harmony and not in the CellProfiler pipeline itself?

Reviewers: Jason Swedlow Melpi Platani Erin Diel Emil Rozbicki

Significance

Nature and Significance: This study aims to demonstrate how phenotypic studies using different markers can be combined and linked to deliver wider application and value.

Relationship to Published Work: This study extends previous work from the same group and attempts a novel extension. The approach is a useful concept and potentially important.

Audience: The method this paper proposes will be of interests to scientists involved with drug discovery and/or computational biology.

Reviewer's Expertise: Cell Biology, Imaging, Imaging Informatics, Machine Learning, Computer Vision

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Referee #1

Evidence, reproducibility and clarity

The submitted manuscript entitled 'Predicting cell health phenotypes using image-based morphology profiling' (RC-2020-00394) by Way et al. presents a set of seven dyes/staining (as two separate panels) to microscopically screen cell viability. For automatic classification a training/test set of 119 CRISPR (approximately 2 sgRNAs per gene) perturbations on 3 cancer cell lines were generated (lung A549, ovarian ES2, lung HCC44). After segmentation of cell nuclei a set of morphological cell measurements were extracted from each perturbation (total 952 features). The nature of these feature spanning cell cycle and viability phenotypes, enabled the authors to define 70 different phenotype classes, which are used to model a classifier by elastic linear regression. Specific definitions (cell cycle and ROS) were partly predicted/validated in an independent existing image data set (Drug Repurposing Hub project). The data is available as web-based application/visualization and the supplementary method is well described.

Major concerns:

(1)The only fundamental argument of this manuscript not to apply state-of-the-art deep learning (DL) machine-learning (mentioned in McCain et al. 2018), which does not require segmentation, feature extraction, abstraction, manual gating is the 'interpretability' of the predictions. However, performance, precision, scalability (by modern GPUs) with DL should clearly outperform 'manual' regression models. All recent machine vision benchmarks in microscopy confirm this, but also clearly shows 'real world' translational applications, e.g.

https://www.nature.com/articles/s43018-020-0085-8,

https://www.biorxiv.org/content/10.1101/2020.07.02.183814v1.full.pdf,

In other words, the presented methodology is not compared to DL, and is not convincing in terms of interpretability benefits.

(2)One aforementioned point of the methodology is cryptically/not described: Why it should be less expensive compared with other (which?) approaches (see introduction)?

(3)Generalizability and/or training data size is essential for any model-based classification, but not evaluated or validated in the current manuscript. The independent validation on a A549 cell line only data might be not sufficient/convincing.

Minor concerns:

(1)Highest test performance comprises that precision is mainly driven by cell cycle/count and live status and could be probably derived from DRAQ7 (Fig. 2) and DNA granularity (Fig. 3, bottom right) and would argue for rigid feature selection across channels and features.

(2)Any H2AX and 'polynuclear' would probably fail in any cell line with this size of training data.

(3)To what refers the 'weights' of the model in Fig. 1c?

Significance

This manuscript is not advanced in the context of latest improvements/developments of cell-based microscopic classification. Rationale in the introduction and the conclusion are not linked (interpretability, generalizability, costs). It seems to be unfinished or unformatted to this end?

The author/co-authors have been instrumental/pioneered with their past work on cell-based image processing (CellProfiler software), but the presented methodology is simply outdated. Therefore, a revision towards a comparison and benchmarking with DL will also not help.

Ref (DL with MIL): https://academic.oup.com/bioinformatics/article/32/12/i52/2288769

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Reply to the reviewers

Reply to the reviewers:

We are grateful to the referees for investing valuable time in reviewing our work, and for recognising the importance and utility. We thank them for their insightful and constructive comments that have helped us significantly improve the manuscript.

Below, we provide a point-by-point response to all specific questions raised.

Reviewer #1 (Evidence, reproducibility and clarity (Required)): In order to improve SARS-CoV-2 diagnostics, Reijns et al. developed a multiplexed RT-qPCR protocol that allows simultaneous detection of two viral genes, one housekeeping gene as well as an external gene as an extraction control. Compared to running parallel assays to detect genes individually, the turnaround time is much shorter and reagents are saved. Furthermore, the presented data suggest that the assay is more sensitive than commercial kits. The authors also propose the detection of the human housekeeping gene as a measure of sample quality control. In principal, this work has potential but the manuscript itself needs a better structure. **Major concerns:** The authors have used the Takara RT-qPCR kit for their study. Did the authors try other commercial kits?

We have not assessed other commercial kits as the Takara reagent performed well, and has been easy to source. We expect that other one-step kits could be used if the need arose.

When we initiated this work in March 2020, we selected the Takara One Step PrimeScript™ III RT-PCR Kit based on 1) the practical advantages of a one-step reaction mix, 2) published evidence of its successful use in SARS-CoV-2 detection (see below), 3) availability in sufficient quantities for testing at scale, and 4) affordability.

(Published evidence: One of the first descriptions of an assay to detect SARS-CoV-2 [1] employed the Takara One Step PrimeScript™ III RT-PCR Kit, and this kit was later shown by others to perform as well as or better than Qiagen Quantifast Multiplex RT-PCR +R mastermix, ThermoFisher TaqPath 1-Step RT-qPCR MasterMix and ThermoFisher Taqman Fast Virus 1-step mastermix, when used to detect SARS-CoV-2 RNA from nose and throat swabs with N1, N2 or N gene assays [2].)

Can the authors elaborate on the supply chain of the Takara kit?

We have not had problems securing the Takara kit in sufficient quantities and in a timely fashion, and did so through the company’s Scotland and NE England representative. The managing director of Takara Bio Europe provided the following statement, as a clarification of the supply chain:

“Takara Bio Inc. has worked on significantly increasing the production of one-step RT-qPCR reagents to cover worldwide needs for SARS-CoV-2 detection. The production of this kit is based in China under ISO13485 certification and the European stock is based in, and distributed, from Paris. Throughout this pandemic, Takara Bio Europe has supplied millions of reactions around Europe to COVID-19 testing labs, without encountering any shortages or significant shipping delays.”

Could it cover population testing in case of shortages of other commercial kits?

Yes, it could. The Takara kit is available in 4,000 and 20,000 reaction pack sizes and therefore could well be a useful option in case of shortages of other commercial kits. Indeed, one motivation for developing the multiplex assay was to ensure diagnostic testing resilience in the face of reagent shortages.

For better comparison, is it possible to give information on which primers the commercial kits are based on?

We contacted both ThermoFisher and Abbott to ask for more information on the primers and probes included in the TaqPath COVID‐19 Combo Kit (detects N, ORF1ab and S gene) and Abbott RealTime SARS‐CoV‐2 assay (detects RdRp and N gene). Unfortunately, we were informed that this information is proprietary. For clarity, we have included the following in the Materials and Methods section:

“Primers and probes included in the TaqPath COVID-19 Combo Kit (Thermo Fisher Scientific, Cat. No. A47814) detect SARS-CoV-2 ORF1ab, N and S gene; those in the Abbott RealTime SARS-CoV-2 assay (Cat. No. 09N77-090) detect RdRp and N gene. Further details are not available, as this information is proprietary.”

Also, explain better the primers used in this study. For example, the N1 and N2 primers are directed against different regions of the SARS-CoV-2 N gene.

We thank the reviewer for encouraging us to better explain the primers we use for our own assays, and now provide more detailed information in a new Fig 1.

The result section needs a better structure as the first two pages do not refer to any of the main figures. For example, in which figure or table can the reader find the data that are discussed in lines 83 to 87?

We have now substantially re-structured the entire Results section, and include the data that was discussed in lines 83 to 87 of the original manuscript, in Fig 1D of the revised manuscript.

Table S1, instead of current Table 1, could be moved to main figures as it contains the important finding that the multiplexed assay may be more sensitive than the commercial one.

As suggested, we have moved Table S1 to the main display items (now Table 1), and moved the original Table 1 to the supplementary items (now Table S3).

The authors identified some samples that scored negative in commercial assays but positive in their new assay. This is important, however, the possibility of detecting false positives should be strengthened in a "Discussion" section.

We thank the reviewer for highlighting this, and now discuss the issue of detecting false positives in more detail in the Discussion section of the revised manuscript:

“RT-qPCR tests are molecular tests with high intrinsic accuracy, however false positive and false negative results can occur. The use of multiplex assays that detect multiple SARS-CoV-2 targets, such as those reported here, reduces the chance of both. Off-target reactivity is one possible cause of false positives, and although some have reported high false positive rates for the E gene assay [20, 22], this does not match our experience. In two patients, our N1E-RP and N2E-RP assays detected virus, albeit weakly, whereas commercial assays did not. As multiple SARS-CoV-2 targets were positive, these are likely true positive results and not due to off-target reactivity. False positives can also occur due to lab issues such as sample mislabelling, data entry errors, reagent contamination with target nucleic acids or contamination of primary specimens. However high standards of quality control at all stages of testing, and effective mitigation strategies should quickly identify problems. Additionally, sample re-test with an independent assay and/or patient re-sampling should also be effective measures to counter false positives, particularly in low pre-test probability situations such as mass screening.”

Figures 1 to 3 have different panels which seem to be redundant. For example, Fig 1 A and B, Fig 2 B and C, Fig 3 C and D.

These panels did contain the same data, plotted to convey slightly different information. However, we agree that this introduces a level of redundancy. For enhanced clarity, in the revised manuscript, we have removed most of these panels altogether, or moved them to supplementary figures.

Figure 1: Give a rational why comparing before and after extraction. This heavily depends on the extraction method and not on the detection itself. In addition, IVT RNA does not reflect the complexity of a clinical specimen. This is rather confusing and deviates from the important findings.

As part of the validation procedure it was important for us to show that the entire workflow, including the extraction procedure, was robust for use in clinical diagnostics. In this context, comparing pre- and post-extraction RT-qPCR results for both IVT RNA and viral samples provided us with an opportunity to test extraction efficiency. However, we agree that for the purpose of this manuscript, the inclusion of these data in (the former) Fig 1 detracted from the main message. In the revised manuscript we have therefore moved the data comparing Cq values before and after extraction to a new Fig S1, and briefly state the rationale behind this in the main text and figure legend.

It was not our intention to imply that IVT RNA in any way reflects the complexity of a clinical specimen. We include these data as part of the step-by-step validation of our assays. Firstly, we show high sensitivity using IVT RNA; secondly, we show that a similar sensitivity is achieved on viral positive controls; and thirdly, we show that our assays perform equally well to widely used commercial assays on clinical samples.

Figure 3: Were any of the negative samples/patients tested with an undetectable housekeeping gene, re-test positively?

None of our patient samples had undetectable levels of RPP30. We note that all NTS samples were collected by healthcare professionals and in this context such findings will likely be rare. However this may not be the case when dealing with samples obtained by self-swabbing as the reviewer highlights in a comment below.

Did adding this housekeeping gene as a control actually improve the detection of any patient samples? If the authors want to convince the readership of this quality control, experimental evidence should be provided.

Fig 3C and D seem to contain this information somewhat, as here, the values were normalized and the CT values for the E and N gene decreased. Nevertheless there is no real explanation of this figure provided in the Result section at all. While this figure has potential, the authors have to keep in mind that the number of cells in a swab can be affected by many biological factors, including age, sample timing, inflammation of the respiratory tract, etc. In addition, viral genomes can exist intra- as well as extracellular, in the form of free virus. So even in the absence of human cells/detectable housekeeping genomes, viral RNA can be or should be present in a sample in case of infection. This explains (probably) why a correlation between detectable housekeeping gene and viral RNA is absent (Fig 3A and B?). This entire Fig 3 just needs a better explanation. The provided text does not describe any results and should go into a "Discussion" section.

We thank the reviewer for highlighting the need to explain Fig 3 more clearly and that a key question is whether there is a correlation between the levels of the housekeeping control and viral RNA. Prompted by this question, we reanalysed our data and now show that there is a strong and statistically significant positive correlation between Cq values for RPP30 and SARS-CoV-2 targets (see below, and new Fig 4C). This shows that there is a lower probability of detecting SARS-CoV-2 RNA in samples that contain fewer human cells. This likely implies that for samples with high RPP30 Cq values, a proportion of virus positive samples will be missed, contributing to the high false negative rates that have been reported [3-5].

Providing additional experimentation would require systematic re-contacting and re-testing of cases, and this is beyond our current research framework. While outside the scope of the current study, we hope that our manuscript will encourage others to perform the necessary large-scale experiments. Nonetheless, with this correlation alone, we believe that RPP30 provides useful information of benefit to clinical diagnostics (also see our response to Reviewer 2), and in the revised manuscript we outline how it might be best utilised (Discussion, Table S6).

To provide a better explanation of Figure 3 (now Fig 4), we have included the following in the Results section:

“A statistically significant linear correlation between Cq values for each of the viral probes (E, N1, and N2) and the Cq values for the RPP30 sample quality probe (p 40; Fig 4D and Fig S4A). Theoretically, using this approach, even a strong positive sample (SARS-CoV-2 Cq value of 28.2) of good quality (RPP30 Cq value of 20.3) may have given a false negative test result (SARS-CoV-2 Cq value of 40) if it had contained the same low amount of human material as the reference sample (RPP30 Cq value of 32.1; viral Cq: 32.1-20.3+28.2=40). Conversely, normalising samples to an optimal quality sample (RPP30 Cq 20.1/20.3) gives an indication of what viral Cq values may have been if all samples had contained a similar (more optimal) amount of material (Fig 4E, Fig S4B). This highlights the possibility that a proportion of apparent SARS-CoV-2 negative samples are in fact false negatives as a result of insufficient material in the swab fluid.”

Self-swabbing is surely a potential source of variability and false-negatives, but many publications have shown the suitability of saliva testing. This should also be discussed and would probably negate the need for such a quality control.

We agree with the reviewer that self-swabbing will be more prone to variability. Therefore, the RPP30 control will have particular value here, lowering the associated risk of false negatives. While NTS sampling remains a major modality for testing for the foreseeable future, saliva is certainly a potential alternative strategy, one that may benefit from lower sample variability.

We now include the reviewer’s point on this in the Discussion:

“Testing saliva, as an alternative to NTS sampling, could also be beneficial as a modality that may have less-sample to sample variability [7]”

Which assay works better, the N1E-RP or the N2E-RP assay? A final conclusion is missing here.

Although we could not detect substantial differences between these two assays during our validation process, others have reported a marginally higher sensitivity of the N1 over the N2 assay [6]. We would therefore recommend the use of the N1E-RP assay for first line testing, with the N2E-RP assay available as a second line test of equivalent sensitivity in case of inconclusive initial test results. We comment on this in the revised manuscript:

“Although we did not detect substantial differences between our two assays, others have reported higher sensitivity of the N1 over the N2 assay [19]. We therefore recommend the use of the N1E-RP assay for primary testing, and the N2E-RP assay could be employed if initial results are inconclusive.”

Reviewer #1 (Significance (Required)): Naturally, in this pandemic, this topic is important as sensitive and affordable methods to detect SARS-CoV-2 infections are in need. This Reviewer agrees that multiplexing could be an elegant approach to fill this need.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): In this manuscript, Reijns and colleagues describe an approach to detect the causative agent of COVID-19, the beta coronavirus SARS-CoV-2, using an inexpensive in-house multiplex RT-qPCR. Concomitantly, viral E, N and RdRP(probe P2) as well as human RPP30 and a herpesvirus nucleic acid are also detected in order to monitor both the sample quality and the sample preparation. Reijns et al. performed testing on a huge amount of samples and used the data to describe the strength and limitations of the assay. The data is sound and give a very good impression of the 4-plex PCR capabilities. I read manuscript fluently and consider as linguistically very good. However, I still have a few comments and remarks that would strengthen the manuscript:

**Major issues:** In the first section of the results section, many primer / probe conditions are given that make the reading flow difficult. Instead of using (data not shown) it would be helpful to use a table or a graphic to illustrate the various approaches.

We thank the reviewer for suggesting the use of graphics to explain our different approaches. To aid the reader, we now include a diagram in the new Fig 1 that shows the positions of primers and probes used in our work (A), and illustrate the various 4-plex assays (B, C).

In general, I suggest to replace Ct by Cq, since the IVT standards are a quantification method.

As suggested by the reviewer we now use Cq instead of Ct throughout our manuscript, following MIQE guidelines [7].

There has already been a change away from the initial E and RdRP gene based assay because of the published sensitivity issues and the use of degenerate bases as well as the detection of unspecific nucleic acids for E gene). In particular, it has been shown that the Sarbeco-E-yields false positive results (Toptan et al. 2020 (https://doi.org/10.3390/ijms21124396), Konrad et al. 2020 (https://doi.org/10.2807/1560-7917.ES.2020.25.9.2000173)), so that many laboratories do not consider E-gene-based results for borderline samples anymore. In this manuscript, the authors should comment on why they still use the results from the E gene / RdRP and describe their experience.

We thank the reviewer for highlighting issues with the RdRp and E gene primer/probe pairs. In the process of our work we had also become aware that the RdRp-P2 assay suffers from low sensitivity, as has now been widely reported. However, although the E gene assay also detects SARS-CoV, we were not aware of potential problems with high rates of false positives as described by Toptan et al (2020) and Konrad et al (2020). It did come to our attention that early on in the pandemic some oligonucleotide producers reported problems with contamination of primers with SARS-CoV-2 template RNA synthesised in the same facilities, and were careful to avoid these providers. In our work, we did not experience any problems with apparent false positive detection of the E gene: it was never detected in any of our negative controls, and out of 84 patients that tested negative with the commercial TaqPath assay we did not find any that were positive for E gene only when using our N1E-RP and N2E-RP assays. In this context, it is also important to emphasise that a positive diagnosis is given only when both viral targets are detected (Table S6), which is one of the strengths of our multiplex assays.

As suggested by Reviewer 1, we now discuss the issue of false positives in more detail in the revised manuscript. We also comment on high false positive rates observed by others for the E gene assay, citing the two studies, but state that this does not match our own experience:

“Off-target reactivity is one possible cause of false positives, and although some have reported high false positive rates for the E gene assay [20, 23], this does not match our experience.”

In this manuscript, it should be indicated that the SARS-CoV-2 specific Probe P2 (according to Corman et al. 2020) was used. The reason for lower sensitivity due to nucleotide ambiguity and mismatch has to be explained in more detail. In addition to Corman et al. 2020 (see reference 2), Toptan et al 2020 (https://doi.org/10.3390/ijms21124396) might serve as helpful literature.

In tables describing primers and probes, and the new Fig 1, we indicate that we used RdRp probe P2. In addition, we now also specifically state in the legend of Fig 1 that this probe only detects SARS-CoV-2 and that the primers used in the RdRp-P2 assay (as originally designed by Corman et al) contain nucleotide ambiguities and a mismatch. Finally, in the main text we explain:

“Overall, we find RdRp detection to be at least 20-fold less sensitive than for E gene, N1 and N2 under our assay conditions; consistent with reports by others [19]. This may be due to a mismatch in the reverse primer employed in the RdRp (P2) assay, as originally designed [14].”

With regard to the marginally positive samples that were not consistent in all assays, were the PCR products analyzed using high-resolution PAA genes and, if possible, sequenced? The sequencing approach (Sanger or NGS) offers the final characterization of the PCR products (especially for pan-genotypic primers such as E-Sarbeco). The samples declared as "inconclusive" could be further characterized in this way.

Unfortunately, it has not been possible for us to carry out additional analyses for such (now historical) samples. Given the high prevalence of SARS-CoV-2 and the low sequence variability at primer/probe binding sites (new Table 2 and S5), inconclusive or marginally positive samples most likely reflect low viral load and/or low sample quality. Nevertheless, we now highlight the utility of further characterising such samples in the revised manuscript:

“However, differentiating between samples with low viral loads and false positives is challenging. Analysis of such samples by Sanger sequencing of PCR products, or nanopore sequencing of RNA present could provide useful information. Further clinical evaluation and repeat sampling of the patient involved may also be a beneficial route to a secure clinical diagnosis.”

The normalization in figure 3 should be also explained in the main text. Especially, why this approach was used for normalization.

In the Results section we now describe the normalisation as follows:

“A statistically significant linear correlation between Cq values for each of the viral probes (E, N1, and N2) and the Cq values for the RPP30 sample quality probe (p 40; Fig 4D and Fig S4A). Theoretically, using this approach, even a strong positive sample (SARS-CoV-2 Cq value of 28.2) of good quality (RPP30 Cq value of 20.3) may have given a false negative test result (SARS-CoV-2 Cq value of 40) if it had contained the same low amount of human material as the reference sample (RPP30 Cq value of 32.1; viral Cq: 32.1-20.3+28.2=40). Conversely, normalising samples to an optimal quality sample (RPP30 Cq 20.1/20.3) gives an indication of what viral Cq values may have been if all samples had contained a similar (more optimal) amount of material (Fig 4E, Fig S4B). This highlights the possibility that a proportion of apparent SARS-CoV-2 negative samples are in fact false negatives as a result of insufficient material in the swab fluid.”

Nonetheless, it looks like the normalized values wills cluster much more strongly than those corresponding to the actual values. The authors should comment on this phenomenon. It appears that the higher cq values (less virus) are subject to a strong correction factor more often than high values. Are there any statistical relevant tendencies towards this phenomenon? For everyday clinical practice, does this mean that low samples Cqs (mostly) only reflect the quality of the sample, but not the viral load?

We thank the reviewer for highlighting the stronger clustering of Cq values after normalisation, and for encouraging us to explore this further. We now show that there is a statistically significant linear correlation between RPP30 and SARS-CoV-2 Cq values (Fig 4C). This would indeed imply that a substantial proportion of the variability in SARS-CoV-2 Cq values seen in clinical practice is due to sample quality rather than different viral loads. However, outliers from the linear correlation when comparing samples from many different patients are to be expected (as seen in Fig 4C), because viral load is known to vary, with time of sampling relative to onset of symptoms one important contributing factor. In a research context, expressing viral load relative to a human control may be beneficial to differentiate between sample quality and absolute quantities of (intra/extracellular) viral RNA.

In the revised manuscript we state:

“Notably, the SARS-CoV-2 Cq values clustered more strongly after normalisation (Fig 4D, E; Fig S4). This reduced variability not only shows that the amount of human material present in NTS samples impacts on assay sensitivity, but also suggests that variability in viral load is not as great as implied by RT-qPCR data without normalisation.”

Finally, it remains somewhat unclear to what extent the Cq values of the RPP30 should have an influence on the routine diagnostics. The authors discuss that a fixed cutoff value would be a possibility to sort out poor swab samples, but if a cq value is available it would also make sense to generate a kind of quality score that can display the significance of a test. It would be helpful if the authors could comment on this or other possibilities.

We agree that it would be beneficial for routine diagnostics to derive such a measure. However, at this stage we do not have sufficient data to generate a robust quality score based on the RPP30 Cq values. Nonetheless, we believe RPP30 Cq values have immediate utility for routine diagnostics, and could help improve validity of test results going forward:

1. Samples with undetectable RPP30 should trigger repeat sample collection, and not be given a false negative test result;
2. Samples with high viral Cq values and/or for which only one of two viral targets are detected can be better interpreted in the context of the amount of human material as measured by RPP30 Cq;
3. Ongoing monitoring of swab quality allows rapid identification of potential technical issues with swabbing;
4. Normalisation of viral Cq values using RPP30 Cq values might be helpful in a research context to derive a more meaningful measure of viral loads, by removing one source of variability;
5. Collection of such data on an ongoing basis would ultimately allow this to be translated into a quality score that could be used as part of diagnostics algorithms. In the revised manuscript we now discuss this as follows:

“Absence of RPP30 signal (undetected or Cq >40) clearly indicates that absence of viral detection cannot be interpreted as a negative test result and that a repeat test is required (Table S6). However, utilising RPP30 Cq values when interpreting an apparent SARS-CoV-2 negative sample requires further consideration: what should the RPP30 Cq limit be for which to order a repeat test? One option would be to simply set an arbitrary cut-off, e.g. one could decide to re-test any samples with RPP30 Cq >30, or with Cq values above the 95th centile (Cq ~ 31 for our 108 samples). To determine robust cut-off limits, collection of RPP30 data for a much larger number of patient samples would be desirable. This would allow development of diagnostic algorithms that could incorporate a sample quality score based on the level of RPP30 detected. Nonetheless, RPP30 data, even as it stands, are useful for the interpretation of cases for which only one of the SARS-CoV-2 targets is (weakly) positive, with samples with high RPP30 Cq values interpreted with particular caution. In such cases, repeat testing of the same sample (with an independent assay of equal or better sensitivity) would be advisable, and repeat patient specimen collection and testing might also be considered (see Table S6 for guidance).”

Over the past few months, more and more virus subtypes have formed through the manifestation of point mutations (and amino acid substitutions). The authors should therefore definitely comment on the current strains as to whether all primers / probes are able to detect the virus variants circulating worldwide without loss of sensitivity.

We thank the reviewer for this suggestion and now include a table providing information on mismatches in primer and probe binding sites (see Table 2 and Table S5 of the revised manuscript). This shows that only a small proportion of 97,782 strains for which high quality genome sequencing is available have changes in primer/probe binding sites. In addition, the use of two different primer/probe sets in our multiplex assays provides a further safeguard against failure to detect strains with such changes.

Along this line, which virus strains were used for the cultivation as described in line 131? Is sequence data available? If so, it would provide helpful information to characterize the viral strain.

We have added strain information, accession codes for genome sequences and information on primer/probe binding for both control strains (hCoV-19/England/02/2020 and BetaCoV/Munich/ChVir984/2020) we used in our work (see Materials and Methods of the revised manuscript).

Line 206ff: In my opinion, this section belongs more to the discussion part than to material and methods that describe the technical implementation.

We agree and have now moved this section to the Discussion. Furthermore, we’ve made additional changes to better highlight the potential for further improvements to our assays, and SARS-CoV-2 RT-qPCR assays in general.

Is there a loss of sensitivity compared to the single PCRs? This data is very important and useful for other users. They should therefore be included explicitly in the manuscript (supplements).

We set out to develop multiplex PCR assays to allow more efficient and cost-effective testing. In the early stages of this process we performed small pilot experiments with positive control IVT RNA and individual primer/probe pairs that are widely used and well-established to sensitively detect SARS-CoV-2 RNA. With the exception of the RdRp primers/probe, we found all to perform well, with the ability to detect 10 copies of RNA. However, we did not perform a side-by-side comparison of uni- and multiplex PCRs, and to improve the structure and flow of the Results section, as requested by Reviewer 1, we have now removed all mention of the single PCR assays.

Altogether, the key message of our work is that the N1E-RP and N2E-RP assays are able to detect between 1 and 3 copies of SARS-CoV-2 RNA and show equivalent performance to commercially available multiplex assays.

**Minor issues:** Line 15 ff.: Source is missing, is this WHO-data?

The estimated number of infections and fatalities at the time of writing of the original manuscript was based on data from the online interactive dashboard hosted by Johns Hopkins University. At the suggestion of Reviewer 3, we have removed precise numbers from the revised manuscript to make the introduction less time-dependent. Nonetheless, we now include a reference to the JHU online resource, as well as the weekly epidemiological updates from the WHO (https://www.who.int/emergencies/diseases/novel-coronavirus-2019/situation-reports) for readers interested in the latest figures.

Fig S3: How was the digital droplet PCR carried out? A brief description should be included in the legend text.

We purchased these samples from QCMD, an independent International External Quality Assessment & Proficiency Testing (EQA/PT) organisation. QCMD performed the digital droplet PCR, before distribution under the QCMD 2020 Coronavirus Outbreak Preparedness EQA Pilot Scheme, and provided us with details, which have now been added to the Materials and Methods section:

“Quantification of control samples was carried out by QCMD prior to distribution within the EQA scheme, using droplet digital PCR (ddPCR) with E-gene primers and probe [13, 14] on the Biorad droplet digital PCR platform. A serial dilution of inactivated SARS-CoV-2 (strain BetaCoV/Munich/ChVir984/2020; GenBank Accession MT270112, [32]) was prepared and each dilution replicate tested 4 times using both RT-qPCR and ddPCR assays. Regression analysis was used to assess the linearity across the dilution series, and the analytical measurement range established for both assays, comparing results of each by Bland-Altman difference plot."

In addition, we provide more details with the relevant table (new Table S3) and in the legend of the associated figure (new Fig 2) we state: “See Materials and Methods for details”.

Figure 1a: PCR efficiencies are missing.

We have now added PCR efficiencies to all relevant graphs.

Line 145: MS2 appears, but without explaining the context. This should be improved here with additional information (this does not appear until line 154).

At first mention of MS2 in the main text, we now state:

“Internal controls were included to provide confirmation of successful nucleic acid extraction and absence of PCR inhibitors, with lysis buffer spiked with both MS2 (an RNA bacteriophage that infects Escherichia coli) and PhHV (a DNA virus that infects seals), detected by the TaqPath and N1E-RP/N2E-RP assays respectively..”

Page 15, H20 instead of H20, reaction mix instead of Reaction mix.

In the supplementary protocol, we have changed “H2O” to “H2O” and “Reaction mix” to “reaction mix”.

Reviewer #2 (Significance (Required)): The novel coronavirus SARS-CoV-2 is the causative agent of the acute respiratory disease COVID-19 which has become a global concern due to its rapid spread and high death rate. While some patients have no symptoms at all, but are still able to spread the virus, others have severe symptoms, often with fatal outcome. The gold standard in SARS-CoV-2 detection is the RT-qPCR approach, however, the high cost commercial kits are available in limited amounts only. The issue of the scarcity of resources is still an highly important issue, especially in terms of the incredibly rapidly increasing number of cases worldwide. Thus, the manuscript is of significance for the field and timely. Especially, diagnostic laboratories in low-income countries that are involved in the managing the pandemic but also researchers will benefit from this manuscript and save resources.

Reviewer #3 (Evidence, reproducibility and clarity (Required)): In this study Reijns et al developed a multiplex RT-PCR assay (alternative primer-probe sets and enzyme mixes) to detect SARS‐CoV‐2 and internal controls. The authors conclude that their assay performed equally well as established commercial kits. The authors also demonstrated that nose‐and‐throat swab samples have considerable variability in patient material content (>1,000‐fold variability). High variability is expected, but it is still important to substantiate this notion with numbers. Overall, I like the study and find it methodologically sound. Sample numbers in the tests are in most cases good. I have very few objections and hope to see the manuscript published soon.

**SPECIFIC COMMENTS:** 1."The COVID‐19 pandemic originated in Wuhan (China) in December 2019 and at the time of writing has infected more than 13.1 million people worldwide, resulting in well over 0.57 million COVID‐19‐related deaths..." I suggest a more timeless starting of the introduction, not pointing out exact number of infections and deaths since these numbers quickly become obsolete. The reader will know the severity of the pandemic and the importance of methodological development without statement of exact numbers. This comment reflects my personal opinion and it is completely up to the authors to choose how to phrase this section.

We agree with the reviewer that a more timeless start to the introduction makes more sense. Therefore, as suggested, we have changed this section of the manuscript, which now reads as follows:

“The COVID-19 pandemic, caused by the novel coronavirus SARS-CoV-2 [1], originated in Wuhan (China) in December 2019 and rapidly spread across the globe, resulting in substantial mortality [2, 3] and widespread economic damage. Until a vaccine becomes available, public health strategies centred on reducing the rate of transmission are crucial to mitigating the epidemic, for which effective and affordable testing strategies to enable widespread population surveillance are essential.”

2.Tables listing primers and probes should include the amplicon (PCR product) length for each primer-probe pair. Product length is an important consideration for fragmented RNA samples, such as for example heat-inactivated or longer-term stored samples. It should not be put on the reader to find out the amplicon lengths.

To provide the reader with this information, the revised manuscript now includes the following:

1. As suggested, the amplicon length for each primer pair is added to all tables that list primers and probes (PCR products: RdRp – 100 bp; E- 113 bp; N1 – 72 bp; N2 – 67 bp);
2. A diagram in a new Fig 1 indicates the positions of all primers and probes on the SARS-CoV-2 genome along with amplicon length.
3. A supplementary SnapGene file with primers and probes on the SARS-CoV-2 (Wuhan-Hu-1) genome to allow readers to look at further details in the context of the viral genome.

   3.Line 131: "To confirm sensitivity using total viral RNA, nucleic acids isolated from cultured SARS‐CoV‐2 were also used to make a dilution series (10^‐1 to 10^‐6)." I lack a methodological description how viral nucleic acid was quantified. It is not entirely trivial to separate viral RNA from RNA contributed from the cells used for the in vitro expansion of the virus.

We apologise for the lack of clarity on this in our original manuscript. The purpose of this experiment was not to measure a defined number of RNA molecules, but to ensure that there was no inhibition of viral target amplification in a more complex sample by demonstrating linearity over a range of dilutions. The cultured SARS-CoV-2 positive control was provided by Prof Rory Gunson (Clinical Lead West of Scotland Specialist Virology Centre, NHS Greater Glasgow and Clyde) as inactivated supernatant from virus (strain hCoV-19/England/02/2020) propagated in cell culture. We then isolated RNA from a dilution series of this supernatant, using the methods described in our manuscript, but did not determine the precise concentration. The RT-qPCR data for this series shows a good fit and amplification efficiency, similar to what was found for the IVT RNA, and QCMD virus calibration curves (new Fig 2). The known copy number of the QCMD virus (as determined by ddPCR) allowed us to calculate that the concentration of the virus in the supernatant provided to us was between 0.7 and 2.2 x 105 copies/ml, with viral RNA detected down to between 0.7 and 3 copies with our N1E-RP and N2E-RP assays. We have substantially restructured the results section, and hope to have made the way we used the different viral controls clearer in the revised version of the manuscript.

4.Line 150: "All positive and negative controls gave the expected results (Table S4)" I don't like the exact formulation since it is not clear for the reader what are the "expected results", including the "expected" quantitative results (Ct).

We agree that the use of “expected results” does not provide the reader with sufficient information. We have therefore changed this to:

“Results for controls were as anticipated (Table S4), with signal absent (undetermined) for SARS-CoV-2 and RPP30 targets for the negative controls, and Cq values for the SARS-CoV-2 RNA positive control (50 copies) similar to those obtained previously (Fig 2A).”

In addition, we now provide more information on the precise nature of the negative and positive controls with Table S4:

“-ve (extr), negative control with viral transport medium after RNA isolation (does not contain SARS-CoV-2 or human material; does contain PhHV);

-ve, negative control containing water only (should not contain any RNA)

+ve, positive control with in vitro transcribed RNA (50 copies; contains SARS-CoV-2 target RNA, does not contain human or PhHV nucleic acids)”

Reviewer #3 (Significance (Required)): This study provides an alternative multiplex RT-PCR assay to detect SARS-CoV-2 infection. I find the results important and useful for the research and medical community.

Rebuttal references

1. Zhu N, Zhang D, Wang W, Li X, Yang B, Song J, et al. A Novel Coronavirus from Patients with Pneumonia in China, 2019. N Engl J Med. 2020;382(8):727-33. Epub 2020/01/25. doi: 10.1056/NEJMoa2001017. PubMed PMID: 31978945; PubMed Central PMCID: PMCPMC7092803.
2. Brown JR, O’Sullivan D, Pereira RP, Whale AS, Busby E, Huggett J, et al. Comparison of SARS-CoV2 N gene real-time RT-PCR targets and commercially available mastermixes. 2020:2020.04.17.047118. doi: 10.1101/2020.04.17.047118 %J bioRxiv.
3. Arevalo-Rodriguez I, Buitrago-Garcia D, Simancas-Racines D, Zambrano-Achig P, del Campo R, Ciapponi A, et al. False-negative results of initial RT-PCR assays for COVID-19: A systematic review. 2020:2020.04.16.20066787. doi: 10.1101/2020.04.16.20066787 %J medRxiv.
4. Watson J, Whiting PF, Brush JE. Interpreting a covid-19 test result. BMJ. 2020;369:m1808. Epub 2020/05/14. doi: 10.1136/bmj.m1808. PubMed PMID: 32398230.
5. Woloshin S, Patel N, Kesselheim AS. False Negative Tests for SARS-CoV-2 Infection - Challenges and Implications. N Engl J Med. 2020;383(6):e38. Epub 2020/06/06. doi: 10.1056/NEJMp2015897. PubMed PMID: 32502334.
6. Vogels CBF, Brito AF, Wyllie AL, Fauver JR, Ott IM, Kalinich CC, et al. Analytical sensitivity and efficiency comparisons of SARS-CoV-2 RT-qPCR primer-probe sets. Nat Microbiol. 2020. Epub 2020/07/12. doi: 10.1038/s41564-020-0761-6. PubMed PMID: 32651556.
7. Bustin SA, Benes V, Garson JA, Hellemans J, Huggett J, Kubista M, et al. The MIQE guidelines: minimum information for publication of quantitative real-time PCR experiments. Clin Chem. 2009;55(4):611-22. Epub 2009/02/28. doi: 10.1373/clinchem.2008.112797. PubMed PMID: 19246619.

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

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Referee #3

Evidence, reproducibility and clarity

In this study Reijns et al developed a multiplex RT-PCR assay (alternative primer-probe sets and enzyme mixes) to detect SARS‐CoV‐2 and internal controls. The authors conclude that their assay performed equally well as established commercial kits. The authors also demonstrated that nose‐and‐throat swab samples have considerable variability in patient material content (>1,000‐fold variability). High variability is expected, but it is still important to substantiate this notion with numbers. Overall, I like the study and find it methodologically sound. Sample numbers in the tests are in most cases good. I have very few objections and hope to see the manuscript published soon.

SPECIFIC COMMENTS:

1."The COVID‐19 pandemic originated in Wuhan (China) in December 2019 and at the time of writing has infected more than 13.1 million people worldwide, resulting in well over 0.57 million COVID‐19‐related deaths..." I suggest a more timeless starting of the introduction, not pointing out exact number of infections and deaths since these numbers quickly become obsolete. The reader will know the severity of the pandemic and the importance of methodological development without statement of exact numbers. This comment reflects my personal opinion and it is completely up to the authors to choose how to phrase this section.

2.Tables listing primers and probes should include the amplicon (PCR product) length for each primer-probe pair. Product length is an important consideration for fragmented RNA samples, such as for example heat-inactivated or longer-term stored samples. It should not be put on the reader to find out the amplicon lengths.

3.Line 131: "To confirm sensitivity using total viral RNA, nucleic acids isolated from cultured SARS‐CoV‐2 were also used to make a dilution series (10^‐1 to 10^‐6)." I lack a methodological description how viral nucleic acid was quantified. It is not entirely trivial to separate viral RNA from RNA contributed from the cells used for the in vitro expansion of the virus.

4.Line 150: "All positive and negative controls gave the expected results (Table S4)" I don't like the exact formulation since it is not clear for the reader what are the "expected results", including the "expected" quantitative results (Ct).

Significance

This study provides an alternative multiplex RT-PCR assay to detect SARS-CoV-2 infection. I find the results important and useful for the research and medical community.

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

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In this manuscript, Reijns and colleagues describe an approach to detect the causative agent of COVID-19, the beta coronavirus SARS-CoV-2, using an inexpensive in-house multiplex RT-qPCR. Concomitantly, viral E, N and RdRP(probe P2) as well as human RPP30 and a herpesvirus nucleic acid are also detected in order to monitor both the sample quality and the sample preparation. Reijns et al. performed testing on a huge amount of samples and used the data to describe the strength and limitations of the assay. The data is sound and give a very good impression of the 4-plex PCR capabilities. I read manuscript fluently and consider as linguistically very good. However, I still have a few comments and remarks that would strengthen the manuscript:

Major issues:

In the first section of the results section, many primer / probe conditions are given that make the reading flow difficult. Instead of using (data not shown) it would be helpful to use a table or a graphic to illustrate the various approaches. In general, I suggest to replace Ct by Cq, since the IVT standards are a quantification method.

There has already been a change away from the initial E and RdRP gene based assay because of the published sensitivity issues and the use of degenerate bases as well as the detection of unspecific nucleic acids for E gene). In particular, it has been shown that the Sarbeco-E-yields false positive results (Toptan et al. 2020 (https://doi.org/10.3390/ijms21124396), Konrad et al. 2020 (https://doi.org/10.2807/1560-7917.ES.2020.25.9.2000173)), so that many laboratories do not consider E-gene-based results for borderline samples anymore. In this manuscript, the authors should comment on why they still use the results from the E gene / RdRP and describe their experience.

In this manuscript, it should be indicated that the SARS-CoV-2 specific Probe P2 (according to Corman et al. 2020) was used. The reason for lower sensitivity due to nucleotide ambiguity and mismatch has to be explained in more detail. In addition to Corman et al. 2020 (see reference 2), Toptan et al 2020 (https://doi.org/10.3390/ijms21124396) might serve as helpful literature. With regard to the marginally positive samples that were not consistent in all assays, were the PCR products analyzed using high-resolution PAA genes and, if possible, sequenced? The sequencing approach (Sanger or NGS) offers the final characterization of the PCR products (especially for pan-genotypic primers such as E-Sarbeco). The samples declared as "inconclusive" could be further characterized in this way.

The normalization in figure 3 should be also explained in the main text. Especially, why this approach was used for normalization. Nonetheless, it looks like the normalized values wills cluster much more strongly than those corresponding to the actual values. The authors should comment on this phenomenon. It appears that the higher cq values (less virus) are subject to a strong correction factor more often than high values. Are there any statistical relevant tendencies towards this phenomenon? For everyday clinical practice, does this mean that low samples Cqs (mostly) only reflect the quality of the sample, but not the viral load? Finally, it remains somewhat unclear to what extent the Cq values of the RPP30 should have an influence on the routine diagnostics. The authors discuss that a fixed cutoff value would be a possibility to sort out poor swab samples, but if a cq value is available it would also make sense to generate a kind of quality score that can display the significance of a test. It would be helpful if the authors could comment on this or other possibilities.

Over the past few months, more and more virus subtypes have formed through the manifestation of point mutations (and amino acid substitutions). The authors should therefore definitely comment on the current strains as to whether all primers / probes are able to detect the virus variants circulating worldwide without loss of sensitivity. Along this line,which virus strains were used for the cultivation as described in line 131? Is sequence data available? If so, it would provide helpful information to characterize the viral strain.

Line 206ff: In my opinion, this section belongs more to the discussion part than to material and methods that describe the technical implementation.

Is there a loss of sensitivity compared to the single PCRs? This data is very important and useful for other users. They should therefore be included explicitly in the manuscript (supplements).

Minor issues:

Line 15 ff.: Source is missing, is this WHO-data?

Fig S3: How was the digital droplet PCR carried out? A brief description should be included in the legend text.

Figure 1a: PCR efficiencies are missing.

Line 145: MS2 appears, but without explaining the context. This should be improved here with additional information (this does not appear until line 154).

Page 15, H20 instead of H20, reaction mix instead of Reaction mix.

Significance

The novel coronavirus SARS-CoV-2 is the causative agent of the acute respiratory disease COVID-19 which has become a global concern due to its rapid spread and high death rate. While some patients have no symptoms at all, but are still able to spread the virus, others have severe symptoms, often with fatal outcome. The gold standard in SARS-CoV-2 detection is the RT-qPCR approach, however, the high cost commercial kits are available in limited amounts only. The issue of the scarcity of resources is still an highly important issue, especially in terms of the incredibly rapidly increasing number of cases worldwide. Thus, the manuscript is of significance for the field and timely. Especially, diagnostic laboratories in low-income countries that are involved in the managing the pandemic but also researchers will benefit from this manuscript and save resources.

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Referee #1

Evidence, reproducibility and clarity

In order to improve SARS-CoV-2 diagnostics, Reijns et al. developed a multiplexed RT-qPCR protocol that allows simultaneous detection of two viral genes, one housekeeping gene as well as an external gene as an extraction control. Compared to running parallel assays to detect genes individually, the turnaround time is much shorter and reagents are saved. Furthermore, the presented data suggest that the assay is more sensitive than commercial kits. The authors also propose the detection of the human housekeeping gene as a measure of sample quality control. In principal, this work has potential but the manuscript itself needs a better structure.

Major concerns:

The authors have used the Takara RT-qPCR kit for their study. Did the authors try other commercial kits? Can the authors elaborate on the supply chain of the Takara kit? Could it cover population testing in case of shortages of other commercial kits?

For better comparison, is it possible to give information on which primers the commercial kits are based on? Also, explain better the primers used in this study. For example, the N1 and N2 primers are directed against different regions of the SARS-CoV-2 N gene.

The result section needs a better structure as the first two pages do not refer to any of the main figures. For example, in which figure or table can the reader find the data that are discussed in lines 83 to 87?

Table S1, instead of current Table 1, could be moved to main figures as it contains the important finding that the multiplexed assay may be more sensitive than the commercial one. The authors identified some samples that scored negative in commercial assays but positive in their new assay. This is important, however, the possibility of detecting false positives should be strengthened in a "Discussion" section.

Figures 1 to 3 have different panels which seem to be redundant. For example, Fig 1 A and B, Fig 2 B and C, Fig 3 C and D.

Figure 1: Give a rational why comparing before and after extraction. This heavily depends on the extraction method and not on the detection itself. In addition, IVT RNA does not reflect the complexity of a clinical specimen. This is rather confusing and deviates from the important findings.

Figure 3: Were any of the negative samples/patients tested with an undetectable housekeeping gene, re-test positively? Did adding this housekeeping gene as a control actually improve the detection of any patient samples? If the authors want to convince the readership of this quality control, experimental evidence should be provided.

Fig 3C and D seem to contain this information somewhat, as here, the values were normalized and the CT values for the E and N gene decreased. Nevertheless there is no real explanation of this figure provided in the Result section at all. While this figure has potential, the authors have to keep in mind that the number of cells in a swab can be affected by many biological factors, including age, sample timing, inflammation of the respiratory tract, etc. In addition, viral genomes can exist intra- as well as extracellular, in the form of free virus. So even in the absence of human cells/detectable housekeeping genomes, viral RNA can be or should be present in a sample in case of infection. This explains (probably) why a correlation between detectable housekeeping gene and viral RNA is absent (Fig 3A and B?). This entire Fig 3 just needs a better explanation. The provided text does not describe any results and should go into a "Discussion" section.

Self-swabbing is surely a potential source of variability and false-negatives, but many publications have shown the suitability of saliva testing. This should also be discussed and would probably negate the need for such a quality control.

Which assay works better, the N1E-RP or the N2E-RP assay? A final conclusion is missing here.

Significance

Naturally, in this pandemic, this topic is important as sensitive and affordable methods to detect SARS-CoV-2 infections are in need. This Reviewer agrees that multiplexing could be an elegant approach to fill this need.

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Reply to the reviewers

We thank the reviewers for their feedback and constructive comments to our work. We provide here a point-by-point response to the comments of Reviewers #1, #2 and #3 (text in grey and italic).

Responses written in plain text correspond to Reviewer comments that have been addressed in the revised version of the manuscript provided at this stage of the review process (referred-to as “revised version I” below).

Reponses written in bold text correspond to comments that need further experiments. The list of experiments we intend to perform to address these comments is provided in a separate document (Revision plan). The results of these additional experiments will be included in a later revised version of the manuscript referred-to as “revised version II” below.

Reviewer #1

The manuscript addresses an important topic, the posttranscriptional maturation of ribosomes. This topic is inherently interesting because we normally think of ribosome biogenesis as a sequential series of steps that automatically proceeds and cannot be "accelerated" in physiological conditions, but only "delayed" in the presence of genetic mutations. In short, the manuscript proposes that RIOK2 phosphorylation by the action of RSK, below the Ras/MAPK pathway promotes the synthesis of the human small ribosomal subunit.

I honestly admit that I have some difficulties in reviewing this manuscript. The quality of the presented data is, in generally, good. However, overall I find the whole manuscript preliminary and I am not much convinced of the conclusions. Several aspects are superficially analyzed. In short, I think that most of the conclusions are not fully supported by the data because shortcuts are present. A list of all the aspects that I found wrong are listed.

Biological issue

1. _The authors claim that the effects of the inhibition of the maturation of ribosomes by acting on a pathway upstream of RIOk2 are limited to the 40S subunit. This is far from being a trivial point, for the following reason. RIOK2 is known to affect the maturation of 40S ribosomes. Hence, the fact that using an upstream inhibitor of the MAPK pathway such as PD does not inhibit 60S processing in reality would argue against a biologically relevant control in ribosome maturation (of the MAPK patheay). Have the authors considered this? In a way, also, given the fact that the mutants confirm a role in 18S final maturation, it is a bit complex to put all the data in a clear biological context.

We agree that we put more emphasis on the effects on the pre-40S pathway than on the pre-60S pathway in the original manuscript but we did not claim that the effects of PD or LJH inhibitors of the MAPK pathway are restricted to the 40S subunit. We described that the effect of PD or LJH on the 32S was less severe than on the 30S, and we did mention variations of the 12S intermediate. These changes are in the same range of amplitude as the changes in the 21S and 18S-E intermediates in the small subunit pathway. The Northern blot data concerning the pre-60S pathway were placed in the supplementary material of the original manuscript, which may have left the reader with an impression of lesser emphasis. We rephrased this part in the present revised version I of the manuscript (Page 6, Line 26) and we now show the pre-40S and pre-60S intermediates on the same figures (Figures 1A and 1C).

In addition, we will probe more exhaustively the intermediates of the pre-60S pathway in the revised version II of the manuscript as described in the revision plan. These data will be complemented with metabolic labeling experiments to provide a more dynamic analysis of the pre-rRNA processing defects resulting from inactivation of the MAPK pathway. Furthermore, as requested by Reviewer #2 (see below), we will quantify more accurately these data.

A number of specific issues will be concisely described.

Manuscript very well written. Data do not always support the strong conclusions. Low magnitude of the observed effects.

In introduction the authors make a general claim that ribosome biogenesis is one of the most energetically demanding cellular activities. This statement lingers in the literature since 15 years but in reality it has never been formally proved for mammalian cells, and certainly not for HEK293 cells. The original statement, to my knowledge, can be traced by some obscure statement referred to the yeast case and then repeated as a truth. In conclusion, beside being a very banal observation, it should be referenced.

We agree with this comment of Reviewer #1. The original statement has been proposed by Jonathan R. Warner (Warner, 1999, TiBS and references therein) and data from the Bähler group also supported this statement (Marguerat et al., 2012, Cell). However, these data were indeed referring to yeast (S. cerevisiae and S. pombe). In the present revised version I of the manuscript, we introduced the reference of a review providing quantitative data of ribosome biogenesis in human cells (Lewis & Tollervey, 2000, Science) and we modified the problematic sentence as follows:” Growing human cells produce around 7500 ribosomal subunits per minutes (Lewis and Tollervey 2000), which represents a significant expenditure of energy.” (Page 4, Line 1).

Growth factors, energy status are not cues but are proteins or metabolites (introduction).

We agree with this comment of Reviewer #1. We changed the text accordingly in the revised version I of the manuscript (Page 4, Line 8).

Authors write about mTOR without making statements on mTORC1/2. This is very obsolete. Also I am not sure that the choice of Geyer et al., 1982, and subsequent papers makes much sense. At the very minimum TOP mRNA concepts and mTORC1 must be defined.

We provide more details on the mTOR pathway in the revised version I of the manuscript according to Reviewer #1’s suggestions (Page 4, Line 13 and Page 5, Line 3).

The authors claim that their work fills a major gap between known functions of MAPK and cytoplasmic translation. I would not be so sure about it.

Our original sentence stated that “our work fills a major gap between currently known functions of MAPK signaling in Pol I transcription and cytoplasmic translation”. Indeed, although MAPK signaling was known to regulate Pol I transcription and cytoplasmic translation, the impact of the pathway on the post-transcriptional steps of ribosome synthesis, namely pre-ribosome assembly and maturation, has been very little investigated and remains poorly understood. Our data provides the first example of a detailed mechanism of regulation of the maturation of pre-ribosomal particles by the MAPK pathway. Reviewers #2 and #3 seem to agree with this point:

Reviewer #2: “However, there is a lacking mechanistic connection of signaling pathways to pre-rRNA processing and maturation steps of ribosome biogenesis. The authors set out to provide a specific example of a direct target of MAPK signaling, RSK that regulates pre-rRNA maturation through the phosphorylation of a ribosome assembly factor (RIOK2), offering for the first time providing mechanistic insight into MAPK regulation of pre-rRNA maturation.”

Reviewer #3: “With these provisos, the work is technically good and will be of considerable interest to the field. The post-transcriptional regulation of ribosome synthesis is increasingly recognized a significant topic.”

Results. Authors start with a major mistake, i.e. that PMA selectively stimulates the MAPK pathway. Perhaps it stimulates, certainly it does not do it selectively.

We agree with this comment of Reviewer #1. We removed the term “selectively” in the problematic sentence (Page 6, Line 8).

RIOK2 phosphosites are first found by bioinformatics analysis. It should be noted that the predicted phosphosite (S483) is found only in a limited set of datasets from MS databases. The actual importance of this site would not emerge from unbiased studies. Also, there are many other phosphosites that were not analyzed in this study.

We agree with Reviewer #1 that phosphorylation of S483 of RIOK2 has been detected in a limited number of mass spectrometry datasets, but these datasets have been reported in high impact journals (Nature Methods, Mol Cell Proteomics, Science), attesting of the quality of these studies

As mentioned by Reviewer #1, there are several other phosphosites within RIOK2 that were not analyzed in our study. We provided the list of these phosphosites in Supplementary Table S1 of the original manuscript. Besides T481 and S483, none of the other sites belong to consensus motifs recognized by ERK or RSK at medium and high stringency. They are therefore less relevant to our study. We only analyzed phosphorylation at S483 because: (i) our mass spectrometry analysis revealed that S483 is the only phosphosite in RIOK2 whose level increases upon MAPK activation but not in the presence of the MAPK inhibitor PD184352 (Figure 2B); (ii) our in vitro kinase assay showed that the phosphorylation level of RIOK2 by RSK is residual when S483 is replaced by a non-phosphorylatable alanine (Figure 3D); (iii) our data presented in Figure 2C further show that mutation of T481 to an alanine does not prevent RIOK2 phosphorylation on RxRxxS/T motifs upon stimulation of the MAPK pathway.

We clarified this point in the relevant part of the result section of the revised version I of the manuscript (Page 7, Lines 16 and 24, Page 8, Line 17 and Page 9, Line 5).

Throughout the paper the authors use the word strongly, significantly, but the actual effects seem in general quite marginal.

We agree with Reviewer #1 that some of the phenotypes described in the manuscript are modest, in particular the phenotypes resulting from the S483A mutation of RIOK2, which is not aberrant for a point mutation. We rephrased several sentences throughout the manuscript to soften the formulation in the description and interpretation of the data and in the conclusions.

Discussion. The authors claim that they provide solid evidence on MAPK signalling to ribosome maturation. At the very best this is circumstantial evidence for the 40S maturation.

We rephrased the sentence accordingly (Page 16, Line 5): “Our study provides evidence that MAPK signaling applies another level of coordination during ribosome biogenesis, by directly regulating pre-40S particle assembly and maturation.”

Figure 1.

Unclear why LJH should increase P-ERK.

A negative feedback loop has been described in the MAPK pathway whereby RSK activation partially inhibits ERK phosphorylation (Saha et al., 2012, Horm Metab Res; Dufresne et al., 2001, MCB; Schneider et al., 2011, Neurochem; Re Nett et al., 2018, EMBO Rep). Inactivation of RSK with LJH alleviates this inhibition, which results in increased phosphorylation levels of ERK.

We added this information in the revised version of the manuscript along with the corresponding references (Page 6, Line 17).

General lack of quantitation (sd, replicates, bars). Experiment done only on a single cell line in a single experimental setup.

As also requested by Reviewer #2 (Major comment 1.), we applied in the revised version I of the manuscript RAMP quantifications to all Northern blot data. We included error bars corresponding to biological replicates.

Furthermore, in order to validate the impact of the MAPK pathway on pre-ribosome assembly and maturation, we plan to perform the same experiments using PD inhibitors in different cell lines and we will provide a figure with accurate RAMP quantifications, error bars and statistical significance, in the revised version II of the manuscript (see revision plan).

Very different effects on 21S by LJH, PMA and siRNA for RIOK2. Overall the message given by the authors is to me mysterious.

We assume that the reviewer wanted to point out the difference between PMA, PMA+LJH and shRNA for RSK since we did not perform RNAi targeting RIOK2. We agree with this comment. We believe that this difference is likely due to experimental setups that are different between both experiments. In the experiment using inhibitors, we assessed short-term effects of RSK inhibition after acute stimulation of the MAPK pathway (starved cells stimulated with PMA), while in the experiment using shRSK, we monitored long term effects of RSK depletion in serum-growing cells in which other signaling pathways are also active. Prolonged RSK depletion is likely to induce pleiotropic cellular effects, which would interfere with ribosome biogenesis both directly and indirectly. These differences probably explain the variable effects on the 21S intermediate. However, in both experiments we do observe an accumulation of the early 30S intermediate, consistent with the phenotype observed when ERK is inactivated (PD inhibitor), therefore indicating that RSK regulates some post-transcriptional stages of ribosome biogenesis.

To make our results clearer we have withdrawn the experiments using shRSK to avoid the risk of showing indirect effects due to the prolonged absence of RSK. Instead, we included RAMP analyses with error bars from 2 biological replicates using PD and LJH inhibitors (Figure 1B).

Figure 2.

Several red flags. For instance in 2C the loaded levels of RIOK2-HA loaded are clearly less than the ones of the other genotypes, hence the conclusion on P-RIOK2 is not convincing.

Our aim in this experiment was to compare the impact of PMA treatment on the phosphorylation levels of different RIOK2 mutants (T481A, S483A, double mutant). For a given mutant, the levels of RIOK2 loaded in the two conditions (i.e. not stimulated and PMA stimulated) are very similar and we therefore assume that our conclusions are valid.

We nevertheless plan to repeat these experiments and quantify the data for the revised version II of the manuscript.

Staining with anti-P RIOK2 lacks controls, how can be sure that the signal is due to the phosphate? Phosphatase treatment?

We fully agree with Reviewer #1 and we did perform an experiment showing that the phosphorylation signal disappears following treatment of the protein extracts with λ-phosphatase. We did not show these data in the original version of the manuscript because of space limitations. We added these data in the supplementary material of the revised version I of the manuscript (Supplementary Figure S2B) and amended the text accordingly (Page 7, Line 24)

Why FBS does not lead to ERK staining in HEK293? There are plenty of growth factors in FBS that should lead to ERK phosphorylation. I do not understand this experiment.

We agree with this comment. Addition of serum to starved cells does lead to ERK and RSK phosphorylation but with a much lesser efficiency compared to stimulation by EGF and PMA. ERK phosphorylation is barely visible on the exposure shown in Figure 2D but RSK-phosphorylation is clearly observed, although the signal is much weaker compared to EGF and PMA treatments. It is common to observe a stronger response with purified PMA and EGF (see Carrière et al., 2011, JBC ; Ray et al., 2013, Oncogene). There are indeed several growth factors in the serum, but the most abundant (Insulin, IGF1, TGF) are present at ng/ml concentration, while EGF is used at 25 µg/ml in Figure 2D. Moreover, they are not very strong activators of the Ras/MAPK pathway, and it is also possible that after 20 min of FBS treatment the phosphorylation is in the decreasing phase.

In the present revised version I of the manuscript, we included a set of western blots from another experiment showing the same results but of better quality to make the effects more visible (Fig. 2D). We also provided quantifications of phosphorylation of RIOK2 and associated statistical analyses (Fig. 2E).

Figure 3. In vitro phosphorylation, if I understood, it relies on a truncated version of RIOK2. Why? Is the folding of the full length protein not permissive to in vitro phosphorylation?

We did not test phosphorylation of the full length RIOK2 protein in vitro because RIOK2 has been reported to auto-phosphorylate (Zemp I. et al., 2009, JCB) and we were concerned that this auto-phosphorylation activity of RIOK2 in addition to RSK phosphorylation may render this experiment inconclusive.

HA-RSK3 is less?

It was reported that RSK3 is insoluble when over-expressed (Zhao et al., 1996, JBC), which explains the lower levels of protein recovered in our soluble extract. The information was present in the legend of Figure but we transferred it to the main text of the result section in the present revised version I of the manuscript (Page 10, Line 3).

Figure 4. Immunofluorescence is low mag, difficult to understand.

We agree with Reviewer #1. We modified the FISH experiment figure to show cells with a higher magnification and we provided more details in the text (Page 12, Lines 20-25) to facilitate the understanding of the data.

I really like the experiments with RIOK2 mutants, however I wonder what about protein levels after the knock-in? Given the 18S phenotype overlap between the phenotype of the RIOK2 loss of function with the S483A, testing protein level becomes of the utmost importance.

We checked RIOK2 protein levels and observed that the mutations do not decrease the level of RIOK2. On the contrary, the mutations slightly increase RIOK2 levels. Therefore, we are pretty confident that the phenotypes resulting from expression of RIOK2 mutants do not result from defects in the global accumulation of the protein. These data have been added to Figure 4C of the revised version I of the manuscript and we amended the text accordingly (Page 12, Line 5).

Figure 5. Low quality IFL.

Our aim in preparing this figure was to show many cells in the different images to show that the effect of our mutation was homogenous at the level of cell populations. The drawback is that cells are small and look blurred. We improved the quality of the figure in this revised version I of the manuscript with new images from the same experiment, showing less cells with a higher magnification.

Hard to think that histogram quantitation of nuclear versus cytoplasmic staining are reliable in the absence of fractionation, better quantitation, experiment done in other cell lines and so on.

We provide in this revised version I of the manuscript a supplementary figure explaining the procedure we used to quantify the fluorescence data (Supplementary Fig. S7).

Furthermore, to confirm this result using other experimental conditions and cell lines, we will transfect HEK293 and HeLa cells with plasmids expressing GFP-tagged RIOK2 WT or the S483S mutant and we will compare the kinetics of nuclear import of both proteins upon inhibition of pre-40S particle export by leptomycin B using fluorescence microscopy and GFP quantifications. Second, we will transfect HeLa cells with plasmids expressing HA-tagged RIOK2 WT or S483A and perform fractionation assays to monitor their presence in both cytoplasmic and nuclear compartments. We will include these data in the revised version II of the manuscript.

However, very beautiful Fig. 5E perhaps the best of the paper shows also mobility shift driven by S483, thus supporting posttranslational modifications.

We thank Reviewer #1 for this comment. We added the note on the evidence of RIOK2 post-translational modification in the result section (Page 14, Line 9).

Fig. 6. IFL studies are really impossible to interpret.

We improved the quality of the figure with new images from the same experiment, showing less cells with a higher magnification. NOB1 IF data and quantifications have been transferred to the supplemental material (Supplemental Fig. S4A and S4B) to clarify the figure. In addition, we provided more explanations on the principle of this experiment and expected results in the text (Page 15, Line 9).

The effects on RIOK2 release (this figure) and 18S maturation (Fig. 5) are very clear and of great quality.

We thank Reviewer #1 for this comment.

Overall conclusions. The manuscript tends to overinflate the meaning of several experiments. What to me is very clear and interesting is that the the authors provide clear evidence that S483A mutants have a defect in 40S maturation. Whether this is due to MAPK signalling, is only circumstantial. I would suggest to build up on the strong findings and eliminate ambiguous data.

We do not fully agree with this comment of Reviewer #1. If mutation S483A were simply a partial loss of function mutation, this would not be of strong interest for the subject of this manuscript. It would just indicate that S483 is important for RIOK2 function independently of its phosphorylation status. Our data show that the impact of S483 mutation on pre-rRNA processing and other phenotypes is different depending on whether the serine is converted to an alanine (phosphorylation mutant) or to an aspartic acid (phospho-mimetic mutation). These data are a strong indication that what matters is not simply the serine residue by itself but its phosphorylation status.

Reviewer #1 (Significance (Required)):

The paper deals with an important topic, namely whether a regulation of ribosome maturation exists, and how it is mechanistically regulated. In this context, the analysis of the ERK pathway is highly needed considered that most works deal with effects of the PI3K-mTOR pathway, and the parallel, yet important RAS-ERK pathway, is less understood.

As a final note, we should consider that S6K downstream of mTOR, and ribosomal S6K, downstream of ERK have been considered to share some substrates.

We introduced this information in the revised version of the manuscript (Page 19, Line 20). A related comment has been raised by Reviewer #3 (see below, Caveat #2).

The manuscript is interesting, but several statements given by the authors are rather superficial. An example, listed in the previous section, relates to the linguistic usage of mTOR kinase, instead of detailing whether we are dealing with mTORc1 or mTORc2.

We agree with this comment of Reviewer #1. Given that the main focus of this manuscript is the regulation by the MAPK pathway, we had chosen to put less emphasis on mTOR in the introduction. However, we added more precise information on mTOR in the present revised version I of the manuscript to address this comment (Page 4, Line 13 and Page 5, Line 3).

A second gross mistake is the definition of PMA as a stimulator of the ERK pathway. If this is certainly true, this is historically not correct as seminal papers by the group of Parker define this drug as a stimulator of conventional PKC kinases. In short, this paper is a step back in knowledge from the perspective of the literature context.

We are a bit confused by this comment because seminal papers from the Parker group clearly state that PMA activates the MAPK pathway via PKC (Adams and Parker, 1991, FEBS Lett.; Ways et al., 1992, JBC; Whelan et al., 1999, Cell Growth Differ.). We agree, as mentioned earlier by Reviewer #1, that PMA is not specific to MAPK, a comment that has been addressed above.

All people interested to the crosstalk between ribosome maturation and signaling pathways will be certainly read this manuscript.

My expertise is within the ribosome biology and signalling field.

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

There have been mechanistic connections of various signaling pathways to regulation ribosome biogenesis steps including rDNA transcription by RNA polymerase I and III, ribosomal protein transcription, and differential mRNA translation efficiency. However, there is a lacking mechanistic connection of signaling pathways to pre-rRNA processing and maturation steps of ribosome biogenesis. The authors set out to provide a specific example of a direct target of MAPK signaling, RSK that regulates pre-rRNA maturation through the phosphorylation of a ribosome assembly factor (RIOK2), offering for the first time providing mechanistic insight into MAPK regulation of pre-rRNA maturation.

The authors observe slight pre-rRNA processing defects upon the use of RSK inhibitors and RSK depletion. They identified several candidate ribosome assembly and modification factors containing the canonical RSK substrate motif, including the RIOK2 kinase. Phosphorylation at this motif was verified to be specifically phosphorylated by RSK1 and 2 isoforms in cells and in an in-vitro kinase assay. The authors produced RIOK2 knock-in eHAP1 cell lines expressing non-phosphorylatable or phosphomimetic versions of RIOK2, observing slowed cellular proliferation, decreases in global translation, slight pre-rRNA processing abnormalities, but not changes in overall mature 18S rRNA levels. More specifically, the authors defined the inability of RIOK2 to be phosphorylated leads to defects in RIOK2 dissociation from the pre-40S ribosomal subunit in an in-vitro assay, and inability for it to be recycled for reuse in pre-ribosome export from the nucleus to the cytoplasm by immunofluorescence.

Overall, the authors provide an interesting mechanism of MAPK regulation of a ribosome assembly factor RIOK2. However, they fail to provide the necessary reproducibility, controls, quantification, and consistent results between experiments to support their hypotheses.

Major Comments:

1. The northern blots reported throughout the manuscript are lacking proper reproducibility and quantification. First, the northern blots are lacking a loading control, which is necessary to report fold changes that are being measured across treatments. Please include a proper loading control (i.e. 7SL or U6 RNAs). Additionally, more rigorous analysis of the pre-rRNA precursor levels through ratio analysis of multiple precursors (RAMP) (Wang et al 2014) can be completed to provide a clearer depiction on which precursor(s) are accumulating. It is unclear for the Figure 1 northern blots if there were replicates completed and what the error bars represent in Figure 1B. Please report replicates, so that statistical analysis can be completed on the differences in precursor relative abundance. This need is emphasized by the small changes observed in pre-rRNA levels (less than 2 fold) between conditions.

As mentioned above (Reviewer #1), we applied in the revised version I of the manuscript RAMP quantifications to all Northern blot data. These quantifications are shown as separate panels in the figures of the revised manuscript.

Furthermore, we are planning to repeat the Northern blot experiments of Figure 1 to obtain biological replicates in other cell lines. We will probe the membranes to detect the 7SL RNA as a loading control in all these experiments. We will perform RAMP analyses on all these Northern blot experiments to provide more accurate quantifications of the pre-rRNA levels in the different conditions. These data will be included in the revised version II of the manuscript.

1. The western blots reported throughout the manuscript are lacking proper reproducibility and quantification. For example, the western blots validating RSK1 and RSK2 depletion in Figure 1C lack a proper loading control. Additionally, it is unclear if there are replicates completed and there is lack of statistical analysis to determine if the changes are significant. Please include loading controls, replicates, and quantification of the western blots throughout the manuscript.

We have included actin levels as loading controls in several figures (Figures 2D, 3A, 3C, 3E, 4C) of the revised version I of the manuscript. We also added phosphorylated Rps6 at Ser235/36 to monitor RSK activity in Figures 1A, 2D, 3A.

We provided quantifications and associated statistical analyses of phosphorylation of RIOK2 presented in Figures 3A and 3C of the revised version I of the manuscript. We also included quantifications of the in vitro phosphorylation assays presented in Figures 3F and 3G.

We are nevertheless planning to repeat and quantify more accurately the western blot experiments presented in Figures 2A, 2C and 3E of the revised version I of the manuscript. These data will be included in the revised version II of the manuscript.

1. Please report the full bioinformatic analysis of the RSK substrate motif search among human AMFs including other AMFs found in this search. A sorted list format would be valuable for the reader to understand other potential RSK substrates involved in ribosome biogenesis.

We understand the request of Reviewer #2. Providing the full list of AMFs identified in our bioinformatic screen would be valuable for the reader, mostly because it would make clearer that RSK seems to be regulating multiple stages of the pre-ribosome maturation pathway, therefore that RSK inhibition induces pleiotropic defects in ribosome synthesis. However, we are currently working on a more global study of the impact of MAPK regulation on the post-transcriptional steps of ribosome synthesis that we would like to publish in a near future.

1. The authors report that RSK inhibition/depletion leads to accumulation of the 30S pre-rRNA, yet mutation of its target site on RIOK2 or RIOK2 depletion leads to an accumulation of the 18S-E pre-rRNA. Additionally, the phosphomimic mutation of RIOK2 leads to an accumulation of 30S, the opposite of the expected result. Please elaborate on this discrepancy in processing defects observed across experiments.

In contrast to RIOK2 which is specifically involved in the late, cytoplasmic stages of the maturation of the pre-40S particles, RSK regulates ribosome biogenesis at multiple levels. Upon activation of the MAPK pathway, RSK activates Pol I transcription in the nucleoli and promotes translation of mRNAs encoding ribosomal proteins and AMFs. In addition, our bioinformatic screen identified several AMFs at different stages of the maturation pathway of both ribosomal subunits as potential targets of RSK. These considerations imply that RSK inhibition is expected to impact ribosome biogenesis at multiple levels (Pol I transcription, availability of RPs and AMFs, export of the pre-ribosomal particles, probably several maturation steps) whereas RIOK2 inactivation more specifically delays 18S-E processing in the cytoplasm. In terms of processing, RSK inhibition induces a significant accumulation of the 30S intermediate. This is another evidence that RSK regulates pre-rRNA processing at several stages. This phenotype might result, as recently described in yeast (Yerlikaya et al., 2016, MCB), from an inhibition of RPS6 phosphorylation which affects its early incorporation into pre-ribosomes, although this has not been demonstrated in human cells. This 30S precursor accumulation affects production of the downstream intermediates and we strongly believe that this precludes accumulation of 18S-E even if the activity of RIOK2 is affected. Given the broad implication of RSK at different stages of ribosome biogenesis, it is biologically relevant to observe that inactivation of RSK does not result in the same processing defects as inactivation of RIOK2.

We nevertheless tried to make this point clearer in the present revised version I of the manuscript. We added in the supplementary material a diagram (Supplementary Fig. S1C) showing all the known and hypothetical targets of ERK and RSK in ribosome synthesis to provide the readers with a global view of the function of RSK in this process and refer to this figure in the introduction and results. In the introduction, we also emphasize more on the multiple aspects of the regulation of ribosome synthesis by ERK and RSK (Page 4, Line 18).

Concerning the phospho-mimetic mutant, it does accumulate slightly the 45S and 30S intermediates contrary to the non-phosphorylatable mutant but this is not totally unexpected. RIOK2 is incorporated into pre-ribosomes in the nucleus, at a stage that remains unclear, and constitutive RIOK2 phosphorylation may interfere with this recruitment and affect processing at an earlier stage. This point has been addressed in the discussion of the revised version I of the manuscript (Page 18, Line 7).

Are there similar results for RSK depletion/inhibition and RIOK2 release from the pre-40S and inability to import into the nucleus? If so, this could provide phenotypic consistency between these two proteins in the proposed pathway to further support the hypothesis.

We performed the same experiments as reported in Figure 6C to try to demonstrate a cytoplasmic retention of RIOK2 after leptomycin B treatment upon ERK inhibition (PD treatment). We also performed IF and cell fractionation experiments upon PD treatment. In all cases, we failed to observe the expected result. We strongly believe that we are facing here the same problem as described above for the previous comment of Reviewer #2. ERK and thus RSK inhibition leads to accumulation of the early, nucleolar 30S intermediate, indicating that the processing pathway is significantly blocked at an early stage preceding formation of the pre-40S particles in which RIOK2 is recruited. This early blockage most likely explains why we do not see the same phenotypes. We discussed this comment in the discussion section of the revised version I of the manuscript (Page 18, Line 19).

1. Mature levels of 18S rRNA are not altered in the RIOK2 mutant cell lines. This could be due to compensation in these mutant cell lines since RIOK2 is essential.

We agree with Reviewer #2 that compensation mechanisms may operate to restore mature 18S rRNA levels despite RIOK2 mutation. On the other hand, although RIOK2 is indeed essential, we may expect that the point mutation of S483 only partially affects RIOK2 function and delays the maturation of pre-40S particles but not to a sufficient extent to impact the mature 18S rRNA levels. This has been observed by others (Montellese et al., 2017, NAR; Srivastava et al., 2010, MCB).

We added this point in the discussion section of the revised version I of the manuscript (Page 19, Line 9).

Please report the mature 18S rRNA levels upon shRNA depletion and RSK inhibitors to provide insight into if this pathway significantly alters mature 18S rRNAs as a mechanism for the altered translation and proliferation observed.

We will probe the levels of the mature 18S and 28S rRNAs in these experiments and the results will be included in Figure 1 of the revised version II of the manuscript.

Minor Comments:

1. Figure 1A lower: The authors use an RSK inhibitor LJH685, that does not inhibit RSK phosphorylation S380. Therefore, another verification of RSK inhibition must be used besides RSK-pS380 abundance as for PD184352 inhibition. Please validate the usage of this RSK inhibitor in the experiments by inclusion of quantification of a direct downstream substrate of RSK, such as YB1-pS102 quantification.

We agree with Reviewer #2. We have probed the membrane with anti-RPS6 and anti-phosho-RPS6 antibodies to show the effect of LJH treatment on RPS6 phosphorylation. These data have been added to Figure 1A in the revised version I of the manuscript and the text has been updated (Page 6, Line 16).

1. Page 7, Lines 8-12: The authors state that RSK knockdown led to increases in the 45S, while the LJH685 treatment led to no changes in 45S levels due to differences in growth conditions. Please elaborate more on how growth conditions would alter 45S pre-rRNA levels. It would be expected that stimulation of the MAPK pathway would increase pre-rRNA transcription compared to steady state growth conditions. However, pre-rRNA processing northern blots are only measuring steady state levels of the precursors. Thus, an rDNA transcription assay would need to be completed to evaluate these differences.

We do observe that PMA treatment of starved cells induces an increase in 45S precursor levels, consistent with an increase in transcription but we agree that northern blot experiments measure the steady-state levels of the intermediates.

To address this comment, we propose to perform short pulse labelings with ortho-phosphate to assess synthesis of the 45S precursor independently of its processing in the different conditions. These data will be included in the revised version II of the manuscript.

1. Figure 2C: Please quantify these results to properly evaluate the role of these two phosphorylation sites in MAPK signaling.

We will repeat these experiments and quantify the results in the new version of Figure 2C.

1. Please include the RIOK2 pS483 antibody generation methodology used in this study.

We added this information in the Materials and Methods section of the revised version I of the manuscript (Page 21, Line 22).

1. In vitro kinase assay methods: Is the recombinant RSK1 the human version of the protein? Please clarify in methods.

Human recombinant RSK1 has been purchased from SignalChem. The information has been added in the revised version I of the manuscript (Page 30, Line 5).

1. Figure 4B: Please include statistical analysis of the puromycin incorporation assay.

We performed a statistical analysis of this assay out of 3 replicates. This analysis has been included in the present revised version I of the manuscript (Figure 4B).

1. Page 13, Line 18: Please explain why RIOK2 co-IP with NOB1 is important.

We added this explanation in the result section of the revised version I of the manuscript (Page 14, Line 3).

1. In vitro dissociation assay: There is no control for pulldown of entire pre-40S particles and not just NOB1 protein. Thus, it is unclear if RIOK2 is dissociating from NOB1 or entire pre-40S particles. Please reference previous literature of the methodology of this experiment if applicable. Additionally, please include controls, such as western blotting of ribosomal proteins or northern blotting of rRNA in the pulldown fraction used.

We agree with Reviewer #2. We have probed the membranes with antibodies detecting LTV1 and ribosomal protein RPS7 to show that the entire pre-40S particle is indeed pulled down. These additional data have been added in Figure 6A of the revised version I of the manuscript and the text has been amended accordingly (Page 14, Line 20).

1. Page 16, Lines 10-12: The authors state "RSK facilitates the release of RIOK2 and other AMFs", however the only other AMF in this study was NOB1. Please reword appropriately that most likely facilitates release of RIOK2 and other AMFs in a RIOK2 dependent or independent manner if it also phosphorylates other AMFs which possess the motif.

We agree with Reviewer #2 and we changed the text accordingly (Page 16, Line 11) but we did not introduce the hypothesis that RIOK2 may target directly other AMFs of late pre-40S particles which possess the motif because our in silico screen did not identify consensus RXRXXS/T motifs in any of these factors.

Reviewer #2 (Significance (Required)):

This manuscript is significant due to the lack of mechanistic connection of cellular signaling pathways to pre-rRNA processing. There have been, for the most part, no mechanistic connection of signaling pathways to pre-rRNA processing regulation and none for direct targets of MAPK signaling (Reviewed in Gaviraghi et al 2019). They provide the groundwork for analysis of MAPK signaling in regulation of an assembly factor and inclusion of their motif analysis could provide RSK signaling targets' regulation of specific steps of ribosome biogenesis that remain to be elucidated.

Although the research delves into a specific mechanism, its audience could be far reaching as it is in the ribosome biogenesis field and MAPK signaling, which have broad implications in cancer and developmental diseases.

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

The authors report that inhibition of MAPK signaling via RSK is associated with modest alterations in the relative abundance of human pre-rRNA species, that are most marked for 30S but also visible for 21S - although not clearly shown for 18S-E.

RIOK2 has two closely spaced sites predicted as RSK targets, one of which was confirmed to be MAPK sensitive and shown to be an RSK substrate in vitro. Substitution of Ser483 with Ala was associated with reduced growth and 18S-E accumulation, consistent with impaired NOB1 cleavage activity. RIOK2-S483A also showed greater pre-ribosome association in vivo and consistent with this, more stable association in vitro and increase cytoplasmic residence. These effects are clear, although the data do not directly demonstrate their linkage to loss of RSK phosphorylation.

The mutations were apparently generated directly in the genome of haploid cells, potentially raising concerns that the introduction of a deleterious mutation might have been accompanied by compensatory mutations elsewhere. However, three cells line gave similar results, mitigating this concern.

Specific comments:

1. To help the reader, the authors should directly discuss why they think the data on MAPK inhibition did not reveal a clearer pre-18S cleavage phenotype, as would have been expected for loss of RIOK2 activity.

This comment is similar to major comment #4 of Reviewer #2.

Please refer to the above response.

1. Fig. S3: The degree of RSK depletion with the siRNAs appears very modest, as are the effects on RIOK2-P. Moreover, the double depletion is not clearly better than single depletions. These data should probably be supported by quantitation or withdrawn._

We agree with Reviewer #3 that the effects shown in this figure are modest but we originally chose to show these data because their further supported the role of RSK in RIOK2 phosphorylation at S483 in complement to Figure 3.

We have withdrawn this figure from the present revised version I of the manuscript.

1. Fig. 5D: For 18S-E recovery with RIOK2, is the ratio adjusted for the increase in 18S-E abundance in the mutant - ie is recovery increased when adjusted for the increased pre-rRNA abundance?_

In these experiments, the tagged versions of RIOK2 WT and S483A have been expressed ectopically from plasmids in cells expressing the endogenous wild-type protein. RIOK2 S483A does not behave as a dominant negative mutant in these conditions and does not induce 18S-E accumulation, as shown in the northern blot analysis of the 18S-E levels in the cell lysates (lower panel). This information is indicated in the revised version I of the manuscript (Page 13, Line 26).

Reviewer #3 (Significance (Required)):

Overall, the analyses on the phenotype of RIOK2-S483A, and the demonstration that this site is an RSK target, appear convincing.

Caveats are

1) the phenotype seen on inhibition of RSK, would not have implicated RIOK2 as the obvious candidate for the factor responsible for the observed processing defects;

We agree with this comment, which has also been raised by Reviewer #2 (Major comment 4.). We provide several evidence in the manuscript that RSK phosphorylates RIOK2 on S483 in vivo and in vitro (Figure 3). However, as explained above in response to Reviewer #2, we cannot correlate the in vivo phenotypes resulting from RSK or RIOK2 inactivation for biological reasons. As mentioned in the introduction, RSK regulates multiple substrates at different stages of ribosome biogenesis (Translation of RPs and AMFs, Pol I transcription, pre-ribosome maturation and export), whereas RIOK2 is specifically implicated in the cytoplasmic maturation of pre-40S particles. Inactivation of RSK is therefore expected to induce pleiotropic defects in ribosome biogenesis, and in particular early defects (Reduced Pol I transcription, 30S precursor accumulation) that preclude observation of the expected phenotype linked to RIOK2 inactivation, i.e. 18S-E accumulation.

We nevertheless tried to clarify this point as described in the response to Reviewer #2, major comment 4.

2) the RIOK2-S483A phenotype is not demonstrated to be RSK dependent. This raises the possibility that, although RSK can phosphorylate S483, the effects of the mutation are not due to the loss of this modification.

As mentioned by Reviewer #3, our data show that RSK can phosphorylate RIOK2 S483 in vitro and in vivo (Figure 3). We believe that Figure 4C strongly suggests that the accumulation of the 18S-E in cells expressing RIOK2 S483A mutant is due to the loss of S483 phosphorylation, since mutation of S483 to an aspartic acid (S483D), generally considered as a mutation mimicking a phosphorylated serine, does not affect 18S-E maturation. However, although our manuscript provides many lines of evidence identifying RSK as the kinase responsible for RIOK2 phosphorylation at S483, we cannot formally exclude that other AGC kinases involved in growth and proliferation, such as S6K or Akt, may also be involved redundantly or alternatively. Our data presented in Figure 3A showing that treatment of cells with the RSK inhibitors LJH decrease RIOK2 phosphorylation at S483 support a specific role of RSK.

We developed this point in the discussion section (Page 18, from Line 25).

With these provisos, the work is technically good and will be of considerable interest to the field. The post-transcriptional regulation of ribosome synthesis is increasingly recognized a significant topic.

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Referee #2

Evidence, reproducibility and clarity

There have been mechanistic connections of various signaling pathways to regulation ribosome biogenesis steps including rDNA transcription by RNA polymerase I and III, ribosomal protein transcription, and differential mRNA translation efficiency. However, there is a lacking mechanistic connection of signaling pathways to pre-rRNA processing and maturation steps of ribosome biogenesis. The authors set out to provide a specific example of a direct target of MAPK signaling, RSK that regulates pre-rRNA maturation through the phosphorylation of a ribosome assembly factor (RIOK2), offering for the first time providing mechanistic insight into MAPK regulation of pre-rRNA maturation.

The authors observe slight pre-rRNA processing defects upon the use of RSK inhibitors and RSK depletion. They identified several candidate ribosome assembly and modification factors containing the canonical RSK substrate motif, including the RIOK2 kinase. Phosphorylation at this motif was verified to be specifically phosphorylated by RSK1 and 2 isoforms in cells and in an in-vitro kinase assay. The authors produced RIOK2 knock-in eHAP1 cell lines expressing non-phosphorylatable or phosphomimetic versions of RIOK2, observing slowed cellular proliferation, decreases in global translation, slight pre-rRNA processing abnormalities, but not changes in overall mature 18S rRNA levels. More specifically, the authors defined the inability of RIOK2 to be phosphorylated leads to defects in RIOK2 dissociation from the pre-40S ribosomal subunit in an in-vitro assay, and inability for it to be recycled for reuse in pre-ribosome export from the nucleus to the cytoplasm by immunofluorescence.

Overall, the authors provide an interesting mechanism of MAPK regulation of a ribosome assembly factor RIOK2. However, they fail to provide the necessary reproducibility, controls, quantification, and consistent results between experiments to support their hypotheses.

Major Comments:

1.The northern blots reported throughout the manuscript are lacking proper reproducibility and quantification. First, the northern blots are lacking a loading control, which is necessary to report fold changes that are being measured across treatments. Please include a proper loading control (i.e. 7SL or U6 RNAs). Additionally, more rigorous analysis of the pre-rRNA precursor levels through ratio analysis of multiple precursors (RAMP) (Wang et al 2014) can be completed to provide a clearer depiction on which precursor(s) are accumulating. It is unclear for the Figure 1 northern blots if there were replicates completed and what the error bars represent in Figure 1B. Please report replicates, so that statistical analysis can be completed on the differences in precursor relative abundance. This need is emphasized by the small changes observed in pre-rRNA levels (less than 2 fold) between conditions.

2.The western blots reported throughout the manuscript are lacking proper reproducibility and quantification. For example, the western blots validating RSK1 and RSK2 depletion in Figure 1C lack a proper loading control. Additionally, it is unclear if there are replicates completed and there is lack of statistical analysis to determine if the changes are significant. Please include loading controls, replicates, and quantification of the western blots throughout the manuscript.

3.Please report the full bioinformatic analysis of the RSK substrate motif search among human AMFs including other AMFs found in this search. A sorted list format would be valuable for the reader to understand other potential RSK substrates involved in ribosome biogenesis.

4.The authors report that RSK inhibition/depletion leads to accumulation of the 30S pre-rRNA, yet mutation of its target site on RIOK2 or RIOK2 depletion leads to an accumulation of the 18S-E pre-rRNA. Additionally, the phosphomimic mutation of RIOK2 leads to an accumulation of 30S, the opposite of the expected result. Please elaborate on this discrepancy in processing defects observed across experiments. Are there similar results for RSK depletion/inhibition and RIOK2 release from the pre-40S and inability to import into the nucleus? If so, this could provide phenotypic consistency between these two proteins in the proposed pathway to further support the hypothesis.

5.Mature levels of 18S rRNA are not altered in the RIOK2 mutant cell lines. This could be due to compensation in these mutant cell lines since RIOK2 is essential. Please report the mature 18S rRNA levels upon shRNA depletion and RSK inhibitors to provide insight into if this pathway significantly alters mature 18S rRNAs as a mechanism for the altered translation and proliferation observed.

Minor Comments:

1.Figure 1A lower: The authors use an RSK inhibitor LJH685, that does not inhibit RSK phosphorylation S380. Therefore, another verification of RSK inhibition must be used besides RSK-pS380 abundance as for PD184352 inhibition. Please validate the usage of this RSK inhibitor in the experiments by inclusion of quantification of a direct downstream substrate of RSK, such as YB1-pS102 quantification.

2.Page 7, Lines 8-12: The authors state that RSK knockdown led to increases in the 45S, while the LJH685 treatment led to no changes in 45S levels due to differences in growth conditions. Please elaborate more on how growth conditions would alter 45S pre-rRNA levels. It would be expected that stimulation of the MAPK pathway would increase pre-rRNA transcription compared to steady state growth conditions. However, pre-rRNA processing northern blots are only measuring steady state levels of the precursors. Thus, an rDNA transcription assay would need to be completed to evaluate these differences.

3.Figure 2C: Please quantify these results to properly evaluate the role of these two phosphorylation sites in MAPK signaling.

4.Please include the RIOK2 pS483 antibody generation methodology used in this study.

5.In vitro kinase assay methods: Is the recombinant RSK1 the human version of the protein? Please clarify in methods.

6.Figure 4B: Please include statistical analysis of the puromycin incorporation assay.

7.Page 13, Line 18: Please explain why RIOK2 co-IP with NOB1 is important.

8.In vitro dissociation assay: There is no control for pulldown of entire pre-40S particles and not just NOB1 protein. Thus, it is unclear if RIOK2 is dissociating from NOB1 or entire pre-40S particles. Please reference previous literature of the methodology of this experiment if applicable. Additionally, please include controls, such as western blotting of ribosomal proteins or northern blotting of rRNA in the pulldown fraction used.

9.Page 16, Lines 10-12: The authors state "RSK facilitates the release of RIOK2 and other AMFs", however the only other AMF in this study was NOB1. Please reword appropriately that most likely facilitates release of RIOK2 and other AMFs in a RIOK2 dependent or independent manner if it also phosphorylates other AMFs which possess the motif.

Significance:

This manuscript is significant due to the lack of mechanistic connection of cellular signaling pathways to pre-rRNA processing. There have been, for the most part, no mechanistic connection of signaling pathways to pre-rRNA processing regulation and none for direct targets of MAPK signaling (Reviewed in Gaviraghi et al 2019). They provide the groundwork for analysis of MAPK signaling in regulation of an assembly factor and inclusion of their motif analysis could provide RSK signaling targets' regulation of specific steps of ribosome biogenesis that remain to be elucidated.

Although the research delves into a specific mechanism, its audience could be far reaching as it is in the ribosome biogenesis field and MAPK signaling, which have broad implications in cancer and developmental diseases.

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Referee #3

Evidence, reproducibility and clarity

The authors report that inhibition of MAPK signaling via RSK is associated with modest alterations in the relative abundance of human pre-rRNA species, that are most marked for 30S but also visible for 21S - although not clearly shown for 18S-E.

RIOK2 has two closely spaced sites predicted as RSK targets, one of which was confirmed to be MAPK sensitive and shown to be an RSK substrate in vitro. Substitution of Ser483 with Ala was associated with reduced growth and 18S-E accumulation, consistent with impaired NOB1 cleavage activity. RIOK2-S483A also showed greater pre-ribosome association in vivo and consistent with this, more stable association in vitro and increase cytoplasmic residence. These effects are clear, although the data do not directly demonstrate their linkage to loss of RSK phosphorylation.

The mutations were apparently generated directly in the genome of haploid cells, potentially raising concerns that the introduction of a deleterious mutation might have been accompanied by compensatory mutations elsewhere. However, three cells line gave similar results, mitigating this concern.

Specific comments:

1.To help the reader, the authors should directly discuss why they think the data on MAPK inhibition did not reveal a clearer pre-18S cleavage phenotype, as would have been expected for loss of RIOK2 activity.

2.Fig. S3: The degree of RSK depletion with the siRNAs appears very modest, as are the effects on RIOK2-P. Moreover, the double depletion is not clearly better than single depletions. These data should probably be supported by quantitation or withdrawn.

3.Fig. 5D: For 18S-E recovery with RIOK2, is the ratio adjusted for the increase in 18S-E abundance in the mutant - ie is recovery increased when adjusted for the increased pre-rRNA abundance?

Significance

Overall, the analyses on the phenotype of RIOK2-S483A, and the demonstration that this site is an RSK target, appear convincing.

Caveats are

1)the phenotype seen on inhibition of RSK, would not have implicated RIOK2 as the obvious candidate for the factor responsible for the observed processing defects;

2)the RIOK2-S483A phenotype is not demonstrated to be RSK dependent. This raises the possibility that, although RSK can phosphorylate S483, the effects of the mutation are not due to the loss of this modification.

With these provisos, the work is technically good and will be of considerable interest to the field. The post-transcriptional regulation of ribosome synthesis is increasingly recognized a significant topic.

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Referee #1

Evidence, reproducibility and clarity

The manuscript addresses an important topic, the posttranscriptional maturation of ribosomes. This topic is inherently interesting because we normally think of ribosome biogenesis as a sequential series of steps that automatically proceeds and cannot be "accelerated" in physiological conditions, but only "delayed" in the presence of genetic mutations. In short, the manuscript proposes that RIOK2 phosphorylation by the action of RSK, below the Ras/MAPK pathway promotes the synthesis of the human small ribosomal subunit.

I honestly admit that I have some difficulties in reviewing this manuscript. The quality of the presented data is, in generally, good. However, overall I find the whole manuscript preliminary and I am not much convinced of the conclusions. Several aspects are superficially analyzed. In short, I think that most of the conclusions are not fully supported by the data because shortcuts are present. A list of all the aspects that I found wrong are listed.

Biological issue

1. The authors claim that the effects of the inhibition of the maturation of ribosomes by acting on a pathway upstream of RIOk2 are limited to the 40S subunit. This is far from being a trivial point, for the following reason. RIOK2 is known to affect the maturation of 40S ribosomes. Hence, the fact that using an upstream inhibitor of the MAPK pathway such as PD does not inhibit 60S processing in reality would argue against a biologically relevant control in ribosome maturation (of the MAPK patheay). Have the authors considered this? In a way, also, given the fact that the mutants confirm a role in 18S final maturation, it is a bit complex to put all the data in a clear biological context.

A number of specific issues will be concisely described.

Manuscript very well written. Data do not always support the strong conclusions. Low magnitude of the observed effects.

In introduction the authors make a general claim that ribosome biogenesis is one of the most energetically demanding cellular activities. This statement lingers in the literature since 15 years but in reality it has never been formally proved for mammalian cells, and certainly not for HEK293 cells. The original statement, to my knowledge, can be traced by some obscure statement referred to the yeast case and then repeated as a truth. In conclusion, beside being a very banal observation, it should be referenced.

Growth factors, energy status are not cues but are proteins or metabolites (introduction). Authors write about mTOR without making statements on mTORC1/2. This is very obsolete. Also I am not sure that the choice of Geyer et al., 1982, and subsequent papers makes much sense. At the very minimum TOP mRNA concepts and mTORC1 must be defined.

The authors claim that heir work fills a major gap between known functions of MAPK and cytoplasmic translation. I would not be so sure about it.

Results. Authors start with a major mistake, i.e. that PMA selectively stimulates the MAPK pathway. Perhaps it stimulates, certainly it does not do it selectively.

RIOK2 phosphosites are first found by bioinformatics analysis. It should be noted that the predicted phosphosite (S483) is found only in a limited set of datasets from MS databases. The actual importance of this site would not emerge from unbiased studies. Also, there are many other phosphosites that were not analyzed in this study.

Throughout the paper the authors use the word strongly, significantly, but the actual effects seem in general quite marginal.

Discussion. The authors claim that they provide solid evidence on MAPK signalling to ribosome maturation. At the very best this is circumstantial evidence for the 40S maturation.

Figure 1. Unclear why LJH should increase P-ERK. General lack of quantitation (sd, replicates, bars). Experiment done only on a single cell line in a single experimental setup. Very different effects on 21S by LJH,PMA and siRNA for RIOK2. Overall the message given by the authors is to me mysterious.

Figure 2. Several red flags. For instance in 2C the loaded levels of RIOK2-HA loaded are clearly less than the ones of the other genotypes, hence the conclusion on P-RIOK2 is not convincing. Staining with anti-P RIOK2 lacks controls, how can be sure that the signal is due to the phosphate? Phosphatase treatment? Why FBS does not lead to ERK staining in HEK293? There are plenty of growth factors in FBS that should lead to ERK phosphorylation. I do not understand this experiment.

Figure 3. In vitro phosphorylation, if I understood, it relies on a truncated version of RIOK2. Why? Is the folding of the full length protein not permissive to in vitro phosphorylation? HA-RSK3 is less?

Figure 4. Immunofluorescence is low mag, difficult to understand. I really like the experiments with RIOK2 mutants, however I wonder what about protein levels after the knock-in? Given the 18S phenotype overlap between the phenotype of the RIOK2 loss of function with the S483A, testing protein level becomes of the utmost importance.

Figure 5. Low quality IFL. Hard to think that histogram quantitation of nuclear versus cytoplasmic staining are reliable in the absence of fractionation, better quantitation, experiment done in other cell lines and so on. However, very beautiful Fig. 5E perhaps the best of the paper shows also mobility shift driven by S483, thus supporting posttranslational modifications.

Fig. 6. IFL studies are really impossible to interpret. The effects on RIOK2 release (this figure) and 18S maturation (Fig. 5) are very clear and of great quality. Overall conclusions. The manuscript tends to overinflate the meaning of several experiments. What to me is very clear and interesting is that the the authors provide clear evidence that S483A mutants have a defect in 40S maturation. Whether this is due to MAPK signalling, is only circumstantial. I would suggest to build up on the strong findings and eliminate ambiguous data.

Significance

The paper deals with an important topic, namely whether a regulation of ribosome maturation exists, and how it is mechanistically regulated. In this context, the analysis of the ERK pathway is highly needed considered that most works deal with effects of the PI3K-mTOR pathway, and the parallel, yet important RAS-ERK pathway, is less understood. As a final note, we should consider that S6K downstream of mTOR, and ribosomal S6K, downstream of ERK have been considered to share some substrates.

The manuscript is interesting, but several statements given by the authors are rather superficial. An example, listed in the previous section, relates to the linguistic usage of mTOR kinase, instead of detailing whether we are dealing with mTORc1 or mTORc2. A second gross mistake is the definition of PMA as a stimulator of the ERK pathway. If this is certainly true, this is historically not correct as seminal papers by the group of Parker define this drug as a stimulator of conventional PKC kinases. In short, this paper is a step back in knowledge from the perspective of the literature context.

All people interested to the crosstalk between ribosome maturation and signaling pathways will be certainly read this manuscript.

My expertise is within the ribosome biology and signalling field.

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Reply to the reviewers

Please note that the authors have provided a formatted PDF version of this rebuttal, including additional figures and references, via the Open Science Framework: https://osf.io/5acqp/

Reviewer #1

This is an interesting and thorough study characterising human iPSC with hetero or homozygous mutation in pi3k pathway that lead to its hyper-activation. They prove that the increased stemness results from enhanced autocrine responsiveness to TGF signalling pathway. The main conclusions are well supported by the presented data. Cutting edge tools and bioinformatic analysis are adequately applied. I have only one important point:

1) Western blot based validation of TGF pathway activation in wt and mutant iPSCs will be helpful to strengthen the results based on bioinformatic data.

AUTHORS’ RESPONSE__:__ We thank the Reviewer for the positive evaluation of our work.

Functional validation of the signalling hypothesis is indeed important, and we did in fact already present supportive data. Current evidence suggests that SMAD2 is the main transcription factor mediating actions of the TGFb/NODAL pathway in an early developmental context [1,2], and we have shown increased phosphorylation of SMAD2 (S465/S467) in PIK3CAH1047R/H1047R iPSCs using RPPA in the two datasets shown in Fig.2.

We have attempted to demonstrate increased NODAL protein directly in PIK3CAH1047R/H1047R cells, but have been unsuccessful due to poor signal on immunoblotting. We thus opted for functional testing of our hypothesis using the experiment presented in Fig. 5, wherein TGFb (a surrogate for NODAL) is removed from the culture medium. Human iPSCs depend strictly on TGFb/NODAL for maintenance of NANOG expression and thus pluripotency [3,4]. Upon exclusion of TGFb/NODAL from the culture medium of normal human iPSCs, the early responses (prior to overt differentiation) are expected to be: (A) decreased NODAL expression, due to well-established autoregulation [2], then (B) a decrease in NANOG and ultimately POU5F1 (OCT3/4) mRNA levels (see also Introduction, lines 80-90). The evidence in Fig. 5 that PIK3CAH1047R/H1047R fail to exhibit these responses upon exogenous TGFb/NODAL removal supports the notion that these cells autonomously sustain TGFb/NODAL signalling.

For improved clarity, we have also added the following information to the revised manuscript:

lines 202-205: “This is consistent with strong NODAL mRNA upregulation and increased pSMAD2 (S465/S467) in PIK3CAH1047R/H1047R iPSCs in the current study (Dataset S2 and RPPA data in Fig. 2, respectively), and with prior evidence of activation of the NODAL/TGFb pathway in homozygous PIK3CAH1047R iPSCs.”

Reviewer #2

In this manuscript, Madsen et al have investigated the role of heterozygous versus homozygous PIK3CAH1047R gain-of-function mutation at maintaining stemness of induced pluripotent stem cells (iPSCs). The authors have performed high-depth RNAseq, proteomic, and RPPA analyses to show that biallelic PIK3CA alterations induce stronger activation of the PI3K signaling axis, compared to monoallelic mutations. The authors claim that a higher PI3K signaling dose activates the NODAL/TGF-b pathway, which in turn supports stemness in an autocrine fashion. These are important findings, however, the manuscript and its conclusions can be improved.

AUTHORS’ RESPONSE__:__ We thank the Reviewer for acknowledging the importance of the work and for their constructive suggestions for improvements.

The authors have described the role of PIK3CAH-1047R gain-of-function mutation in cancer and overgrowth syndromes. However, cancer associated somatic mutations in PIK3CA are mostly heterozygous. Similarly, PIK3CA related overgrowth syndromes (PROS) are caused by post-zygotic mosaic PIK3CA activating mutation. As such, the relevance of homozygous PIK3CA alterations to these pathological conditions is unclear. The authors should elaborate on the biological implications of their findings.

AUTHORS’ RESPONSE__:__ We disagree with the Reviewer’s comment which implies that homozygous PIK3CA mutations are not relevant to many cancers. In our previous work [5], we provided evidence that many human cancers harbour multiple PIK3CA mutant alleles. Specifically, among cancers with a unique PIK3CA mutation, approximately 50% exhibit multiple copies according to allele copy number analysis. We further demonstrated that a substantial proportion of cancers have multiple different PIK3CA variants or additional oncogenic ‘hits’ within the pathway. These findings have been supported by other recent high-profile papers [6–8]. Such multiple alterations increase activity of the PI3K pathway beyond the level seen with heterozygosity alone [5,6]. This substantial body of literature renders our PIK3CAH1047R iPSC model system highly relevant for studying disease-relevant, dose-dependent oncogenic PIK3CA activation.

The Reviewer is correct, however, that PROS is caused by postzygotic heterozygous PIK3CA mutations almost exclusively. Observations in homozygous cells are therefore not directly relevant to the pathogenesis of PROS. On the other hand, the heterozygous cells are closely relevant, being human, carefully matched with isogenic controls, and unperturbed by further manipulations such as artificial immortalisation. Our prior studies demonstrated no clear phenotypes in heterozygous cells in the iPSC differentiation paradigm, despite the rock solid causal nature of heterozygous mutations in PROS. This negative finding, surprising given the dramatic PROS phenotypes, is very important in understanding how best to create disease-relevant PROS models. One intent of the current study was to increase the sensitivity of our transcriptomic analysis, and to combine this with proteomic studies to determine if heterozygous cells really do not exhibit a phenotype. We now show that there are indeed faint echoes in heterozygous cells of the dramatic changes in homozygous cells. We believe that the human growth phenotype is a summative consequence of such small differences in growth behaviours sustained over months and years, highlighting how subtle difference in signalling can lead to dramatic human growth consequences across the lifecourse. Similar observations were also recently made following systematic analyses of oncogenic RAS mutations [9]. The new information we present about heterozygous PIK3CAH1047R cells, while much less “showy” than the cancer-relevant behavious of homozygous cells, we thus contend is very important for understanding of the PROS phenotype and its experimental modelling. To emphasise this point, we have added the following statements to the abstract and discussion, respectively.

• lines 56-57: “This work illustrates the importance of allele dosage and expression when artificial systems are used to model human genetic disease caused by activating PIK3CA mutations.”
• lines 104-106: “We discuss the implications of our findings for understanding and modelling developmental disorders and cancers driven by genetic PI3K activation.”
• lines 333-340: “Finally, our observations are important for future studies seeking to model human PIK3CA-related diseases. The modest changes observed in heterozygous PIK3CAH1047R cells, in sharp contrast to the radical transcriptional alterations in homozygous cells, emphasise the importance of careful allele dose titration when artificial overexpression systems are used to model disorders caused by genetic PIK3CA activation. Our findings in heterozygous cells are also a reminder that very small effect sizes in cellular systems may summate and result in major human phenotypes over a life course. That such minor changes are found in a cellular study of a rare and severe disorder emphasises the challenges of modelling much more subtle disease susceptibility conferred by GWAS-detected genetic associations, where cellular effect sizes are likely to be smaller still.”

  The role of biallelic PIK3CA mutation is reminiscent of compound mutations in PIK3CA which have also been shown to increase PI3K signaling output. However, double PIK3CA mutations confer enhanced sensitivity to PI3K inhibition (Toska et al. Science 2019). Could the authors kindly speculate on this discrepancy.

AUTHORS’ RESPONSE: We emphasise first that PIK3CAH1047R/H1047R cells do respond to BYL719 at the signalling level, as demonstrated previously [5] and in the manuscript (revised Figure S5; see also additional Western blot below). Our point is that the cells have undergone a switch to self-sustained stemness. That is, while PIK3CA activation was the driver of the initial change in cell state, the induced stemness phenotype is no longer reversed by removal of that trigger, with our data suggesting that this is now driven by self-sustained TGFb/NODAL signalling. This is in line with the role of this pathway in the maintenance of the pluripotent state. We speculate that this may be important in a cancer context where surviving stem cells may permit cancer persistence after toxic therapies, even if short term growth of tumours is reduced by agents such as PI3K inhibitors.

Our data are not directly comparable to prior cellular data, for example in Vasan et al. [6], due to: (a) use of different cell model system and (b) assessment of different functional responses. We would also sound some methodological notes of caution re some of the prior studies alluded to, as potentially confounding differences in growth rate in the cells studied was not corrected for. It is well-established that IC50 and Emax values depend on cell division rates, and failure to correct for this can result in artefactual correlations between genotype and drug sensitivity (see, e.g., Hafner et al. Nature Methods 2016: “Growth rate inhibition metrics correct for confounders in measuring sensitivity to cancer drugs” [10]**).

Similarly, the p110 alpha specific inhibitor, alpelisib, is highly effective against PIK3CA-mutant ER+ breast cancer and PROS. As such, the clinical relevance of the insensitivity of homozygous PIK3CA mutation to PI3K inhibitors is unclear.

AUTHORS’ RESPONSE__:__ Efficacy of Alpelisib in PROS is currently supported only by unregistered observational studies, but is nevertheless striking. It is not relevant to our findings in homozygous cells, as the Reviewer has previously observed, however.

As for cancer, in a randomised phase 3 trial that compared Alpelisib/BYL719 with fulvestrant to fulvestrant alone, the overall response (irrespective of PIK3CA mutant status) was indeed greater with the combination treatment (26.6 % vs 12.8 %), with a hazard ratio of 0.65 (95% CI, 0.5 to 0.85) in patients with PIK3CA-mutant caners versus a hazard ratio of 0.85 (95% CI, 0.58 to 1.25) in those without a PIK3CA mutation [11]. This trial demonstrated the utility of additional PIK3CA mutant-centric stratification, but a substantial proportion of patients with PIK3CA-mutant tumours (>50%) did not benefit from the BYL719 and fulvestrant combination [11]. However, these observations are not directly relevant to this manuscript and are instead included in a separate manuscript focused on PI3K signalling and stemness in human breast cancers (preprint [12]**).

Figure 2: The authors have performed RPPA analysis in the presence of 100 nM BYL719. Alpelisib is commonly used at 1 uM concentration for in-vitro experiments, and has a cMax of ~5 uM. We suggest the authors perform western blot analysis to confirm the results of RPPA.

AUTHORS’ RESPONSE__:__ We carefully chose the optimal concentration of BYL719 to preserve inhibitor selectivity, and to avoid undue toxicity and confounding off-target effects, rather than copying the dose “commonly used”. The Cmax is not relevant to our use of BYL719 in the current study as a precise tool compound. We refer the Reviewer to the known pharmacological characteristics of this compound [13,14]. According to available evidence, it is only a selective PI3Kα inhibitor at concentrations 250 nM (Table below adapted from Ref. **[13]; for formatted version, please see PDF version: https://osf.io/ecmhr/)

Enzyme

In vitro IC50 for NVP-BYL719 (nM)

PI3Kα

4.6 +/- 0.4

PI3Kα-H1047R

4.8 +/- 0.4

PI3K**b

1156 +/- 77

PI3K**d

290 +/- 180

PI3K**g

250 +/- 140

PI4K**b

571 +/- 42

We have previously demonstrated (Fig. 2C in Ref. [5]) that 100 nM BYL719 is sufficient to restore pAKT (S473) levels in both heterozygous and homozygous PIK3CAH1047R to levels observed in WT cells. This is consistent with the RPPA data reported in the current work (Fig. 2B). Of note, while 500 nM BYL719 completely ablates pAKT irrespective of genotype, we previously noted substantial toxicity [5], precluding use of this or higher doses of BYL719 in our model system. This is in line with a recent Nature Cell Biology study by Yilmaz et al. ([15]) which demonstrated the essential growth-promoting role of the PI3K pathway in human pluripotent stem cells; Yilmaz et al. also demonstrate that compared to somatic cells (fibroblasts), human pluripotent stem cells suffer dramatic effects on growth/survival in response to Torin1/rapamycin [15], overall suggesting that this cell type is exquisitely sensitive to inhibition of the PI3K/AKT/mTOR pathway.

In the present study we have also confirmed that 250 nM BYL719, used for Fig. 5 experiments, has worked as expected at the level of pAKT (S473) as shown in the below Western blot (see also revised Fig. S5; please access PDF version to view Western blot: https://osf.io/ecmhr/)

Figures 3 and 4: The authors should expand their RNAseq analysis to demonstrate enrichment of stemness and TGFb signaling in homozygous mutant cells compared to heterozygous cells.

AUTHORS’ RESPONSE__:__ We thank the Reviewer for this suggestion. The unsupervised MDS plot (Fig. 1A) clearly demonstrates the overlap between wild-type and heterozygous cells, strongly suggesting functional concordance and consistent differences to homozygous counterparts. Indeed, the below count table illustrates that the majority of differentially expressed genes in homozygous versus wild-type cells are also differentially expressed in homozygous versus heterozygous cells, including the direction of the change (please access the PDF version for formatted table: https://osf.io/ecmhr/)

Comparison

Differentially expressed gene count

HOMvsWT

5644

HOMvsHET

5764

HOMvsWT AND HOMvsHET

4825 (2300 upregulated; 2525 downregulated; 1 discordant)

We have now performed additional fast gene set enrichment analyses (fgsea; shown below - please access PDF version to view figure: https://osf.io/ecmhr/) using the R package fgsea ([16]) and 14 of the Broad Institute’s 50 Hallmark Gene Set Collection [17], including manual addition of the PLURINET signature [18]. The 14 gene sets were chosen based on their relevance to answering the Reviewer’s question as well as their connection to PI3K signalling. Fold changes for all expressed genes were included in the analyses, without further thresholding in order to minimise bias.

The results for homozygous vs wild-type comparisons are concordant with our upstream regulator analyses using IPA; as expected, TGFb signalling and PI3K signalling are among the top positively enriched (NES > 1) in comparison between homozygous and heterozygous cells. Unsurprisingly, however, the strength of the enrichments are lower when comparing the two PIK3CAH1047R genotypes.

We are not convinced that including these surplus data will add value to the manuscript and its main message, however we will leave this decision to the discretion of the Editor (please also refer to our response to the subsequent question from Reviewer 2). Moreover, these data will remain visible in the publicly available rebuttal document.

The authors should confirm the results of pathway analysis in vitro to show that homozygous PIK3CA mutation confers increased stemness compared to heterozygous mutation.

AUTHORS’ RESPONSE__:__ This was a key finding in our previous publication [5]. The aim of the current study was to interrogate this phenomenon further through high-depth transcriptomic/signalling analyses.

Figure 5: Kindly provide direct evidence demonstrating that increased PIK3CA signaling output induces NODAL expression in this experimental setting.

AUTHORS’ RESPONSE__:__ We have consistently demonstrated increased NODAL mRNA expression (RNAseq data, Fig. S4 and Ref. [5]). Unfortunately, we have been unsuccessful in attempts to obtain good quality immunoblots for NODAL protein in PIK3CAH1047R/H1047R cells (as noted in response to Reviewer 1). We note, in fact, that such documentation of NODAL protein levels, while not unprecedented, is fairly rare.

Also, please normalize gene expression data to WT cells so it is easy to visualize the changes in NODAL and NANOG expression in homozygous and heterozygous mutants compared to WT iPSCs.

AUTHORS’ RESPONSE__:__ It is arithmetically more precise to normalise to the highest expression (i.e. that of PIK3CAH1047R/H1047R cells) – thereby avoiding artificial inflation of fold-changes when normalising to very low levels of expression. Ultimately, the relative levels calculated – and the increased expression of NODAL in PIK3CAH1047R/H1047R cells – are identical visually. Only the entirely arbitrary units change. Thus we do not deem normalisation to WT to be necessary or to add value to the analysis.

Kindly quantify Fig. S5.

AUTHORS’ RESPONSE__:__ These brightfield micrographs were taken as part of routine practice to monitor cell health during maintenance and experimentation, and are suboptimal for direct quantitation due to uneven illumination background and lack of whole-well imaging. Nevertheless, we have now undertaken quantification as the Reviewer suggests, using individual images taken during independent experimental replicates. The results have been added to Fig. S5 and support our assertion that 250 nM BYL719 had a growth inhibitory effect in homozygous PIK3CAH1047R iPSCs. All raw images and associated data have been uploaded to the Open Science Framework (https://osf.io/hbf7x/). The following short method section detailing the image analysis algorithm has also been included in the revised supplementary material:

“Colony size quantitation from light micrographs

Routine cell culture light micrographs were acquired on an EVOS FL digital inverted microscope (AMF4300, Thermo Fisher Scientific) using the 4X or 10X objective (final magnification 40X and 100X, respectively). For quantitation, 4X images were used for colony segmentation with Definiens Developer XD software. Background was detected using a contrast threshold; for this each pixel was compared to those in the surrounding 24 pixels (i.e. a 5x5 pixel box), and pixels with low contrast (between -50 and +50) were classified as background. Remaining pixels were classified as colonies, and any holes (pixels that were not initially classified as being part of the colony due to low contrast) were filled. Edges of the resulting colonies were smoothened by shrinking and then growing the colonies by 2 pixels. Finally, colonies less than 2000 pixels in size were reclassified as background. The area of the resulting colonies could then be measured and averaged over each field of view.”

Reviewer #3

In this manuscript by Madsen et al., a comparison of the transcriptome and proteome in heterozygous and homozygous PIK3CAH1047R human pluripotent stem cells mutants is presented. The authors demonstrate marked alterations in expression at both the protein and RNA level of homozygous mutants compared to wildtype, while heterozygous lines exhibit only minor changes. Multiple analytical approaches are employed to investigate network alterations, leading the authors to suggest a TGFβ-mediated rewiring of key pluripotent genes to induce a state of sustained stemness. Madsen et al. conclude with a set of experiments to functionally implicate NODAL/TGFβ autocrine signalling in PIK3CAH1047R dose-dependent stemness. The key conclusions are not convincing. While the unbiased omics approach sets up this study well, the study suffers from a lack of convincing functional assays (cell biological assays) to test their model and tease apart a phenotype for the het cells. More robust functional experiments are required to support the finding the NODAL/TGFβ signalling mediates the self-sustained stemness, particularly because this is the major novel finding distinguished from the authors previous work.

AUTHORS’ RESPONSE__:__ We thank the Reviewer for their detailed critique. Our perspective on the robustness and novelty of our findings diverges from that of the Reviewer, however, as we elaborate on in more detail below.

While the authors present a comprehensive omics investigation into alterations between wild type, homozygous, and heterozygous mutants, the critical functional experiments are lacking. In Figure 5, the authors seek to support the role of TGFβ in mediated stemness in the homozygous mutants, however, are not able to directly deplete TGFβ due to technical limitations of the culture conditions. Consequentially, the experiments are primarily built on the use of NODAL withdrawal and stimulation. The data presented thus implicate NODAL in the stemness phenotype, but it's not obvious TGFβ is substantially involved, particularly considering the inhibitor subsequently employed also inhibits NODAL type 1 receptors.

AUTHORS’ RESPONSE__:__ NODAL and TGFb activate shared signalling pathways downstream from their respective receptors, and indeed they (as well as Activin) can be used interchangeably in stem cell culture, which is common practice [19–21]. Commercially available Essential 8/TeSR-E8 is supplemented with TGFb not NODAL; therefore the factor we have removed is TGFb, prior to any controlled introduction of NODAL (based on strong upregulation of its mRNA in PIK3CAH1047R/H1047R). Any residual TGFb-like ligands will be contributed by Matrigel as outlined in the text (lines 247-251). It is well-established that “NODAL/TGFb signalling” denotes signalling through SMAD2/3/4 (as opposed to BMP signalling through SMAD1/5/8), and this is how we use the term throughout the manuscript. Accordingly, it is functional activation of the “NODAL/TGFb signalling pathway” that we investigate (see also response to Reviewer 1, p.1).

In summary, we seek not to make a distinct point about TGFb, but rather refer to NODAL/TGFb signalling as a matter of biochemical correctness. For clarity, we now replace mentions of “TGFb signalling” with “NODAL/TGFb signalling” throughout the revised manuscript. We have also revised the legend for Figure 3 to make this clearer.

Furthermore, there is a paucity of readouts for stemness. For example, a more convincing narrative would include additional expression markers of the core pluripotency network (e.g. OCT4, SOX2, etc.) as well as functional readouts (e.g. NODAL withdrawal and assessment of differentiation) after NODAL stimulation/depletion and comparing across genotypes. Overall, the primary conclusions of this work are not well-evidence by the presented data and the authors should consider additional functional experiments or reframing the narrative.

AUTHORS’ RESPONSE__:__ We chose the current strategy because we wanted to capture the earliest changes after depletion of NODAL/TGFb/ signalling, prior to any signalling rewiring triggered by differentiation. In fact, we believe that a strength of this study is our observation of differences in critical stemness markers in spite of the short time course. To aid non-expert readers we offered a primer on stemness genes and rationale for the markers chosen in the existing introduction (lines 80-90).

We have further assessed additional stemness and differentiation marker genes in two independent homozygous PIK3CAH1047R cell lines using a high-throughput pluripotent stem cell scorecard (Fig. S4). This replicates the effect on cell marker genes documented by RT-qPCR in Fig.5, while also showing additional reductions in genes that were upregulated in homozygous PIK3CAH1047R cells (MYC, GDF3, FGF4) and which have previously been shown to be highly expressed in pluripotent stem cells (we have now added this additional clarification to the legend of Fig. S4) [22]. Despite the short term treatment, these data also show that no other treatment but SB431542 is capable of triggering expression of early neuroectoderm markers (CDH9, MAP2 and PAPLN) [23], prior to overt morphological changes in the cultures (Fig. S5; higher resolution images are also available via The Open Science Framework: https://osf.io/hbf7x/). Neuroectodermal gene expression is expected upon inhibition of TGFb signalling in human pluripotent stem cells [24,25].

A key conclusion of this study is there is a dose-dependent stemness phenotype. As this is not explicitly defined, to this reader, it would imply a graded response between wild type, heterozygotes, and homozygotes in the phenotypic and molecular characteristics. However, as is noted particularly in the omics components of the manuscript, there is in fact "near-binary" alteration in the assayed characteristics. Again, this should be qualified more explicitly, but it is more consistent with the data, which suggests the heterozygotes behave very similarly to the wild types, while homozygotes have substantial alterations. I would suggest the authors consider renaming their descriptions, removing "near-binary" and "dose-dependent" to something like "dose-threshold." This suggests after X threshold of oncogenic PI3K signalling, substantial alterations occur; under this threshold (e.g. hets), changes are marginal. In the event however that there may be a more "dose-dependent" effect, I would expect the transcriptomic and proteomic changes observed in the heterozygous cell lines should be seen in the homozygous cell lines (of which they are likely in greater in magnitude in addition to other changes).

AUTHORS’ RESPONSE__:__ This appears to us to be largely a matter of semantics. In talking of “dose dependency” we were certainly not implying a graded affect (as the Reviewer points out, our are findings are far from this, suggesting a sharp threshold of dose which triggers widespread changes), and indeed nothing in these words strictly suggests this interpretation. Nevertheless we are sensitive to the fact of the Reviewer’s interpretation of the term, and mindful that this might be shared by other readers. On the other hand talking of a “near-binary” effect seems to us to be an accurate description of our findings. We have edited the manuscript to minimise ambiguity with the following changes:

• line 49 “dose” replaced with “strength”: “We demonstrate signalling rewiring as a function of oncogenic PI3K signalling strength, and provide experimental evidence that self-sustained stemness is causally related to enhanced autocrine NODAL/TGFb”
• line 102: “This work provides in-depth characterisation of the near-binary PI3K signalling effects seen in hPSCs ….”
• lines 195, 198, 317: inserted “allele dose-dependent” We would also like to take issue with the case that the Reviewer seems to be making that a more graded change in gene expression across heterozygotes and homozygotes is to be expected. As mentioned in the manuscript (lines 206-210), there is evidence for NODAL/TGFb pathway activation in heterozygous cells. Nevertheless given the known temporal, context- and dose-dependent effects of this pathway [1,2,26,27] and, importantly, the widely described biological properties of developmental systems (featuring positive feedback loops, bistability and hysteresis; see Ref. [28,29]), we have no reason to expect that transcriptomic and proteomic changes observed in homozygous cell lines will be reproduced in heterozygous cell lines.

The manuscript would benefit from more direct comparisons between the heterozygotes and homozygotes.

AUTHORS’ RESPONSE__:__ Please refer to the additional data provided in response to a similar question by Reviewer 2.

Further to the above point, as the marginal phenotype observed in heterozygotes is a critical point in this paper, the authors would benefit from including heterozygote lines in the functional experiments presented in Fig 5. Inclusion of the hets in these experiments would instill confidence in this reader that the marginal molecular alterations characterized at the proteomic and transcriptomic level is reflected in the lack of functional stemness-sustaining behaviour.

AUTHORS’ RESPONSE__:__ The lack of stemness-sustaining behaviour in the heterozygous clones was demonstrated across multiple different experiments in our previous work, and further functional studies of early differentiation in these cells seemed a poor use of resource and very unlikely to give useful insights. Given the major disease phenotype associated with the same genetic change (PROS), the relative lack of phenotype in heterozygous cells was surprising and holds obvious implications for disease modelling (see also response to Reviewer 2, pp.2-3), and for how model systems are “calibrated” against human developmental disease. The aim of the current work was to:

1. • Determine whether increasing the depth of signalling and transcriptomic analyses would unmask small but important changes in heterozygous mutants that might have been missed in prior studies (i.e. we actively aimed to increase the power of the study for identification of subtle changes) and *
2. • To characterise in greater depth the signalling and transcriptional changes underpinning the robust threshold effect observed for self-sustained stemness driven by PIK3CAH1047R/H1047R. We would further observe that PROS does not feature obvious qualititative errors in tissue specification, but rather excessive growth of more or less normally differentiated tissues. We conceptualise this as reflecting a small incremental growth advantage in normally differented tissues of certain lineages that summates to create a major disease phenotype over months and years.*

Thus, without the functional and mechanistic experiments alluded to above, the claims/ conclusions are speculative. In particular, the cancer narrative is irrelevant to the study. Considering both the lack of conclusive differentiation experiments or relevant breast cancer experiments, the discussion on differentiation therapy for breast cancer should be removed.

AUTHORS’ RESPONSE__:__ The reference to cancer links to a computational study of human breast cancers where we specifically looked at the relationship between strength of PI3K signalling and ‘stemness’ [12], both measured using established transcriptional indices. We have included the bioRxiv reference in our revised manuscript (see l.337). While there is an element of speculation in this cancer observation, we do feel it is important and grounded in this and the BioRXiv study, and would prefer to maintain it. However, if editors take a different view it can be removed.

Reproducibility is a concern for this study. The authors should perform more replicates on their experiments (focusing on technical replicates of the lines employed to discern technical vs biological variability). A challenge in reading this manuscript is understanding which replicates were used for which experiments, and whether they are technical or biological (i.e. different lines). While some of the figure legends note this information, it would be helpful to provide clarity throughout the text. In addition, it should be noted that some experiments (e.g. the RPPA analysis in Fig 2B and Fig S3B) show substantial variability between replicates, but because it appears only a single technical replicate from two different cell lines was used, it is impossible to distinguish whether the variability is of a biological or technical nature. The authors would do well to focus on collecting more technical replicates of fewer biological replicates, and then expand to include more biological replicates if initial biological variation is observed.

AUTHORS’ RESPONSE__:__ We strenuously disagree with the Reviewer on this point. Throughout this manuscript, we have been transparent and thorough in reporting how experiments were performed, including the number of both biological and technical replicates. Representative examples include:

Legend to Figure 2A (RPPA dataset in growth-replete conditions): “The data are based on 10 wild-type cultures (3 clones), 5 PIK3CAWT/H1047R cultures (3 clones) and 7 PIK3CAH1047R/H1047R cultures (2 clones) as indicated.”

Legend to Figure 5: “The data are from two independent experiments, with each treatment applied to triplicate cultures of three wild-type and two homozygous iPSC clones.”

Specifically to address the RPPA studies, and as is clear from the Figure 2 legend, we initially performed RPPA analyses in growth factor-replete conditions with extensive technical and biological replication, arguing against the Reviewer’s point. To aid interpretation, we opted for summarising this large dataset in Venn diagrams (following extensive limma-based statistical analysis, including correction for multiple comparisons and sample interdependence as advised in Ref. [30]). If the Reviewer deems it valuable, we could include a heatmap overview as shown below:

[To view figure, please access PDF version of this rebuttal on https://osf.io/ecmhr/]

We took the view that the above representation, while comprehensive, is not particularly informative to the reader. All individual data points for both total and phosphoproteins – with and without normalisation – are plotted as part of separate barplots in the accompanying RNotebook (https://osf.io/d9tca/). These clearly demonstrate that the technical and biological variability in canonical PI3K signalling responses at the level of AKT and immediately downstream of AKT is very low. The same applies to the increased phosphorylation of SMAD2 (S465/S467) in PIK3CAH1047R iPSCs. We include two examples below, and would be happy to include the link to the above RNotebook in the respective Figure legend if the Reviewer deems this helpful.

[To view figure, please access PDF version of this rebuttal on https://osf.io/ecmhr/]

The interpretation of the second RPPA experiment (Fig. 2B) in growth factor-depleted conditions is focused entirely on these responses due to their consistency across both datasets (further supported by low-throughput signalling analyses in the previous PNAS publication).

We had made all raw data and guided analysis scripts for the above RPPA dataset publicly available, and the same is true for all original data as highlighted in the Materials & Methods section. Thus we strongly believe that readers have the opportunity to assess our work and reproduce our analyses/conclusions fully should they wish to do so.

• Finally, we noted in the initial PNAS paper describing these models that we derived and worked with up to 10 independent homozygous PIK3CAH1047R clones, as well as with 3 and 4 independent heterozygous and wild-type clones, respectively. This exceeds the common use of 2 clones (if at all mentioned) in many similar studies in the stem cell literature (e.g. Ref. [31–34]). In our view, derivation of more than two independent clones is crucial for reproducibility in gene editing studies given substantial variability arising from genetic drift [35,36]. We have consistently shown the phenotypic robustness of our mutant clones across the two studies; note, for example, the low technical and biological variability in both heterozygous and homozygous mutants in the transcriptomic data in Fig. 1A. As noted in the manuscript, the high-depth RNAseq data analysis was performed in different clones and independently of the RNAseq reported in Ref. [5], yet yields highly similar results and confirms transcriptional rewiring of PIK3CAH1047R/H1047R iPSCs.*

Throughout the text, the authors frequently reference their previous study in PNAS and often the lines of what is novel in this paper vs. reproduction of previous findings is blurred. The authors would benefit from reducing the frequency of referencing their previous study and focusing on emphasizing the novelty of the present findings.

AUTHORS’ RESPONSE__:__ We have carefully reviewed all instances of citation of our previous study in the manuscript and have reduced their numbers to improve focus on the current findings as suggested. As noted above, however, the current study builds closely upon the findings of the previous work, and referring to these to put the current work in context is important. Indeed, this is reflected in some of the reviewers’ collective comments and questions which are answered by the prior study. We have carefully reviewed the places in which we have cited our previous study and note that except for 2 citations in the Introduction and 3 more in the Discussion, all remaining citations are in the context of linking new and old data, which we believe is important for clarity as suggested by the reviewers. However, if editors take a different view we can minimise this and reduce the number of citations.

Without functional assays to complement and test their models, this manuscript is not a significant advance.

AUTHORS’ RESPONSE__:__ While we take the Reviewer’s point that further studies could have strengthened robustness of the evidence supporting a mediating role of NODAL/TGFb signalling in PI3K-driven stemness, we think this assertion is far too sweeping, and neglects numerous facets of the study of use and interest to several fields (as agreed by the other reviewers). To recapitulate some key points of interest/use of this study:

• Using a carefully derived PIK3CAH1047R iPSC model system and pharmacologically relevant doses of a recently approved PI3Ka-selective inhibitor, we demonstrate that the efficacy of the latter can depend on the strength of PI3K pathway activation and phenotype under investigation – despite expected downregulation of PI3K signalling by Alpelisib, the stemness phenotype is not reversed.
• We link this to self-sustained TGFb signalling in cells with strong PI3K activation by homozygous PIK3CAH1047R The link between the two pathways and the underlying rewiring are likely to be relevant in other contexts, as observed recently in a breast epithelial model system [37]. Given similarity between human pluripotent stem cells and cancer cells, our findings are of wider relevance.
• Aberrant PI3K activation has been associated with numerous pathologies, so it is important for the field to have well-characterised model systems with endogenous expression of one of the most common PIK3CA mutations. Our thorough characterisation of PIK3CAH1047R iPSCs validates one such model.
• To our knowledge, this is the first study to provide a comprehensive and integrated characterisation of isoform-specific PI3K signalling and transcriptomic changes in human pluripotent stem cells. This is important because current knowledge of PI3K signalling in human PSCs is largely based on extrapolation of findings from mouse embryonic stem cells, with many previous studies relying on high concentrations of the non-specific pan-PI3K inhibitor LY294002 (the use of which has been discouraged by the PI3K signalling community [38]).

  I believe the narrative was written for pluripotent stem cell biologists but without robust functional and quantitative cell biological assays to test their models, I don't anticipate stem cell biologists will be very interested.

AUTHORS’ RESPONSE__:__ The Reviewer is incorrect in his/her assertion about the target audience. PI3K signalling plays a key role in numerous disease and physiological processes as well as in development, and is of broad interest to cancer biologists, genetecists, rare disease biologists, biochemists, cell signallers, and endocrinologists among many others. Indeed we started with a primary focus on disease modelling (cancer, PROS) rather than stem cell biology, but because our findings are significant for the role of PI3K in stem cell biology as well as for these diseases, we aimed to make findings accessible across many of these readers. We refer the Reviewer to our previous response with regards to the significance of this work.

**Minor Comments:**

Consider adding gridlines to the MDS plots for clarity of read

AUTHORS’ RESPONSE__:__ This is a matter of taste, and as we honestly can not see how it would enhance appreciation of the very clear clustering, we have decided to leave the plot in its current form.

In Fig S2, some of the in-figure labelling is incorrect

AUTHORS’ RESPONSE__:__ We thank the Reviewer for spotting this. We believe the labelling error to be corrected now and we have further tried to streamline the plot headings, but please do let us know if there is something else which we may have missed.

In Fig S1C, the authors note poor correlation in the heterozygotes between this and a previous study. It would be helpful to qualify this discrepancy, as it is potentially concerning.

AUTHORS’ RESPONSE__: The sensitivity to detect differential gene expression is high for large fold changes (as seen in PIK3CAH1047R/H1047R mutants) in transcriptomic studies, but declines rapidly for fold changes in expression lines 126-131: “The magnitudes of gene expression changes in PIK3CAH1047R/H1047R cells correlated strongly with our previous findings (Spearman’s rho = 0.74, p WT/H1047R iPSCs (Fig. S1C), as expected given the smaller number and lower magnitude of observed gene expression changes in heterozygous cells, and the lower depth of previous transcriptomic studies__.”*

Line 208, the authors state that the small p-value for the homozygotes is suggestive of a dose-dependent effect. This is not the case; it simply suggests a greater probability of the effect being non-random.

AUTHORS’ RESPONSE__:__ The Reviewer is formally correct, and we apologise for the imprecision of our language. Nevertheless biological effect size is pertinent to the p value determined, and so our statement, while requiring an inductive leap from the reader, is not wholly invalid. To tidy this up and improve precision we have reworded as follows:

lines 215-217: “This is in keeping with the much lower effect size in heterozygous cells, and consistent with a critical role for the TGFbeta pathway in mediating the allele dose-dependent effect of PIK3CAH1047R in human iPSCs.”

What does the height in Fig 4B correspond to? It would perhaps be of value to scale nodes based on the significance value.

AUTHORS’ RESPONSE__:__ 4B illustrates hierarchical clustering of the module eigengenes - the height corresponds to similarity of gene expression. We clarify this in the revised manuscript.

References

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23 Tsankov, A. M. et al. (2015) A qPCR ScoreCard quantifies the differentiation potential of human pluripotent stem cells. Nat. Biotechnol. 33, 1–15.

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27 David, C. J. and Massagué, J. (2018) Contextual determinants of TGFβ action in development, immunity and cancer. Nat. Rev. Mol. Cell Biol. 19, 1–17.

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29 Sonnen, K. F. and Aulehla, A. (2014) Dynamic signal encoding-From cells to organisms. Semin. Cell Dev. Biol. 34, 91–98.

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31 Wang, L. et al. (2017) GCN5 Regulates FGF Signaling and Activates Selective MYC Target Genes during Early Embryoid Body Differentiation. Stem Cell Reports 10, 287–299.

32 Zeng, H. et al. (2016) An Isogenic Human ESC Platform for Functional Evaluation of Genome-wide-Association-Study-Identified Diabetes Genes and Drug Discovery. Cell Stem Cell 0, 1660–1669.

33 Ho, L. et al. (2015) ELABELA Is an Endogenous Growth Factor that Sustains hESC Self-Renewal via the PI3K/AKT Pathway. Cell Stem Cell 17, 435–447.

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35 Veres, A. et al. (2014) Low incidence of Off-target mutations in individual CRISPR-Cas9 and TALEN targeted human stem cell clones detected by whole-genome sequencing. Cell Stem Cell 15, 27–30.

36 Ben-David, U. et al. (2018) Genetic and transcriptional evolution alters cancer cell line drug response. Nature 560, 325–330.

37 Katsuno, Y. et al. (2019) Chronic TGF-b exposure drives stabilized EMT, tumor stemness, and cancer drug resistance with vulnerability to bitopic mTOR inhibition. Sci. Signal. 12, eaau8544.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this manuscript by Madsen et al., a comparison of the transcriptome and proteome in heterozygous and homozygous PIK3CAH1047R human pluripotent stem cells mutants is presented. The authors demonstrate marked alterations in expression at both the protein and RNA level of homozygous mutants compared to wildtype, while heterozygous lines exhibit only minor changes. Multiple analytical approaches are employed to investigate network alterations, leading the authors to suggest a TGFβ-mediated rewiring of key pluripotent genes to induce a state of sustained stemness. Madsen et al. conclude with a set of experiments to functionally implicate NODAL/TGFβ autocrine signalling in PIK3CAH1047R dose-dependent stemness.

Major Comments:

1.The key conclusions are not convincing. While the unbiased omics approach sets up this study well, the study suffers from a lack of convincing functional assays (cell biological assays) to test their model and tease apart a phenotype for the het cells. More robust functional experiments are required to support the finding the NODAL/TGFβ signalling mediates the self-sustained stemness, particularly because this is the major novel finding distinguished from the authors previous work. • While the authors present a comprehensive omics investigation into alterations between wild type, homozygous, and heterozygous mutants, the critical functional experiments are lacking. In Figure 5, the authors seek to support the role of TGFβ in mediated stemness in the homozygous mutants, however, are not able to directly deplete TGFβ due to technical limitations of the culture conditions. Consequentially, the experiments are primarily built on the use of NODAL withdrawal and stimulation. The data presented thus implicate NODAL in the stemness phenotype, but it's not obvious TGFβ is substantially involved, particularly considering the inhibitor subsequently employed also inhibits NODAL type 1 receptors. Furthermore, there is a paucity of readouts for stemness. For example, a more convincing narrative would include additional expression markers of the core pluripotency network (e.g. OCT4, SOX2, etc.) as well as functional readouts (e.g. NODAL withdrawal and assessment of differentiation) after NODAL stimulation/depletion and comparing across genotypes. Overall, the primary conclusions of this work are not well-evidence by the presented data and the authors should consider additional functional experiments or reframing the narrative.

• A key conclusion of this study is there is a dose-dependent stemness phenotype. As this is not explicitly defined, to this reader, it would imply a graded response between wild type, heterozygotes, and homozygotes in the phenotypic and molecular characteristics. However, as is noted particularly in the omics components of the manuscript, there is in fact "near-binary" alteration in the assayed characteristics. Again, this should be qualified more explicitly, but it is more consistent with the data, which suggests the heterozygotes behave very similarly to the wild types, while homozygotes have substantial alterations. I would suggest the authors consider renaming their descriptions, removing "near-binary" and "dose-dependent" to something like "dose-threshold." This suggests after X threshold of oncogenic PI3K signalling, substantial alterations occur; under this threshold (e.g. hets), changes are marginal. In the event however that there may be a more "dose-dependent" effect, I would expect the transcriptomic and proteomic changes observed in the heterozygous cell lines should be seen in the homozygous cell lines (of which they are likely in greater in magnitude in addition to other changes). The manuscript would benefit from more direct comparisons between the heterozygotes and homozygotes.

• Further to the above point, as the marginal phenotype observed in heterozygotes is a critical point in this paper, the authors would benefit from including heterozygote lines in the functional experiments presented in Fig 5. Inclusion of the hets in these experiments would instill confidence in this reader that the marginal molecular alterations characterized at the proteomic and transcriptomic level is reflected in the lack of functional stemness-sustaining behaviour.

2.Thus, without the functional and mechanistic experiments alluded to above, the claims/ conclusions are speculative. In particular, the cancer narrative is irrelevant to the study. Considering both the lack of conclusive differentiation experiments or relevant breast cancer experiments, the discussion on differentiation therapy for breast cancer should be removed.

3.Reproducibility is a concern for this study. The authors should perform more replicates on their experiments (focusing on technical replicates of the lines employed to discern technical vs biological variability). A challenge in reading this manuscript is understanding which replicates were used for which experiments, and whether they are technical or biological (i.e. different lines). While some of the figure legends note this information, it would be helpful to provide clarity throughout the text. In addition, it should be noted that some experiments (e.g. the RPPA analysis in Fig 2B and Fig S3B) show substantial variability between replicates, but because it appears only a single technical replicate from two different cell lines was used, it is impossible to distinguish whether the variability is of a biological or technical nature. The authors would do well to focus on collecting more technical replicates of fewer biological replicates, and then expand to include more biological replicates if initial biological variation is observed.

Minor Comments:

• Consider adding gridlines to the MDS plots for clarity of read
• In Fig S2, some of the in-figure labelling is incorrect
• In Fig S1C, the authors note poor correlation in the heterozygotes between this and a previous study. It would be helpful to qualify this discrepancy, as it is potentially concerning.
• Line 208, the authors state that the small p-value for the homozygotes is suggestive of a dose-dependent effect. This is not the case; it simply suggests a greater probability of the effect being non-random.
• What does the height in Fig 4B correspond to? It would perhaps be of value to scale nodes based on the significance value.

Significance

Nature and significance of the advance:

• Throughout the text, the authors frequently reference their previous study in PNAS and often the lines of what is novel in this paper vs. reproduction of previous findings is blurred. The authors would benefit from reducing the frequency of referencing their previous study and focusing on emphasizing the novelty of the present findings.

• Without functional assays to complement and test their models, this manuscript is not a significant advance.

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

• I believe the narrative was written for pluripotent stem cell biologists but without robust functional and quantitative cell biological assays to test their models, I don't anticipate stem cell biologists will be very interested.

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.

• Stem cell biology, cancer biology, systems biology, mTORC1 signalling

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Referee #2

Evidence, reproducibility and clarity

As below.

Significance

In this manuscript, Madsen et al have investigated the role of heterozygous versus homozygous PIK3CAH1047R gain-of-function mutation at maintaining stemness of induced pluripotent stem cells (iPSCs). The authors have performed high-depth RNAseq, proteomic, and RPPA analyses to show that biallelic PIK3CA alterations induce stronger activation of the PI3K signaling axis, compared to monoallelic mutations. The authors claim that a higher PI3K signaling dose activates the NODAL/TGF-b pathway, which in turn supports stemness in an autocrine fashion. These are important findings, however, the manuscript and its conclusions can be improved.

The authors have described the role of PIK3CAH-1047R gain-of-function mutation in cancer and overgrowth syndromes. However, cancer associated somatic mutations in PIK3CA are mostly heterozygous. Similarly, PIK3CA related overgrowth syndromes (PROS) are caused by post-zygotic mosaic PIK3CA activating mutation. As such, the relevance of homozygous PIK3CA alterations to these pathological conditions is unclear. The authors should elaborate on the biological implications of their findings.

The role of biallelic PIK3CA mutation is reminiscent of compound mutations in PIK3CA which have also been shown to increase PI3K signaling output. However, double PIK3CA mutations confer enhanced sensitivity to PI3K inhibition (Toska et al. Science 2019). Could the authors kindly speculate on this discrepancy. Similarly, p110 alpha specific inhibitor, alpelisib, is highly effective against PIK3CA-mutant ER+ breast cancer and PROS. As such, the clinical relevance of the insensitivity of homozygous PIK3CA mutation to PI3K inhibitors is unclear.

Figure 2: The authors have performed RPPA analysis in the presence of 100 nM BYL719. Alpelisib is commonly used at 1 uM concentration for in-vitro experiments, and has a cMax of ~5 uM. We suggest the authors perform western blot analysis to confirm the results of RPPA.

Figures 3 and 4: The authors should expand their RNAseq analysis to demonstrate enrichment of stemness and TGFb signaling in homozygous mutant cells compared to heterozygous cells.

The authors should confirm the results of pathway analysis in-vitro to show that homozygous PIK3CA mutation confers increased stemness compared to heterozygous mutation.

Figure 5: Kindly provide direct evidence demonstrating that increased PIK3CA signaling output induces NODAL expression in this experimental setting. Also, please normalize gene expression data to WT cells so it is easy to visualize the changes in NODAL and NANOG expression in homozygous and heterozygous mutants compared to WT iPSCs

Kindly quantify Fig. S5.

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Referee #1

Evidence, reproducibility and clarity

This is an interesting and thorough study characterising human ipsc with hetero or homozygous mutation in pi3k pathway that lead to its hyper-activation. They prove that the increased stemness is results from enhanced autocrine responsiveness to TGF signalling pathway.

The main conclusions are well supported by the presented data. cutting edge tools and bioinformatic analysis are adequately applied. I have only one important point:

Major comment:

1) western blot based validation of TGF pathway activation in wt and mutant ipscs will be helpful to strengthen the results based on bioinformatic data.

Significance

Important work for studies on signalling, cancer mutations, modelling cancer in stem cells, pluripotency regulation.

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Reply to the reviewers

Response to the reviewers’ comments:

We thank both the reviewer for their critical evaluation and excellent suggestion to improve the manuscript. We are making all the changes suggested by both the reviewers and performing the experiments to address all the concerns specifically from the reviewer #1. Please find below our response to the reviewers’ comments:

Reviewer #1:

This is an interesting study from the Rahaman group that identifies cardiolipin (CL) as a potential binding target for Drp6 recruitment to the nuclear membrane in Tetrahymena (that has a unique nuclear remodeling program). In addition, they identify a residue, I553 in the DTD region, which they claim is a key residue involved in specific CL interactions. While the experiments themselves are technically sound, and are well performed and controlled, I don't find the major conclusion that I553 is involved in direct CL interactions justified or well rationalized. By their own admission (in the discussion), the conservative mutation I553M may perturb local folding and may indirectly affect CL interactions. There is no test of DTD folding with and without the I553M mutation, nor are there other mutations (e.g. I553A and in the vicinity) tested. CD experiments in the absence and presence of CL-containing membranes will likely yield information on the impact of the I553 mutations, while DLS experiments would inform on the hydrodynamic properties (overall 3D fold) of the DTD and the impact of these mutations. CL interactions generally involve a combination of electrostatic and hydrophobic forces. Where do the electrostatic interactions come from? Why would an Isoleucine to Methionine mutation affect the hydrophobic component, even if I553 is the key hydrophobic residue?

Response:

We thank the reviewer for the comments that the experiments are sound, well performed with appropriate controls. While we agree that the exact mechanism of how I553 provides specificity to cardiolipin binding is not addressed in the present manuscript, our study clearly demonstrates that the isoleucine at 553 plays important role in determining cardiolipin specificity and nuclear recruitment. As pointed out by the reviewer, it is possible that changing isoleucine to methionine may affect the local conformation. However, there is no major conformational change in the DTD due to this mutation. This conclusion is based on clear loss of nuclear localization and cardiolipin interaction for the mutant without affecting other properties. The in vitro floatation assay clearly stablish that the effect is directly by inhibiting interaction specifically with cardiolipin containing membrane. It should be further noted that the same domain DTD interacts with other two lipids (PS and PA) and mutant retains interaction with them arguing that conformation of this domain is not significantly changed due to I to M mutation. Consistent with these results I553M mutant could be targeted to the nuclear membrane as a complex with wildtype Drp6 further confirming that I553 could form correct self-assembled structure with wildtype protein required for association with nuclear membrane. This is further substantiated by comparing all the known biochemical properties including GTPase activity, membrane binding via other two lipids, formation of helical spirals and ring structures. Hence it is clear that I553 provides specificity to bind cardiolipin and recruitment to the nuclear membrane. We will further confirm if there is any local conformation change due to the mutation I to M by fluorescence quenching experiments and will be incorporated in the revised manuscript.

Regarding overall folding of the mutant, this is an excellent suggestion by the reviewer. We are planning to perform CD experiments of the I553M mutant and wildtype proteins to compare if there is any change in overall folding due to mutation. This result would be incorporated in the revised manuscript.

Reviewer is right to point out that both electrostatic and hydrophobic interactions are important for interaction with cardiolipin. Electrostatic interaction is important for all the phospholipids while interacting with protein and is expected to come from other amino acid residues which are positively charged. Electrostatic interaction may contribute to the affinity of the interaction by providing additional binding energy. But considering its universal nature of interaction with all the phospholipids, it cannot give specificity for a specific lipid and hence would not discriminate among different phospholipids.

Regarding affecting hydrophobic component, the reviewer is correct that both are strong hydrophobic amino acids and loss of I553M interaction with cardiolipin may not be due to change in hydrophobicity

To address that the loss of cardiolipin interaction is not specific to methionine and is due to absence of isoleucine, the suggestion from the reviewer to replace I553 with A (alanine) is an excellent one. We are doing the experiments and we anticipate to incorporate these results in our revised manuscript.

Reviewer #1 (Significance (Required)):

The addressed phenomenon is restricted to Tetrahymena and may not have far reaching implications. Regardless, the identification of CL as a binding target for Drp6 at the nuclear membrane of this organism is in itself significant. The conclusion that I553 is the key CL binding residue is however not warranted. Additional experiments are needed to dissect how this residue impacts CL interactions and examine whether the observed effect is direct or indirect.

Response:

We thank the reviewer for appreciating the significance of this work. We agree that our data is Tetrahymena specific. However, we believe that the study is relevant for all the proteins whose association with target membranes depend on cardiolipin including many cardiolipin interacting DRPs (such as DRPs involved in biogenesis and maintenance of mitochondria).

We really appreciate the reviewer for the excellent suggestions. Based on this we are performing the following experiments.

1. CD experiments to assess overall folding of I553M and Wildtype protein
2. Fluorescence quenching of Tryptophan (at amino acid position 548) residue in the vicinity of I553 to compare conformation of the mutant with that of wildtype protein.
3. Evaluation of I553A in nuclear localization and cardiolipin binding. We anticipate these results to further confirm if I553 is the key CL binding residue and if the effect is direct.

The writing is not clear in some parts and may require a round of language editing. There are no issues with reproducibility.

Response

We thank the reviewer for pointing out the language editing. We will edit the language wherever we find it appropriate. We would highly appreciate if reviewer can indicate the portions that need special attention.

Reviewr #2:

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

Dynamin is a GTPase superfamily protein involved in membrane fusion and division. This paper focused on Drp6, one of the eight dynamin superfamily proteins of Tetrahymena, and analyzed its nuclear envelope localization mechanism by a combination of in vivo cytogenetical analysis and in vitro biochemical analysis for the various mutant Drp6 proteins. Results showed that a specific amino acid residue (isoleucine at the 553rd) in the membrane binding domain of Drp6 was required for its nuclear membrane localization, but this residue is not required for ER/endosome localization and GTPase activity. Furthermore, in vitro floating analysis using centrifugation indicated that Drp6 specifically bound to the cardiolipin at the 553rd isoleucine residue and this binding was required for Drp6's nuclear membrane localization. Finally, removal of cardiolipin from the conjugating cells using inhibitor treatment showed that cardiolipin was required for the new macronucleus formation (including the expansion of macronuclear envelope) through the function of Drp6. Based on these results, authors concluded that cardiolipin targets Drp6 to the nuclear membrane in Tetrahymena.

\*Major comments:***

The experimental data presented in this paper are reasonable and the results are solid, and therefore I think the deduced conclusions are convincing. However, to improve this paper, I have several minor comments to be revised before publication.

\*Minor comments:***

1. In the previous paper, it has been shown that GFP-Drp6 is localized in the inner nuclear membrane of both macronucleus and micronucleus. In this paper, however, this point is not clearly stated and is not shown in the figures --- I could not understand such localization pattern of GFP-Drp6 in Fig. 1C and Fig. 3b and the statements in the text. I suggest adding such statements somewhere in Introduction or Result section. Also, add adequate references to the corresponding statements in the text.
2. • Related to the comment 1, I suggest replacing Fig. 1C (images of fixed cells) with Fig. S1B (images of live cells) because nuclear localization of GFP-Drp6 are much clearer in Fig. S1B (live cell) than Fig. 1C (fixed cell), and because fixation may cause artificial redistribution of the proteins. Please add arrows in those figures to point out the position of micronucleus in those figures if necessary.*
3. • Similarly, I suggest replacing images of Fig. 5B (fixed cells) with those of Fig. S3 (live cells).*
4. • page 7, line 224: GFP-Nup3 is used as a marker protein of the nuclear pore complex (NPC). However, there is no description of how GFP-Nup3 is obtained or made. Add description how this DNA plasmid was obtained or generated.*
5. • Related to the comment 4, "Nup3" is first discovered in Malone et al., Eukaryotic Cells, 2009, but also soon after discovered as the name of "MicNup98B" in Iwamoto et al., Curr Biol, 2009 and used in several papers including Iwamoto et al., Genes Cells, 2010; JCS, 2015; JCS 2017; and more. Because Nup3 is the Tetrahymena paralogs of human Nup98 and the name of "Nup98" is well established to call these homologs in various eukaryotes, I suggest adding the name of "MacNup98B" after the word of "Nup3" for reader's better understanding. I also suggest adding appropriate references to refer to this protein as follows: Add Malone et al. 2009 for "Nup3" and Iwamoto et al., 2009 for "MacNup98B."*
6. • page 9, line 295: I wonder if "Fig. 3b" may be a mistake of "Fig. 5C." If so, please correct this.*
7. • page 10, the second paragraph (lines 311-322): This paragraph discussed the possible involvement of Drp6 in the nuclear envelope expansion of the post-zygotic nucleus. It may be interesting to point out that large-scale nuclear envelope reorganization including the formation of the redundant nuclear envelope and the type-switching of the NPC (from the MIC-type NPC to the MAC-type one) has been reported at this developmental stage (Iwamoto et al., JCS 2015). For example, the peculiar shaped nuclear envelope with the redundant/overlapping nuclear envelope structure can be seen and the MAC-type NPCs rapidly assembles to the expanding nuclear envelope. It may be interesting to point out that cardiolipin and Drp6 may be involved in these phenomena. But it is too speculative and therefore consider adding such a discussion as an option.*
8. • page 13, line 412: Is the word "GFP-drp6-I553M" written in italics intended for the gene for the GFP-drp6-I553M protein? If so, protein may be acceptable here. Make sure there are no problems with italicized characters. Also, check if the lowercase letter "d" in "drp6" is OK because large letters are used in other cases.*
9. • page 20, figure 1: I recommend switching the positions of HDyn1 and Drp6 in Figure 1a to keep the order in Figure 1b.*
10. • page 21, line 671: Add the word "Tetrahymena" before "Drp 6" to pair with the word "human dynamin 1".*
11. • page 23, line 729: Remove "and."*
12. • page 23, lines 729 and 731: Unify the expression of "cardiolipin" and "Cardiolipin"*
13. • page 23, line 732: Add "or" before "10% Phosphatidylserin."*
14. • page 24, Figure 3a: Please mark the position of I553M in the figure if possible. Alternatively, indicate the range of amino acid residues after the words "red" and "green" in the figure legend.* Response:

We thank the reviewer for the excellent comments that “the experimental data presented in this paper are reasonable and the results are solid, and therefore I think the deduced conclusions are convincing.” We also thank the reviewer for the minor comments which are thorough and very insightful. it will improve the manuscript substantially. We would incorporate all the changes in the revised manuscript.

Reviewer #2 (Significance (Required)):

The corresponding author and his colleagues have reported that Tetrahymena Drp6 is localized to the outer nuclear membrane of both macronucleus and micronucleus of Tetrahymena (Elde et al., 2005) and that Drp6 is required for the formation of new macronuclei during nuclear differentiation (Rahaman et al., 2008). Therefore, these parts are not novel.

The novelty of this study is as follows:

(1) The discovery of a specific amino acid residue (isoleucine at the 553rd) of Drp6 that is required for its nuclear membrane localization.

(2) the discovery of a lipid molecule, cardiolipin, as a critical partner for Drp6's nuclear membrane targeting.

(3) Discovery of involvement of cardiolipin in the new macronucleus formation (the expansion of macronuclear envelope) through the function of Drp6.

*

I think their findings are highly novel and will provide new insight into a field of cell biology. Especially, their findings will contribute to understanding how specific proteins targeted to the specific intracellular membranes. In addition, their methods (such as floatation assay) for analyzing the interaction between the protein of interest and lipid/liposomes will become an important tool.*

Response:

We are very happy to note that the reviewer has pointed out the significance of the present study. We fully agree with reviewer and appreciate thorough analysis and excellent conclusion from the reviewer.

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Referee #2

Evidence, reproducibility and clarity

Dynamin is a GTPase superfamily protein involved in membrane fusion and division. This paper focused on Drp6, one of the eight dynamin superfamily proteins of Tetrahymena, and analyzed its nuclear envelope localization mechanism by a combination of in vivo cytogenetical analysis and in vitro biochemical analysis for the various mutant Drp6 proteins. Results showed that a specific amino acid residue (isoleucine at the 553rd) in the membrane binding domain of Drp6 was required for its nuclear membrane localization, but this residue is not required for ER/endosome localization and GTPase activity. Furthermore, in vitro floating analysis using centrifugation indicated that Drp6 specifically bound to the cardiolipin at the 553rd isoleucine residue and this binding was required for Drp6's nuclear membrane localization. Finally, removal of cardiolipin from the conjugating cells using inhibitor treatment showed that cardiolipin was required for the new macronucleus formation (including the expansion of macronuclear envelope) through the function of Drp6. Based on these results, authors concluded that cardiolipin targets Drp6 to the nuclear membrane in Tetrahymena.

Major comments:

The experimental data presented in this paper are reasonable and the results are solid, and therefore I think the deduced conclusions are convincing. However, to improve this paper, I have several minor comments to be revised before publication.

Minor comments:

1. In the previous paper, it has been shown that GFP-Drp6 is localized in the inner nuclear membrane of both macronucleus and micronucleus. In this paper, however, this point is not clearly stated and is not shown in the figures --- I could not understand such localization pattern of GFP-Drp6 in Fig. 1C and Fig. 3b and the statements in the text. I suggest adding such statements somewhere in Introduction or Result section. Also, add adequate references to the corresponding statements in the text.
2. Related to the comment 1, I suggest replacing Fig. 1C (images of fixed cells) with Fig. S1B (images of live cells) because nuclear localization of GFP-Drp6 are much clearer in Fig. S1B (live cell) than Fig. 1C (fixed cell), and because fixation may cause artificial redistribution of the proteins. Please add arrows in those figures to point out the position of micronucleus in those figures if necessary.
3. Similarly, I suggest replacing images of Fig. 5B (fixed cells) with those of Fig. S3 (live cells).
4. page 7, line 224: GFP-Nup3 is used as a marker protein of the nuclear pore complex (NPC). However, there is no description of how GFP-Nup3 is obtained or made. Add description how this DNA plasmid was obtained or generated.
5. Related to the comment 4, "Nup3" is first discovered in Malone et al., Eukaryotic Cells, 2009, but also soon after discovered as the name of "MicNup98B" in Iwamoto et al., Curr Biol, 2009 and used in several papers including Iwamoto et al., Genes Cells, 2010; JCS, 2015; JCS 2017; and more. Because Nup3 is the Tetrahymena paralogs of human Nup98 and the name of "Nup98" is well established to call these homologs in various eukaryotes, I suggest adding the name of "MacNup98B" after the word of "Nup3" for reader's better understanding. I also suggest adding appropriate references to refer to this protein as follows: Add Malone et al. 2009 for "Nup3" and Iwamoto et al., 2009 for "MacNup98B."
6. page 9, line 295: I wonder if "Fig. 3b" may be a mistake of "Fig. 5C." If so, please correct this.
7. page 10, the second paragraph (lines 311-322): This paragraph discussed the possible involvement of Drp6 in the nuclear envelope expansion of the post-zygotic nucleus. It may be interesting to point out that large-scale nuclear envelope reorganization including the formation of the redundant nuclear envelope and the type-switching of the NPC (from the MIC-type NPC to the MAC-type one) has been reported at this developmental stage (Iwamoto et al., JCS 2015). For example, the peculiar shaped nuclear envelope with the redundant/overlapping nuclear envelope structure can be seen and the MAC-type NPCs rapidly assembles to the expanding nuclear envelope. It may be interesting to point out that cardiolipin and Drp6 may be involved in these phenomena. But it is too speculative and therefore consider adding such a discussion as an option.
8. page 13, line 412: Is the word "GFP-drp6-I553M" written in italics intended for the gene for the GFP-drp6-I553M protein? If so, protein may be acceptable here. Make sure there are no problems with italicized characters. Also, check if the lowercase letter "d" in "drp6" is OK because large letters are used in other cases.
9. page 20, figure 1: I recommend switching the positions of HDyn1 and Drp6 in Figure 1a to keep the order in Figure 1b.　
10. page 21, line 671: Add the word "Tetrahymena" before "Drp 6" to pair with the word "human dynamin 1".
11. page 23, line 729: Remove "and."
12. page 23, lines 729 and 731: Unify the expression of "cardiolipin" and "Cardiolipin"
13. page 23, line 732: Add "or" before "10% Phosphatidylserin."
14. page 24, Figure 3a: Please mark the position of I553M in the figure if possible. Alternatively, indicate the range of amino acid residues after the words "red" and "green" in the figure legend.　

Significance

The corresponding author and his colleagues have reported that Tetrahymena Drp6 is localized to the outer nuclear membrane of both macronucleus and micronucleus of Tetrahymena (Elde et al., 2005) and that Drp6 is required for the formation of new macronuclei during nuclear differentiation (Rahaman et al., 2008). Therefore, these parts are not novel.

The novelty of this study is as follows: (1) The discovery of a specific amino acid residue (isoleucine at the 553rd) of Drp6 that is required for its nuclear membrane localization. (2) the discovery of a lipid molecule, cardiolipin, as a critical partner for Drp6's nuclear membrane targeting. (3) Discovery of involvement of cardiolipin in the new macronucleus formation (the expansion of macronuclear envelope) through the function of Drp6.

I think their findings are highly novel and will provide new insight into a field of cell biology. Especially, their findings will contribute to understanding how specific proteins targeted to the specific intracellular membranes. In addition, their methods (such as floatation assay) for analyzing the interaction between the protein of interest and lipid/liposomes will become an important tool.

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Referee #1

Evidence, reproducibility and clarity

This is an interesting study from the Rahaman group that identifies cardiolipin (CL) as a potential binding target for Drp6 recruitment to the nuclear membrane in Tetrahymena (that has a unique nuclear remodeling program). In addition, they identify a residue, I553 in the DTD region, which they claim is a key residue involved in specific CL interactions. While the experiments themselves are technically sound, and are well performed and controlled, I don't find the major conclusion that I553 is involved in direct CL interactions justified or well rationalized. By their own admission (in the discussion), the conservative mutation I553M may perturb local folding and may indirectly affect CL interactions. There is no test of DTD folding with and without the I553M mutation, nor are there other mutations (e.g. I553A and in the vicinity) tested. CL interactions generally involve a combination of electrostatic and hydrophobic forces. Where do the electrostatic interactions come from? Why would an Isoleucine to Methionine mutation affect the hydrophobic component, even if I553 is the key hydrophobic residue? Additional experiments are therefore essential to identify the actual residues involved in specific CL interactions. CD experiments in the absence and presence of CL-containing membranes will likely yield information on the impact of the I553 mutations, while DLS experiments would inform on the hydrodynamic properties (overall 3D fold) of the DTD and the impact of these mutations.

The writing is not clear in some parts and may require a round of language editing. There are no issues with reproducibility.

Significance

The addressed phenomenon is restricted to Tetrahymena and may not have far reaching implications. Regardless, the identification of CL as a binding target for Drp6 at the nuclear membrane of this organism is in itself significant. The conclusion that I553 is the key CL binding residue is however not warranted. Additional experiments are needed to dissect how this residue impacts CL interactions and examine whether the observed effect is direct or indirect.

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Reply to the reviewers

This is a fascinating and beautifully written article about the possible evolutionary relationship between two major protein superfamilies - the P-loop NTPases and the Rossmans. Both are ancient and highly diverse superfamilies, containing a significant proportion of all extant domain sequences and were probably amongst the earliest enzyme superfamilies to emerge in evolution. No major evolutionary classification of proteins, such as SCOP, reports evolutionary relationships between them.

Both share the same structural architecture of a beta-alpha-beta 3-layer sandwich and have an intriguing number of other shared structural features including the location of the binding site for phospho-ligands. However, whilst both bind phosphorylated ribonucleosides, the mode of binding differs and also the manner in which these compounds are exploited. Furthermore, there are differences in the topologies of the folds possibly suggesting distinct evolutionary trajectories. The Rossmanns appear to be more structurally conserved, whilst the P-Loops vary more in their topologies and possibly represent less stable arrangements of beta-sheets and alpha-helices. The authors have brought together several strands of evidence to explore possibly evolutionary relationships. Detailed structural analyses allow the authors to explicitly detail the significant shared structural features. For example, similarities in the mode of binding the phosphate moiety in the ligand. The structural features are well described and there are appropriate illustrations visualising key differences and similarities. The shared features of the phosphate binding site likely emerged and were favoured early in evolution, as supported by other analyses reported by Longo et al. However, as the authors point out there are other compelling similarities including the equivalent location of this site in the first beta-loop-alpha element in both superfamilies, which is not a necessary constraint of phosphate binding and the authors support this by giving examples of phosphate binding at the tip of alpha-4. In addition, they provide evidence supporting the common involvement of beta-2 which contains the conserved Asp in the Rossmanns common ancestor. The Walker-B Asp in the P-loops is also at the tip of the beta-strand adjacent to beta-1, as in the Rossmanns - although this is an inserted strand relative to the Rossmann topology. The authors propose feasible evolutionary scenarios for how the P-Loops and Rossmans may have diverged to acquire additional secondary structure elements extending the common beta-PBL-alpha-beta-Asp feature present in both superfamilies. Further compelling evidence is given by detection of a bridging protein - Tubulin - linking the two superfamilies. This has the distinct Rossmann topology but binds GTP in the P-loop NTPase mode. Furthermore, the GTP is hydrolysed by water activated by a ligated metal dication. Final support is given by reporting common sequence themes between the P-loop enzyme HPr kinase/phosphatase and some Rossmann proteins. The authors present further interesting and detailed analyses of similarities between the proteins sharing this unusual theme. The evidence provided by the authors for the shared beta-PBL-alpha-beta-Asp fragment seems very strong to me and has been presented in an interesting and informative way. Of course, it is not possible to know the subsequent evolutionary trajectories but the scenarios presented seem plausible.

We thank the reviewer for their encouraging remarks on our manuscript.

**I only have minor comments** 1) SCOP2 provides information on links between superfamilies based on rare sequence or structural features. Have the authors checked this resource for any details on beta-PBL-alpha-beta-ASP fragment? Or perhaps consulted with Alexey Murzin about this feature?

The classification of Rossmann and P-Loop proteins in SCOP2 is consistent with the ECOD classification scheme. For further confirmation, we wrote Alexey Murzin and he replied that Rosmanns and P-Loops are annotated as two separate evolutionary lineages, termed “hyperfamilies” in SCOP2. He found our new evidence compelling, but that given the current criteria for shared ancestry, P-loops and Rossmanns are separate lineages.

2) I was rather confused by the way in which EC annotations were collected for the two superfamilies ie via Pfam – wouldn’t it be better to use SUPERFAMILY as the domain structures would map directly to these sequence relatives. I’m also surprised that they only took the common EC from a Pfam family since the aim of this analysis was to identify how many different enzyme functions the two superfamilies supported. Pfam does not classify by function and so inevitably groups functionally diverse relatives. However, to get the full range of enzyme functions supported by these superfamilies I would have thought all non-redundant EC functions across these constituent Pfam families should be counted. Perhaps I have misunderstood.

We have updated the analysis to make use of the SUPERFAMILY database and, as per your suggestion, we now count all non-redundant EC numbers. Although the EC number counts have somewhat changed, the major point – that these are exceptionally diverse evolutionary lineages – has not.

3) The authors refer to a set of previously curated ‘themes’ and allude to a methodology that will be reported in a forthcoming manuscript. The idea of identifying rare themes and then using them to locate very distant homologues is appealing. However, I think some details should be provided here. For example, some brief details on the technology for detecting the themes and thresholds on significance. How rare are they and how conserved do these fragments need to be between superfamilies to join their curated list? Furthermore, how many of these curated themes are similar to the one reported in their article and do they get crosslinks to other superfamilies based on closely related themes? ie how unique is this theme to the P-loop and Rossmanns and are there closely related themes linking these two superfamilies to other superfamilies? I would imagine it is quite a distinct theme but I would have liked to see a few more details on this to reassure that there are no closely related themes.

We have updated the manuscript to include a more detailed description of the methods used to detect bridging themes shared between the Rossmann and P-Loop evolutionary lineages. In addition, we now include a supplemental table (Table S2) with all of the initial hits from the theme analysis.

4) The authors have built model structures to allow them to estimate ligand location in proteins with no structural characterisation. It would be helpful if they reported the degree of sequence similarity between the query and template proteins and also the model quality.

We have updated this section to include more details. In addition, we have identified a structure from the same T-group to serve as our ligand donor. The updated ligand donor is more closely related to 1ko7 than the previous ligand donor, though the positioning of the ligand is effectively unchanged. We note that the global sequence identity to both the previous and new ligand donor is low (less than 30% sequence identity). However, the phosphate binding loops align well in both sequence and structure, as is detailed in the revised Methods section.

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The study by Longo et al. was devoted to evolutionary history of P-loop NTPases and Rossmann fold proteins. Although not related in sequence, the two protein families share some structural features that imply that they could be diverged from a common ancestor. Using bioinformatic analyses, the study under review identified some bridge proteins (of tubulin family) that share themes of both P-loops and Rossmanns, offering a possible support for the common ancestry. A minimum ancestral peptide structure is proposed based on the analysis and its possible diversification trajectory is hypothesized. Even though the divergence scenario is clearly outlined, the authors do not over-interpret the observations and admit that convergence could still explain the scenario. The methodology and results are sufficiently described and conclusions are explained in detail. Although it would be really interesting to design an experimental study to support the conclusion (and I suppose that the authors will do that), that is clearly outside the scope of this bioinformatic study.

Obtaining experimental evidence for our hypothesis is far from trivial. Modern proteins, including the bridging ones identified here, may not be amenable to exchange due to differing contexts (epistasis). Still, we agree that highlighting experimental directions is a good idea. We have updated the sections From an ancestral seed to intact domains and Conclusion to include a brief discussion of experiments that may help test our hypotheses about the evolution of these protein lineages.

I would not propose any major changes to the manuscript as I think that the message is very clear. **Minor comments:** (1)In the results section, the text is very clear but tends to be repetitive in places. I think the manuscript would be more easily readable if more to the point at some sections.

We have edited the manuscript to remove cases of unnecessary repetition in the results section and throughout.

(2)There is probably a few typos or unclear sentences, e.g. pg 5, mid-page, "The core, most common topology...); pg 12, three lines from the bottom "(where this element in canonical", probably should be "is canonical"; pg 11, mid page "the mode of binding of the catalytic dication of tubuling (often Ca2+)" - all the structures listed in Table S1 list Mg2+, so "often" is a bit misleading.

We have corrected the unclear sentences and typos noted above, as well as a few others.

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Referee #2

Evidence, reproducibility and clarity

The study by Longo et al. was devoted to evolutionary history of P-loop NTPases and Rossmann fold proteins. Although not related in sequence, the two protein families share some structural features that imply that they could be diverged from a common ancestor. Using bioinformatic analyses, the study under review identified some bridge proteins (of tubulin family) that share themes of both P-loops and Rossmanns, offering a possible support for the common ancestry. A minimum ancestral peptide structure is proposed based on the analysis and its possible diversification trajectory is hypothesized.

Even though the divergence scenario is clearly outlined, the authors do not over-interpret the observations and admit that convergence could still explain the scenario. The methodology and results are sufficiently described and conclusions are explained in detail. Although it would be really interesting to design an experimental study to support the conclusion (and I suppose that the authors will do that), that is clearly outside the scope of this bioinformatic study.

I would not propose any major changes to the manuscript as I think that the message is very clear.

Minor comments:

(1)In the results section, the text is very clear but tends to be repetitive in places. I think the manuscript would be more easily readable if more to the point at some sections.

(2)There is probably a few typos or unclear sentences, e.g. pg 5, mid-page, "The core, most common topology...); pg 12, three lines from the bottom "(where this element in canonical", probably should be "is canonical"; pg 11, mid page "the mode of binding of the catalytic dication of tubuling (often Ca2+)" - all the structures listed in Table S1 list Mg2+, so "often" is a bit misleading.

Significance

I think this is a very interesting analysis of the evolutionary history of the P-loop and Rossmann fold family which are considered among the most ancient and abundant protein folds. That makes them of high interest also for origins of protein structure. The results are not firmly conclusive (because of the limits of such analyses), making the outcomes of the study partly hypothetical. I think it would be very interesting to outline suggestions for future experiments that could test the hypothesis to be more valuable to a broader audience.

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Referee #1

Evidence, reproducibility and clarity

This is a fascinating and beautifully written article about the possible evolutionary relationship between two major protein superfamilies - the P-loop NTPases and the Rossmans. Both are ancient and highly diverse superfamilies, containing a significant proportion of all extant domain sequences and were probably amongst the earliest enzyme superfamilies to emerge in evolution. No major evolutionary classification of proteins, such as SCOP, reports evolutionary relationships between them.

Both share the same structural architecture of a beta-alpha-beta 3-layer sandwich and have an intriguing number of other shared structural features including the location of the binding site for phospho-ligands. However, whilst both bind phosphorylated ribonucleosides, the mode of binding differs and also the manner in which these compounds are exploited. Furthermore, there are differences in the topologies of the folds possibly suggesting distinct evolutionary trajectories. The Rossmanns appear to be more structurally conserved, whilst the P-Loops vary more in their topologies and possibly represent less stable arrangements of beta-sheets and alpha-helices.

The authors have brought together several strands of evidence to explore possibly evolutionary relationships. Detailed structural analyses allow the authors to explicitly detail the significant shared structural features. For example, similarities in the mode of binding the phosphate moiety in the ligand. The structural features are well described and there are appropriate illustrations visualising key differences and similarities.

The shared features of the phosphate binding site likely emerged and were favoured early in evolution, as supported by other analyses reported by Longo et al. However, as the authors point out there are other compelling similarities including the equivalent location of this site in the first beta-loop-alpha element in both superfamilies, which is not a necessary constraint of phosphate binding and the authors support this by giving examples of phosphate binding at the tip of alpha-4. In addition, they provide evidence supporting the common involvement of beta-2 which contains the conserved Asp in the Rossmanns common ancestor. The Walker-B Asp in the P-loops is also at the tip of the beta-strand adjacent to beta-1, as in the Rossmanns - although this is an inserted strand relative to the Rossmann topology. The authors propose feasible evolutionary scenarios for how the P-Loops and Rossmans may have diverged to acquire additional secondary structure elements extending the common beta-PBL-alpha-beta-Asp feature present in both superfamilies.

Further compelling evidence is given by detection of a bridging protein - Tubulin - linking the two superfamilies. This has the distinct Rossmann topology but binds GTP in the P-loop NTPase mode. Furthermore, the GTP is hydrolysed by water activated by a ligated metal dication. Final support is given by reporting common sequence themes between the P-loop enzyme HPr kinase/phosphatase and some Rossmann proteins. The authors present further interesting and detailed analyses of similarities between the proteins sharing this unusual theme.

The evidence provided by the authors for the shared beta-PBL-alpha-beta-Asp fragment seems very strong to me and has been presented in an interesting and informative way. Of course, it is not possible to know the subsequent evolutionary trajectories but the scenarios presented seem plausible.

I only have minor comments

1)SCOP2 provides information on links between superfamilies based on rare sequence or structural features. Have the authors checked this resource for any details on beta-PBL-alpha-beta-ASP fragment? Or perhaps consulted with Alexey Murzin about this feature?

2)I was rather confused by the way in which EC annotations were collected for the two superfamilies ie via Pfam - wouldn't it be better to use SUPERFAMILY as the domain structures would map directly to these sequence relatives. I'm also surprised that they only took the common EC from a Pfam family since the aim of this analysis was to identify how many different enzyme functions the two superfamilies supported. Pfam does not classify by function and so inevitably groups functionally diverse relatives. However, to get the full range of enzyme functions supported by these superfamilies I would have thought all non-redundant EC functions across these constituent Pfam families should be counted. Perhaps I have misunderstood.

3)The authors refer to a set of previously curated 'themes' and allude to a methodology that will be reported in a forthcoming manuscript. The idea of identifying rare themes and then using them to locate very distant homologues is appealing. However, I think some details should be provided here. For example, some brief details on the technology for detecting the themes and thresholds on significance. How rare are they and how conserved do these fragments need to be between superfamilies to join their curated list? Furthermore, how many of these curated themes are similar to the one reported in their article and do they get crosslinks to other superfamilies based on closely related themes? ie how unique is this theme to the P-loop and Rossmanns and are there closely related themes linking these two superfamilies to other superfamilies? I would imagine it is quite a distinct theme but I would have liked to see a few more details on this to reassure that there are no closely related themes.

4)The authors have built model structures to allow them to estimate ligand location in proteins with no structural characterisation. It would be helpful if they reported the degree of sequence similarity between the query and template proteins and also the model quality.

Significance

This article present compelling new evidence on the evolutionary relationship between two major, ancient enzyme superfamilies. As far as I'm aware these insights are novel and the detection of the bridging protein relative and the common 'theme', i.e. beta-PBL-alpha-beta-Asp fragment, is a new discovery.

This work makes an important contribution to understanding the evolution of two major enzyme superfamilies and the insights can guide future evolutionary studies and protein design studies.

The audience will be structural and evolutionary biologists, both experimental and computational.

My expertise is in protein evolution and protein structure analyses and I have published a number of reviews and articles analysing and discussing Rossmann-like superfamilies.

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Reply to the reviewers

RESPONSE TO REVIEWER #1

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

In this manuscript, Ishihara et al. investigate and compare microtubule polymerization/depolymerization dynamics inside vs. at the periphery of microtubule asters in a cell-free Xenopus egg extract system. By tracking EB comets, which localize to growing microtubule ends, they find that the microtubule growth rates and EB comet lifetimes (interpreted as an indicator of microtubule catastrophe rates) are similar between the two spatially-distinct microtubule populations. However, using a tubulin-intensity-difference image analysis, the authors are also able to measure local microtubule depolymerization rates, and they find a significant difference in depolymerization rates of the two populations. Specifically, the authors report that the microtubule depolymerization rates measured within asters are faster than those measured at the periphery.

\*Specific comments:***

Figure 2.

In the text, the authors report: "The depolymerization rate was 36.3 {plus minus} 7.9 μm/min (mean, std) in the aster interior, compared to 29.2 {plus minus} 8.9 μm/min (mean, std) at the aster periphery." This difference is certainly not two-fold (as stated in the abstract). It would also be useful to mark the mean rates on the graph in 2B.

We removed the words ‘almost two-fold’ in the abstract. In the revision, we will mark the mean rates on Fig. 2B (using vertical lines).

The bimodal shape of the depolymerization rate distributions in 2B is very interesting. This definitely warrants further investigation. At the minimum, the depolymerization rates should be determined at 50 um- intervals, as done for other parameters in Figure 1. Could it be that there are two coexisting populations of microtubules at the same location? Or is there a clear spatial compartmentalization of the two that is not obvious here because of the too large of a distance interval used for the measurements. This is a very important distinction for the claims of the paper.

We understand the reviewer’s concern. There are some technical limitations that make the depolymerization measurement more challenging. While we use widefield imaging of EB1-GFP comets to obtain polymerization rates from a field of view spanning 500 microns, we may only use TIRF imaging for depolymerization measurements. In this method, we are limited to observing microtubules very close to the cover slip in a small field of view of 80x80 microns at 500 ms time intervals (movies span 1-2 minutes). One would need to move the TIRF field every 1-2 minutes at 50 micron intervals, but the aster periphery would be changing during this time, so the exact location of the measurement is hard to define. Thus, we opted to image the two spatial extremes: interior (close to the MTOCs) and the very periphery (where MT density is still sparse.)

Perhaps, the largest limitation of this approach is the choice of peripheral regions based on the apparent sparsity of MTs in the TIRF field of view. Indeed, when we examine the depolymerization rate distributions for individual movies separately (see figure below, periphery #1-3 are three individual movies), we observe that some movies have rates as low as 20 µm/min, while others have higher values with a center around 36 µm/min. The depolymerization rates for the interior also vary from the mean values of 34.8-43.2 µm/min (interior #1-3 are three individual movies). In general, the spread of depolymerization rate within a field of view as well as across different fields of view is much larger than for polymerization. It is possible that this is partly explained by the lack of precise definition of interior vs. periphery in this TIRF-based measurement approach.

Our data still supports the spatial regulation of depolymerization rate. However, there is no clear evidence for a bimodal distribution of depolymerization rate in any given field of view (80x80 micron square region). To clarify this point, we have removed the language “bimodal” in the main text. In the revisions, we will provide this figure as a supplement.

We thank the critical feedback from reviewer #1 and #2 that allowed us to clarify this issue of apparent bimodality of the depolymerization rates.

The authors make a point here that the distribution of measured polymerization rates is fairly narrow. This appears to be in contrast with Figure 1B, where polymerization rates take on a wide range of values. How do the two distributions of polymerization rates obtained by these two methods compare?

To address this point, we directly compare the standard deviation of the polymerization rate measurements. For Fig. 1B EB1 tracking measurements, std ranges from 7.7-10.5 µm/min for a given spatial bin (as stated in Fig. 1B legend), while for Fig. 2A TIRF measurements std is 4.0 (periphery) and 4.5 µm/min (interior) as stated in the main text. Given that the mean values of polymerization rates are similar, this suggests that the TIRF measurements are less noisy. This further highlights the relative pros and cons of the two measurement methods. To discuss these issues, we have added a new paragraph in the discussion section.

Figure 3.

The laser ablation figure and movies are beautiful, but don't seem to add support to the story. Importantly, the authors do not confirm any spatial variability in depolymerization rate with these experiment. As a matter of fact, although the laser ablation experiments are only performed in the aster interior, the measured depolymerization rates appear to be just as consistent with the periphery rates in Figure 2. as they are with the interior rates in Figure 2. (They span quite a large range of values with the average right in the middle between what was measured for the two areas in Figure 2).

Indeed, the values obtained with laser ablation are quite variable, even compared to the physiological depolymerization rate measured via TIRF microscopy. This perhaps reflects the variability of biology as well as the nature of the laser ablation which measures depolymerization rate at the level of microtubule populations. We hope our paper will increase interest in this rarely measured parameter, and perhaps invention of new probes to measure it more accurately and conveniently.

Given the variability of our measurements, we conclude that the results between the TIRF based approach vs. laser ablation based approach of depolymerization rates are indistinguishable. We agree with the reviewer that the data does NOT argue that laser ablation results are more consistent with the interior TIRF measurements than peripheral TIRF measurements.

To clarify this point, we remove the following clause “, which was comparable to the modal value of the depolymerization rates in the aster interior (Fig. 2).”

We change the concluding sentence of our laser ablation paragraph from

“Overall, these observations suggest that depolymerization dynamics are similar for plus ends following a natural catastrophe vs. ablation in the aster interior.”

to

“Overall, these observations confirm that depolymerization rates are variable, and we find no statistical distinction of rates between plus ends following a natural catastrophe vs. ablation.”

Although the authors report they don't see any correlation between the distance and depolymerization rate, they should still plot the rate as a function of initial cut positions (Figures 3D, 3E).

To address this concern, we plan to provide a supplemental figure in the revision. Please see the preliminary figure below. Due to technical limitations with the laser ablation system (field of view for 60x magnification), we only have measurements that span 15-100 microns from the center..

From the single decaying inward wave the authors conclude that microtubules depolymerize fully to their minus ends which are distributed throughout the aster. Can the possibility that depolymerization is stopped by microtubule lattice defects/islands be excluded by these observations?

The existence of microtubule lattice/defects is a recent development in the field and much is not known. If we assume that defects are structurally unstable, we predict that the episode of depolymerization will continue even when reaching a defect. If defects are stable and lead to instantaneous rescue of plus ends, we cannot distinguish the defects from minus ends. In this latter scenario, the interpretation of the decaying inward wave requires caution.

What are the effects of the local increase in tubulin concentration due to the subunit release by depolymerization? What about the release of other lattice-binding MAPs (stabilizers)?

We are interested in these questions as well. Soluble GDP-bound tubulin, released by depolymerization, is thought to exchange its nucleotide to GTP without need of a GEF, and no GEF is known. The dissociation rate of GDP is ~0.1 [1/sec], for a half-life of ~5 sec (Brylawski and Caplow, 1983, J. of Biol. Chem.), so we believe the tubulin subunits are recycled relatively quickly. It is not entirely obvious whether this necessarily results in a significant increase in ‘soluble’ tubulin concentration given tubulin diffusive transport. We hypothesize the main effect of stabilizing MAPs is on the depolymerization rate as discussed in our model in Fig. 5.

Figure 4.

Is the local depletion of tubulin/EB1 thought to be only within the narrow annulus at ~100 um distance, or is it not measurable on the inside due to the polymer signal? Can the two be separated? Such a sharp transition within a discrete annular region doesn't speak to the relative effects on the inside vs. the outside of the aster?!

Yes, we also believe the soluble tubulin levels are even lower in the more inner regions of the aster. However, polymerized tubulin accounts for a large part of the fluorescence intensity in these inner regions, and our method does not faithfully reflect the soluble fraction. It will be important for future studies to employ specific methods that may unequivocally distinguish polymer vs. soluble tubulin concentrations (see below).

More importantly, the local depletion of either tubulin or EB1 is not a good representation of a depletion of a MAP component that associates with the microtubule lattice. Both tubulin and EB1 bind preferably to microtubule ends, not lattice. Thus showing a profile of slight local tubulin and/or EB depletion does not seem to be relevant for the proposed model. Rather, overall microtubule polymer mass/density as a function of distance may be more relevant?

Reviewer #1 makes a valid point that tubulin and EB1 are specifically incorporated to plus ends and not to the entire lattice as we assume for the MAPs in our theoretical model. To address this issue, we analyzed the fluorescence intensity of images obtained for a MAP that associates with the MT lattice, Tau-mCherry (Mooney et al. 2017). This quantification shows a depletion pattern similar to tubulin and EB1. Thus, we believe the local depletion is a general feature. For the revision, we plan to incorporate this Tau-mCherry data in Fig. 4.

Figure 5.

The toy model is intuitive and clear, but not sufficient without any experimental investigation. An attempt to quantify the actual distributions of at least one or a few selected proposed MAPs is needed. Is the depletion strongest where microtubule density is highest? What is the ratio of a MAP intensity to microtubule polymer density as a function of distance? How does that relate to local depolymerization rates? What are other testable model predictions that can show support for the proposed mechanism?

We understand that our proposal is rather speculative, and the goal of this manuscript was to propose a hypothesis that may inspire others working on assembly on intracellular organelles. Although Tau is not an endogenous component of the egg extract system, we believe that our new quantification of Tau-mCherry depletion adds more credibility to our general proposal.

Microtubule density is roughly uniform within the interior of the aster according to our current understanding (Ishihara et al. 2016 eLife). So the MAP:MT ratio is relatively uniform throughout the aster except at the very periphery where there are very few MTs assembled (i.e. “depletion is weakest where MT density is lowest.”)

In the future, we may perform (1) FCS measurements of candidate MAPs to directly measure the concentration profile of the candidate MAP in soluble form and (2) depletion/addback to show which MAP most affects depolymerization rate. Although these experiments are appealing, this requires generation of new molecular reagents as well as calibration of a highly specialized optical method. Therefore, we decided to limit this paper to focus on the unusual observation of the variation of depolymerization rate and speculate the underlying mechanism.

Also, the table is insufficiently described. Are any or all of these MAPs known to be specific regulators of microtubule depolymerization rates, but not other dynamics parameters?

There are a large number of MAPs in Xenopus eggs, as there are in all cells, and the degree to which their effects on microtubules has been characterized is variable. To address this comment we include in the revised ms a list of known MAPs that are present in Xenopus egg extract, along with their estimated concentration from a published proteomic study. We annotate each MAP as to whether it increases or decreases microtubule stability, acknowledging that these data are very incomplete, in some cases there is disagreement in literature, and that we are combining pure protein and whole cell analysis. This table illustrates the challenge of associating dynamics regulation with any one MAP, since the behavior of microtubules is regulated by all these factors operating in parallel. That said, certain MAPs jump out as candidate depolymerization regulators that have been little studied for effects on dynamics, for example, MAP7.

In the revision, we suggest to add this expanded table as a supplementary Table in addition to Table 1.

Protein Description

Gene Symbol

Est. Conc. (nM)

MT polymerization/nucleation/rescue?

MT depolymerization/catastrophe?

Lead reference

Microtubule-associated protein RP/EB family member 1

MAPRE1

1800

Increase

Decrease

PMID: 18364701

Stathmin

STMN1

1600

Decrease

Increase

PMID: 11792540

MAP4

MAP4

960

Increase

Decrease

PMID: 7962090

Echinoderm microtubule-associated protein-like 2

EML2

580

Decrease

Increase

PMID: 11694528

EML4 protein

EML4

500

Increase

Decrease

PMID: 17196341

Disks large-associated protein 5

DLGAP5

380

Increase

Decrease

PMID: 16631580

Cytoskeleton-associated protein 5

CKAP5

300

Increase

Increase

PMID: 23666085

Kinesin-like protein KIF2C

KIF2C

200

Decrease

Increase

PMID: 12620232

CAP-Gly domain-containing linker protein 1

CLIP1

190

na

na

Cytoskeleton-associated protein 4

CKAP4

160

Increase

Decrease

PMID: 9799226

Echinoderm microtubule-associated protein-like 1

EML1

140

na

na

Ensconsin

MAP7

91

na

Decrease

PMID: 31391261

Targeting protein for Xklp2

TPX2

91

Increase

Decrease

PMID: 26414402

Microtubule-associated protein 1B

MAP1B

85

Increase

Decrease

PMID: 7664878

MAP1S

MAP1S

66

Decrease

Decrease

PMID: 25300793

Hyaluronan mediated motility receptor

HMMR

61

na

na

MAP7 domain-containing protein 1

MAP7D1

47

na

na

Cytoskeleton-associated protein 2

CKAP2

46

Increase

Decrease

PMID: 15504249

Microtubule-associated tumor suppressor 1

MTUS1

43

na

na

Kinesin-like protein KIF2A

KIF2A

37

Decrease

Increase

PMID: 29980677

CLIP-associating protein 1

CLASP1

30

Decrease

Decrease

PMID: 29937387

Microtubule-associated protein RP/EB family member 3

MAPRE3

21

Increase

Decrease

PMID: 20850319

MAP7 domain containing 2 protein variant 2 (Fragment)

MAP7D2

8

na

na

CAP-Gly domain-containing linker protein 4

CLIP4

2

na

na

\*Minor comments:***

Figure 1.

typo in the figure legend: "interior (distance>300 μm) vs. periphery (50 μmThere appears to be a clear dip in EB1 density at 100 um (Figure 1C). What could be the cause of that?*

Thank you for catching the typo. We corrected this to “periphery (distance>300 µm) vs. interior (50 µmFigure 2.

Note that the distances used in Figure 2. to define 'interior' and 'periphery' are completely different than those in Figure 1. (Interior in Figure 1 is defined to be between 50 and 280 um from the MTOC, and exterior larger than 300 um. However, in Figure 2. interior is defined as less than 100 um, and exterior as larger than 200 um.) Given that the asters are actively growing, it would be good to clearly explain how these intervals were defined in each case.

For both experiments, we had clearly stated the definitions of interior and periphery, either in the figure legends or in the methods section. We have added a new paragraph explaining why we could not choose exactly the same quantitative definitions for these two methods (please also see our reply to Reviewer #2 comment 1).

In the periphery movie, there are several notable examples of apparent minus-end depolymerization and treadmilling. The authors state these are very rare - perhaps a quantification would be useful here?

Thank you for pointing this out. We modified the sentence to reflect the outward depolymerization events in the periphery. “We observed few outward-moving depolymerization events (Reviewer #1 (Significance (Required)):

The observation of distinct depolymerization rates within vs. at the periphery of microtubule asters is novel and interesting. However, the manuscript in its current form is rather preliminary. The observation can be significantly strengthened by additional experiments/analysis that would characterize the effect in more detail. Even more importantly, the authors propose a highly speculative (although compelling) mechanism, but make no attempt to test it in any way. This is a major deficiency of the current manuscript that should be addressed prior to publication.

REFEREES CROSS COMMENTING

I agree with Reviewer #2 that our comments are both overlapping and complementary. I also find Reviewer #2's comments fair and reasonable and see no need for further adjustments.

RESPONSE TO REVIEWER #2

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

\*SUMMARY ***

This paper reports measurements of microtubule dynamics in interphase asters nucleated in Xenopus egg extracts. Dynamics are measured using two methods. First tracking of GFP tagged EB1 protein forming comets at the tips of growing microtubules, as used in other studies, which can only measure growth rates. Second using a recently developed automated tracking based on subtractive difference images of fluorescently labelled microtubules, which can measure both growth and shrinkage rates. The main and novel observation of this paper, using difference image tracking, is that the MT shrinkage rate is ~2 fold faster in the interior of the aster compared with the periphery of the aster, whilst rates of MT polymerisation and catastrophe vary only slightly, if at all. The authors speculate that this might be due to a reduced MAP concentration and occupancy in the aster interior. They also discuss the role of a depletion-dependent increased shrinkage rate as a feedback mechanism to maintain a low MT polymer density in the aster interior.

\*MAJOR COMMENTS***

The movies are startling in their beauty and clarity and the key conclusion that the shrinkage rate is significantly faster in the interior compared to the periphery of the aster is convincing.

The observation that the rate of net MT plus end growth rate is ~10% faster at the periphery compared to interior of the aster is only supported by EB1 tip tracking method. The difference imaging method shows no significant difference in rates. The authors need to discuss this discrepancy between the established and new methods of analysis. It is insufficient to state that the growth rates obtained by the two methods are "consistent".

This comment prompts the comparison of the two methods (EB1 vs. TIRF difference imaging). On one hand, EB1 tracking is more sensitive in detecting plus ends, and allows large N observations so it is likely to show statistical significance. On the other hand, EB1 tracking method is noisier (higher standard deviation) than the TIRF based measurements (see our response to Reviewer #1). In the TIRF difference imaging, the exact location of the periphery (relative to the center as well as the overall microtubule density profile) is hard to evaluate.

What is consistent between the two methods is the approximate mean value of polymerization rates. The 10% faster polymerization velocity is only suggested by the EB1 tracking method, calling for caution/further investigation. However, the potential relatively small difference in polymerization rate is not the main point of this paper.

We deleted the sentence in the results section for the TIRF method: “These values of polymerization rates are consistent with EB1 comet tracking (Fig. 1). ” We have added a new paragraph discussing the discrepancies between the methods in reporting polymerization rate.

The discussion proposing MAP depletion-dependent increased shrinkage rate as a feedback mechanism to limit MT polymer density is reasonable.

The model and discussion of the role of MAPs might be criticised as highly speculative and unsupported by any experimental data. The authors do acknowledge this. Whether the ratio of data to speculative interpretation is appropriate will be an editorial decision for whichever journal ultimately hosts this.

Thank you. This is exactly the kind of comments that we wanted to hear from an initiative like Review Commons. This helps us gauge how our work is received and decide which journal to submit our work.

In particular since the aster forms by growth from the nucleating bead, early in its formation the final interior MTs must have first formed the peripheral MTs and could therefore enter fresh media and bind MAPs. The authors show by calculation that as the aster expands, these MTs and MAPs become isolated from mixing with the external media. This isolation would then suggest that any MAPS released by dissociation or MT depolymerisation must remain in the interior, and are therefore available to rebind to newly formed MTs. So, it is unclear why the MAPs should be depleted in the interior compared to the periphery, unless expansion of the Aster is slowed in which case additional MAPs could diffuse into the stationary periphery from the surrounding media. The kinetics of MT growth, MAP binding and aster expansion would then also be expected to have an effect on the outcome beyond a simple "depletion" of the internal MAP concentration.

We use the term “depletion” to mean a significant decrease of MAP from the cytoplasm. As outlined in our toy model, more MTs lead to more MAP binding and depletion of soluble MAPs. Note that the total local abundance of MAP is constant unless there is significant diffusive transport of MAP from one region to another. We argue this transport is ineffective for the large length scale of interphase asters.

It is also not clear how the authors preferred model would account for the suggestion of bimodal shrinkage rates. It is not clear if this is a simplification (binning things in to external and internal) applied for the purposes of discussion.

Please see our comment to Reviewer #1. We now believe there is no evidence for bimodality of depolymerization rates. The spread of the data reflects the variability of depolymerization rates in a given a field of view as well as the variability across multiple fields of view.

\*MINOR COMMENTS***

Line 71

Authors reference Gardner et al 2011, when discussing depolymerisation as a zero order process, as showing a free tubulin dimer concentration effect on shrinkage rates. However, the results in Gardner refer to the off rate during MT polymerisation, and measurements of rapid small scale events during overall growth phases and would be applicable to GTP-heterodimers, whereas the extended shrinkage events measured in this paper would presumably apply to post-catastrophe GDP-heterodimer dissociation and may not be comparable. The reference should be omitted or a further explanation given.

Thanks, good point. We wanted to cite Gardner et al (2011) to make the point that classic assembly models may not always hold, but the reviewer is correct, that paper only looked at concentration dependence of depolymerization at growing ends. The text was changed to:

“This assumption has been questioned for growing ends (Gardner 2011)​, but not for shrinking ends to our knowledge.”

Line 89

States "density of plus ends is approximately homogenous within interphase asters"

However, in results section it is stated Line 111 that "the plus end density is lower at the periphery compared to the aster center".

Please clarify

The plus end density is approximately homogenous from the center to the periphery of the aster. However, only at the most peripheral region, where there are few microtubules, the density drops.

Line 135

The distances given for the interior and periphery appear to be mixed up.

Thank you, we corrected this.

Line277

"approximately consistent with our Peclet number estimate". 50µm gives a Pe value of 2.8. The Peclat number "significance" is earlier given in terms of "Pe>>1" (Line255). Please clarify what range of experimental values is required for the argument to hold.

Our statement was unclear. We modified the sentence in the following way to clarify our point: “The half-width of the depleted zone extended ~50 microns beyond the growing aster periphery, which is smaller than the typical aster radius. This analysis indicated that soluble protein levels may vary between subregions of growing asters due to subunit consumption.”

Line 404

needs details of the GFP-EB1 and fluorescent tubulin used in this experiment.

The detailed concentrations are described for each method in the subsequent sections. To avoid confusion, we removed the sentence in line 404, which omitted details.

The tubulin depletion measurements detect a 4% reduction in tubulin concentration in the interior versus the exterior, and the same for eGFP-EB1 (Fig.4B). This observation provides important support for the depletion proposal. But the experiments apparently lack a control for potential reduction of fluorescence excitation intensity with depth in these deep specimens (equivalent to the inner filter effect in spectroscopy). Is there a component whose apparent concentration (fluorescence emission intensity) does not decrease by 4% in the interior of the aster?

Indeed, fluorescent intensity measurements require special attention. Our samples are made by squashing 4 ul of extract under a 18 mm x 18 mm coverslip and the resulting thickness is 10 micron, which we believe is a distance that is too small to result in an inner filter effect.

In response to Reviewer #2’s request for an example of a component whose fluorescence intensity is uniform, we provide the intensity profile of the inert 10kDa Dextran labeled with Alexa568. This serves as a control for the reviewer’s specific concern with our method. We will incorporate this as a supplementary figure in the revision.

There is no direct discussion of the relative lifetime of MTs in the interior compared to the exterior of the aster. Catastrophe rates and growth rates are essentially invariant, I think this implies that MT lifetimes are essentially the same in the interior versus the exterior? Please confirm and estimate the lifetime. This could exclude a maturation process whereby one set of MAPs got replaced by another over time?

Indeed, MT lifetime is a function of four rates: polymerization, depolymerization, catastrophe, and rescue. The figure below shows the MT lifetime as a function of depolymerization rate, assuming other parameters are fixed at what we found in our previous report Ishihara et al. 2016. In regions of fast depolymerization rate 40 µm/min, the microtubule lifetime is 0.98 min. As the depolymerization rate decreases to 30 and 25 µm/min, the lifetime increases to 1.5 and 2.4 min. This implies that the microtubules at the aster periphery are longer lived than those in the interior.

Association and dissociation rate constants have not been measured for most MAPs, but in general we expect them to be fast compared to the timescale of MT lifetime of ~1 minute. Most MAPs bind in the low micromolar or high nM regime, which implies dissociation rates of seconds or less. MAP4 and MAP7 were both shown to bind and dissociate rapidly in living cells (PMID: 16714020, PMID: 11719555)

Reviewer #2 (Significance (Required)):

This paper is significant as it is the first observation of spatial variation in MT shrinkage rates in an aster. It proposes the broad shape of an underlying mechanism (depletion of stabilising MAPS in the aster interior) and presents sound quantitative arguments, but the experiments do not directly test this mechanism. Aster formation in Xenopus egg extracts is widely used as a model system, and if indeed the spatial variation turns out to be due to spatial depletion of components then this will become a landmark paper. The paper may promote wider use of this method of automated analysis and encourage study of shrinkage rate mechanisms in other systems.

REFEREES CROSS COMMENTING

In my opinion the comments of reviewer #1 are fair and reasonable and overlap with and complement my own. In my opinion there is zero conflict requiring adjustment.

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

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Referee #2

Evidence, reproducibility and clarity

SUMMARY

This paper reports measurements of microtubule dynamics in interphase asters nucleated in Xenopus egg extracts. Dynamics are measured using two methods. First tracking of GFP tagged EB1 protein forming comets at the tips of growing microtubules, as used in other studies, which can only measure growth rates. Second using a recently developed automated tracking based on subtractive difference images of fluorescently labelled microtubules, which can measure both growth and shrinkage rates. The main and novel observation of this paper, using difference image tracking, is that the MT shrinkage rate is ~2 fold faster in the interior of the aster compared with the periphery of the aster, whilst rates of MT polymerisation and catastrophe vary only slightly, if at all. The authors speculate that this might be due to a reduced MAP concentration and occupancy in the aster interior. They also discuss the role of a depletion-dependent increased shrinkage rate as a feedback mechanism to maintain a low MT polymer density in the aster interior.

MAJOR COMMENTS

The movies are startling in their beauty and clarity and the key conclusion that the shrinkage rate is significantly faster in the interior compared to the periphery of the aster is convincing.

The observation that the rate of net MT plus end growth rate is ~10% faster at the periphery compared to interior of the aster is only supported by EB1 tip tracking method. The difference imaging method shows no significant difference in rates. The authors need to discuss this discrepancy between the established and new methods of analysis. It is insufficient to state that the growth rates obtained by the two methods are "consistent".

The discussion proposing MAP depletion-dependent increased shrinkage rate as a feedback mechanism to limit MT polymer density is reasonable.

The model and discussion of the role of MAPs might be criticised as highly speculative and unsupported by any experimental data. The authors do acknowledge this. Whether the ratio of data to speculative interpretation is appropriate will be an editorial decision for whichever journal ultimately hosts this.

In particular since the aster forms by growth from the nucleating bead, early in its formation the final interior MTs must have first formed the peripheral MTs and could therefore enter fresh media and bind MAPs. The authors show by calculation that as the aster expands, these MTs and MAPs become isolated from mixing with the external media. This isolation would then suggest that any MAPS released by dissociation or MT depolymerisation must remain in the interior, and are therefore available to rebind to newly formed MTs. So, it is unclear why the MAPs should be depleted in the interior compared to the periphery, unless expansion of the Aster is slowed in which case additional MAPs could diffuse into the stationary periphery from the surrounding media. The kinetics of MT growth, MAP binding and aster expansion would then also be expected to have an effect on the outcome beyond a simple "depletion" of the internal MAP concentration.

It is also not clear how the authors preferred model would account for the suggestion of bimodal shrinkage rates. It is not clear if this is a simplification (binning things in to external and internal) applied for the purposes of discussion.

MINOR COMMENTS

Line 71 Authors reference Gardner et al 2011, when discussing depolymerisation as a zero order process, as showing a free tubulin dimer concentration effect on shrinkage rates. However, the results in Gardner refer to the off rate during MT polymerisation, and measurements of rapid small scale events during overall growth phases and would be applicable to GTP-heterodimers, whereas the extended shrinkage events measured in this paper would presumably apply to post-catastrophe GDP-heterodimer dissociation and may not be comparable. The reference should be omitted or a further explanation given.

Line 89 States "density of plus ends is approximately homogenous within interphase asters" However, in results section it is stated Line 111 that "the plus end density is lower at the periphery compared to the aster center". Please clarify

Line 135 The distances given for the interior and periphery appear to be mixed up.

Line277 "approximately consistent with our Peclet number estimate". 50µm gives a Pe value of 2.8. The Peclat number "significance" is earlier given in terms of "Pe>>1" (Line255). Please clarify what range of experimental values is required for the argument to hold.

Line 404 needs details of the GFP-EB1 and fluorescent tubulin used in this experiment.

The tubulin depletion measurements detect a 4% reduction in tubulin concentration in the interior versus the exterior, and the same for eGFP-EB1 (Fig.4B). This observation provides important support for the depletion proposal. But the experiments apparently lack a control for potential reduction of fluorescence excitation intensity with depth in these deep specimens (equivalent to the inner filter effect in spectroscopy). Is there a component whose apparent concentration (fluorescence emission intensity) does not decrease by 4% in the interior of the aster?

There is no direct discussion of the relative lifetime of MTs in the interior compared to the exterior of the aster. Catastrophe rates and growth rates are essentially invariant, I think this implies that MT lifetimes are essentially the same in the interior versus the exterior? Please confirm and estimate the lifetime. This could exclude a maturation process whereby one set of MAPs got replaced by another over time?

Significance

This paper is significant as it is the first observation of spatial variation in MT shrinkage rates in an aster. It proposes the broad shape of an underlying mechanism (depletion of stabilising MAPS in the aster interior) and presents sound quantitative arguments, but the experiments do not directly test this mechanism. Aster formation in Xenopus egg extracts is widely used as a model system, and if indeed the spatial variation turns out to be due to spatial depletion of components then this will become a landmark paper. The paper may promote wider use of this method of automated analysis and encourage study of shrinkage rate mechanisms in other systems.

REFEREES CROSS COMMENTING

In my opinion the comments of reviewer #1 are fair and reasonable and overlap with and complement my own. In my opinion there is zero conflict requiring adjustment.

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

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Ishihara et al. investigate and compare microtubule polymerization/depolymerization dynamics inside vs. at the periphery of microtubule asters in a cell-free Xenopus egg extract system. By tracking EB comets, which localize to growing microtubule ends, they find that the microtubule growth rates and EB comet lifetimes (interpreted as an indicator of microtubule catastrophe rates) are similar between the two spatially-distinct microtubule populations. However, using a tubulin-intensity-difference image analysis, the authors are also able to measure local microtubule depolymerization rates, and they find a significant difference in depolymerization rates of the two populations. Specifically, the authors report that the microtubule depolymerization rates measured within asters are faster than those measured at the periphery.

Specific comments:

Figure 2. In the text, the authors report: "The depolymerization rate was 36.3 {plus minus} 7.9 μm/min (mean, std) in the aster interior, compared to 29.2 {plus minus} 8.9 μm/min (mean, std) at the aster periphery." This difference is certainly not two-fold (as stated in the abstract). It would also be useful to mark the mean rates on the graph in 2B.

The bimodal shape of the depolymerization rate distributions in 2B is very interesting. This definitely warrants further investigation. At the minimum, the depolymerization rates should be determined at 50 um- intervals, as done for other parameters in Figure 1. Could it be that there are two coexisting populations of microtubules at the same location? Or is there a clear spatial compartmentalization of the two that is not obvious here because of the too large of a distance interval used for the measurements. This is a very important distinction for the claims of the paper.

The authors make a point here that the distribution of measured polymerization rates is fairly narrow. This appears to be in contrast with Figure 1B, where polymerization rates take on a wide range of values. How do the two distributions of polymerization rates obtained by these two methods compare?

Figure 3. The laser ablation figure and movies are beautiful, but don't seem to add support to the story. Importantly, the authors do not confirm any spatial variability in depolymerization rate with these experiment. As a matter of fact, although the laser ablation experiments are only performed in the aster interior, the measured depolymerization rates appear to be just as consistent with the periphery rates in Figure 2. as they are with the interior rates in Figure 2. (They span quite a large range of values with the average right in the middle between what was measured for the two areas in Figure 2).

Although the authors report they don't see any correlation between the distance and depolymerization rate, they should still plot the rate as a function of initial cut positions (Figures 3D, 3E).

From the single decaying inward wave the authors conclude that microtubules depolymerize fully to their minus ends which are distributed throughout the aster. Can the possibility that depolymerization is stopped by microtubule lattice defects/islands be excluded by these observations?

What are the effects of the local increase in tubulin concentration due to the subunit release by depolymerization? What about the release of other lattice-binding MAPs (stabilizers)?

Figure 4. Is the local depletion of tubulin/EB1 thought to be only within the narrow annulus at ~100 um distance, or is it not measurable on the inside due to the polymer signal? Can the two be separated? Such a sharp transition within a discrete annular region doesn't speak to the relative effects on the inside vs. the outside of the aster?!

More importantly, the local depletion of either tubulin or EB1 is not a good representation of a depletion of a MAP component that associates with the microtubule lattice. Both tubulin and EB1 bind preferably to microtubule ends, not lattice. Thus showing a profile of slight local tubulin and/or EB depletion does not seem to be relevant for the proposed model. Rather, overall microtubule polymer mass/density as a function of distance may be more relevant?

Figure 5. The toy model is intuitive and clear, but not sufficient without any experimental investigation. An attempt to quantify the actual distributions of at least one or a few selected proposed MAPs is needed. Is the depletion strongest where microtubule density is highest? What is the ratio of a MAP intensity to microtubule polymer density as a function of distance? How does that relate to local depolymerization rates? What are other testable model predictions that can show support for the proposed mechanism?

Also, the table is insufficiently described. Are any or all of these MAPs known to be specific regulators of microtubule depolymerization rates, but not other dynamics parameters?

Minor comments:

Figure 1. typo in the figure legend: "interior (distance>300 μm) vs. periphery (50 μm<distance<280 μm)" There appears to be a clear dip in EB1 density at 100 um (Figure 1C). What could be the cause of that?

Figure 2. Note that the distances used in Figure 2. to define 'interior' and 'periphery' are completely different than those in Figure 1. (Interior in Figure 1 is defined to be between 50 and 280 um from the MTOC, and exterior larger than 300 um. However, in Figure 2. interior is defined as less than 100 um, and exterior as larger than 200 um.) Given that the asters are actively growing, it would be good to clearly explain how these intervals were defined in each case.

In the periphery movie, there are several notable examples of apparent minus-end depolymerization and treadmilling. The authors state these are very rare - perhaps a quantification would be useful here?

Significance

The observation of distinct depolymerization rates within vs. at the periphery of microtubule asters is novel and interesting. However, the manuscript in its current form is rather preliminary. The observation can be significantly strengthened by additional experiments/analysis that would characterize the effect in more detail. Even more importantly, the authors propose a highly speculative (although compelling) mechanism, but make no attempt to test it in any way. This is a major deficiency of the current manuscript that should be addressed prior to publication.

REFEREES CROSS COMMENTING

I agree with Reviewer #2 that our comments are both overlapping and complementary. I also find Reviewer #2's comments fair and reasonable and see no need for further adjustments.

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Reply to the reviewers

We would like to express our appreciation for both the Editors’ and Reviewers’ efforts as essential contributions to the peer review process. We highly value the Reviewers’ constructive critique of our manuscript#RC-2020_00434R entitled “A drug repurposing screen identifies hepatitis C antivirals as inhibitors of the SARS-CoV2 main protease.__” __

We appreciate the Reviewers’ thoughtful consideration of our work and feel their critiques and recommendations have significantly improved our manuscript. Taken together, we believe the additional data, clarification of data presentation, and revised discussion address the heart of the Reviewers’ previous concerns. Thus we feel the work is ready for reconsideration and will be an impactful addition to the literature appropriate for publication. Below we provide a breakdown and a point by point response to previous review critiques.

Thank you for your attention. We look forward to your response.

Best Wishes,

Brian Kraemer, PhD ▪ Associate Director for Research Geriatric Research Education and Clinical Center ▪ Veterans Affairs Puget Sound Health Care System ▪ Research Professor ▪ Departments of Medicine, Psychiatry and Behavioral Sciences, and Pathology ▪ University of Washington ▪ 1660 South Columbian Way ▪ Seattle, WA 98108 ▪ Phone 206-277-1071 ▪ www.kraemerlab.uw.edu

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

In this manuscript, Baker et al. report the screening of a collection of ~6,070 drugs for their inhibitory activity against the enzymatic activity of the SARS-SoV-2 Mpro protein in vitro using two peptide substrates. 50 compounds with activity against Mpro were identified and tested for their dose-dependent effect in the same assay. Several hits were identified, among which are approved drugs that target the HCV protease.

Indeed, there is an urgent need for effective drugs for SARS-CoV-2 infection, and high throughput screenings can discover novel candidates. However, the novelty of this work is quite limited, as former screens have been published with the same target using the same substrates. Moreover, as discussed below the translational impact of the hits discussed is also quite limited, particularly in the absence of antiviral data. Lastly, there are several overstatements in the write up and it will require major editing.

**Major comments:**

1. Were there any positive controls previously shown to potently inhibit the SARS-CoV-2 Mpro included in the screen (e.g. ebselen)? How did these perform in this assay? When first designing our protease assay, we did use ebselen as the initial control. Ebselen showed low potency in all our in our assays and was not considered as a positive control subsequently. It should be noted that Ebselen failed to work against multiple substrates. It is possible that our buffer conditions prevented Ebselen activity. See data plotted below. After identifying boceprevir as a potent inhibitor, it was used in all subsequent assays as a positive control.

It will be helpful if the authors would provide info re the 50 hits from prior screens conducted with this library of compounds - how promiscuous are they across screens? How toxic in cell based assays?

We have updated the table to provide additional useful information as well as a footnote explaining statuses. The compounds in the Broad repurposing library are generally non-toxic and information about them can be found here: https://clue.io/repurposing

The translational potential of the findings appears to be limited. The calculated IC50s for these drugs in the Mpro assay are very high (10-1000 fold higher) relative to their IC50 in an enzymatic assay involving the HCV protease (Boceprevir: IC50 = 0.95 μM vs. 0.084 μM in HCV), Ciluprevir (IC50 = 20.77 μM vs. 0.0087 in HCV), Telaprevir (IC50 = 15.25 μM vs.0.050 μM in HCV) (https://aac.asm.org/content/aac/57/12/6236.full.pdf ). In the absence of antiviral data, the main statement of the manuscript that "the work presented here supports the rapid evaluation of previous HCV NS3/4A inhibitors for repurposing as a COVID-19 therapy." is thus an overstatement. Even is there is some activity, since likely to be limited, as with the HIV protease inhibitors, its chances to elicit a meaningful clinical effect is low. Moreover, when used in monotherapy, some of these protease inhibitors have a very low genetic barrier to resistance.

We have reworked the discussion to incorporate these concerns and limitations of our results.

There are additional inaccurate or overstatements - e.g. line 61 "Probably the most successful approved antivirals are protease inhibitors such as atazanavir for HIV-1 and simeprevir for hepatitis C. [reviewed in 10 and 11]."

We have reworded this statement: (Page 4, Lines 61-62)

“There is precedence for targeting the protease, as this approach has been successful in treating both HIV-1 and hepatitis C (10,11).”

The manuscript requires editing - e.g. structure of sentences, commas, spacing (including in the abstract) etc.

The manuscript has been re-proofed throughout (see tracked changes version of manuscript)

What is the take home message? The statement "Taken together this work suggests previous large-scale commercial drug development initiatives targeting hepatitis C NS3/4A viral protease should be revisited because some previous lead compounds may be more potent against SARS-CoV-2 Mpro than Boceprevir and suitable for rapid repurposing." is unclear.

The take home message of the manuscript is that HCV-targeting protease inhibitors have potential in blocking the SARS-Cov2 protease and a more thorough analysis of the space is needed. As the reviewer pointed out, the identified hits boceprevir and narlaprevir are less potent when targeting the SARS-Cov2 protease as compared to the HCV protease. However, we believe this work does show the potential for screening HCV-targeting protease inhibitors that may not have made it to the clinic. For instance, Boceprevir or Narlaprevir analogs may be even more potent against Mrpo. Further, we believe that these compounds would benefit from further optimization through medicinal chemistry.

We have expanded the discussion to incorporate issues brought up here and in point 3.

Reviewer #1 (Significance (Required)):

Limited. As discussed above

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

SARS-CoV-2 pandemic causing serious health crisis globally. There are no specific medicine or vaccines to contain this virus currently. To address this issue, the authors developed one efficient fluorescent Mpro assay system and screened ~6070 previous used drugs in this article. Several compounds with activity against SARS-CoV-2 Mpro in vitro were founded. Most hits are hepatitis C NS3/4A protease inhibitors with fair IC50 value. Besides, the authors found that most identified compounds in in silico screen lack activity against Mpro in kinetic protease assays.

These research results are well proved and reproducible. But there are two minor questions I present below:

1. In your Mpro assay optimization process you said substrate MCA-AVLQSGFR-K(Dnp)- K-NH2 had drastically lower rates of Mpro catalyzed hydrolysis and were not considered further in your assay development. And in your Fig.1 I saw extremely low RFU changes. But several nice inhibitors were screened using this substrate that was reported in April. Can you explain this result? The substrates used in our assay appear to be much more efficiently cleaved at least with our buffer conditions and Mpro concentrations tested. Variables including recombinant Mpro purity and activity, differences in assay buffer, reader sensitivity may all play a role, but our best guess is that the substrate identified by Marcin Drag’s group (https://doi.org/10.1101/2020.04.29.068890), is more readily cleaved by Mpro. Although screening with other reported substrates is feasible given previous results, we believe the Ac-Abu-Tle-Leu-Gln-AFC to be superior for use in high throughput screening because of its superior cleavage kinetics yielding an improved signal to background ratio for HTS.

To exclude inhibitors possibly acting as aggregators, a detergent-based control should do at the same time when you do IC50 value measurement.

Compound aggregation is a concern, and our assays were all run with detergent in the buffer. Our buffer composition was 20mM Tris pH 7.8, 150mM NaCl, 1mM EDTA, 1mM DTT, 0.05% Triton X-100.

Reviewer #2 (Significance (Required)):

Nice work but the significance of this article is losing now. Most screened hits are reported in the last serval months. Some inhibitor complex structures have been published or released on Protein Data Bank. The novelty is missing. I suggest the authors add more results and resubmit it again.

**Referees Cross-commenting**

I agree with the other two reviewers' comments. The significance of this work is losing but still has something interest. I think it can be published in the lower-impact journal if they complete our suggestions

We concur with both reviewers that demonstration of antiviral activity would strengthen the impact of the manuscript. However, this work remains outside of the scope of feasibility at our institution. We believe that our screen and hit identification can stand on their own until further translational work can be completed.

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

In this report, Baker et al. show that four inhibitors of hepatitis C virus (HCV) NS3/4 protease (ciluprevir, boceprevir, narlaprevir and telaprevir) are also effective inhibitors of the SARS-CoV-2 main protease (Mpro) in enzymatic assays, with lower IC50 values for narlaprevir and boceprevir (around 1 µM in their assay conditions). HCV NS3/4 inhibitors were identified after screening a library of >6,000 compounds of the Broad Institute, including approved drugs. Screening was done with fluorometric proteolytic assays.

Experiments have been apparently well-done and results are sound. The manuscript needs editing.

Reviewer #3 (Significance (Required)):

Experiments have been apparently well-done and results are sound. However, this is a limited study since there are no data obtained in cell culture and a comparison of IC50 values of the selected drugs against HCV and SARS-CoV-2 proteases is missing. It is difficult to infer whether the drugs would be equally effective against SARS-CoV-2 than against HCV, and otherwise, how much should the doses increase in order to have a therapeutic effect.

The manuscript needs editing (see below) and the Discussion is poor. The results reported by authors are not new, and a discussion of the effects of HCV inhibitors on SARS-CoV-2 replication, based on previous publications is necessary to provide the appropriate context for the study.

Here are some references on Covid-19 and HCV inhibitors, that in my opinion should be considered for discussion and proper citation. As correctly pointed out by Baker and co- workers, docking studies should be considered with caution, though.

We appreciate the feedback and have now reworked and expanded the discussion to incorporate reviewer #1 and #3 comments and suggestions.

1: Ghahremanpour MM, Tirado-Rives J, Deshmukh M, Ippolito JA, Zhang CH, de Vaca IC, Liosi ME, Anderson KS, Jorgensen WL. Identification of 14 Known Drugs as Inhibitors of the Main Protease of SARS-CoV-2. bioRxiv [Preprint]. 2020 Aug 28:2020.08.28.271957. doi: 10.1101/2020.08.28.271957. PMID: 32869018; PMCID: PMC7457600.

2: Sacco MD, Ma C, Lagarias P, Gao A, Townsend JA, Meng X, Dube P, Zhang X, Hu Y, Kitamura N, Hurst B, Tarbet B, Marty MT, Kolocouris A, Xiang Y, Chen Y, Wang J. Structure and inhibition of the SARS-CoV-2 main protease reveals strategy for developing dual inhibitors against Mpro and cathepsin L. bioRxiv [Preprint]. 2020 Jul 27:2020.07.27.223727. doi: 10.1101/2020.07.27.223727. PMID: 32766590; PMCID: PMC7402059.

3: Ma C, Sacco MD, Hurst B, Townsend JA, Hu Y, Szeto T, Zhang X, Tarbet B, Marty MT, Chen Y, Wang J. Boceprevir, GC-376, and calpain inhibitors II, XII inhibit SARS-CoV-2viral replication by targeting the viral main protease. Cell Res. 2020 Aug;30(8):678-692. doi: 10.1038/s41422-020-0356-z. Epub 2020 Jun 15. PMID: 32541865; PMCID: PMC7294525.

4: Ke YY, Peng TT, Yeh TK, Huang WZ, Chang SE, Wu SH, Hung HC, Hsu TA, Lee SJ, Song JS, Lin WH, Chiang TJ, Lin JH, Sytwu HK, Chen CT. Artificial intelligence approach fighting COVID-19 with repurposing drugs. Biomed J. 2020 May 15:S2319- 4170(20)30049-4. doi: 10.1016/j.bj.2020.05.001. Epub ahead of print. PMID: 32426387; PMCID: PMC7227517.

5: Elzupir AO. Inhibition of SARS-CoV-2 main protease 3CLpro by means of α-ketoamide and pyridone-containing pharmaceuticals using in silico molecular docking. J Mol Struct. 2020 Dec 15;1222:128878. doi: 10.1016/j.molstruc.2020.128878. Epub 2020 Jul 10.

PMID: 32834113; PMCID: PMC7347502.

Additional computational studies:

1: Hosseini FS, Amanlou M. Anti-HCV and anti-malaria agent, potential candidates to repurpose for coronavirus infection: Virtual screening, molecular docking, and molecular dynamics simulation study. Life Sci. 2020 Aug 8;258:118205. doi:10.1016/j.lfs.2020.118205. Epub ahead of print. PMID: 32777300; PMCID:PMC7413873.

2: Hakmi M, Bouricha EM, Kandoussi I, Harti JE, Ibrahimi A. Repurposing of known anti- virals as potential inhibitors for SARS-CoV-2 main protease using molecular docking analysis. Bioinformation. 2020 Apr 30;16(4):301-306. doi:10.6026/97320630016301.

PMID: 32773989; PMCID: PMC7392094.

3: Chtita S, Belhassan A, Aouidate A, Belaidi S, Bouachrine M, Lakhlifi T. Discovery of Potent SARS-CoV-2 Inhibitors from Approved Antiviral Drugs via Docking Screening. Comb Chem High Throughput Screen. 2020 Jul 30. doi:10.2174/1386207323999200730205447. Epub ahead of print. PMID: 32748740.

4: Alamri MA, Tahir Ul Qamar M, Mirza MU, Bhadane R, Alqahtani SM, Muneer I, Froeyen M, Salo-Ahen OMH. Pharmacoinformatics and molecular dynamics simulation studies reveal potential covalent and FDA-approved inhibitors of SARS-CoV-2 main protease 3CLpro. J Biomol Struct Dyn. 2020 Jun 24:1-13. doi:10.1080/07391102.2020.1782768. Epub ahead of print. PMID: 32579061; PMCID:PMC7332866.

5: Bafna K, Krug RM, Montelione GT. Structural Similarity of SARS-CoV2 Mpro and HCV NS3/4A Proteases Suggests New Approaches for Identifying Existing Drugs Useful as COVID-19 Therapeutics. ChemRxiv [Preprint]. 2020 Apr 21. doi: 10.26434/chemrxiv.12153615. PMID: 32511291; PMCID: PMC7263768.

6: Eleftheriou P, Amanatidou D, Petrou A, Geronikaki A. In Silico Evaluation of the Effectivity of Approved Protease Inhibitors against the Main Protease of the Novel SARS- CoV-2 Virus. Molecules. 2020 May 29;25(11):2529. doi:10.3390/molecules25112529.

PMID: 32485894; PMCID: PMC7321236.

7: Wang J. Fast Identification of Possible Drug Treatment of Coronavirus Disease-19 (COVID-19) through Computational Drug Repurposing Study. J Chem Inf Model. 2020 Jun 22;60(6):3277-3286. doi: 10.1021/acs.jcim.0c00179. Epub 2020 May 4. PMID: 32315171; PMCID: PMC7197972.

8: Chen YW, Yiu CB, Wong KY. Prediction of the SARS-CoV-2 (2019-nCoV) 3C-like protease (3CL pro) structure: virtual screening reveals velpatasvir, ledipasvir, and other drug repurposing candidates. F1000Res. 2020 Feb 21;9:129. doi: 10.12688/f1000research.22457.2. PMID: 32194944; PMCID: PMC7062204.

Minor comments:

We appreciate the time that the reviewer has taken to address grammatical changes and have addressed each throughout the manuscript with tracked changes.

p.2, line 26: > appears as an attractive

Manuscript edited

p.2, line 27: > we show that the existing

Manuscript edited

p.2, line 33: > separate numbers and units, eg. 1.10 µM (this is a persisting error that should be corrected throughout the whole ms)

Manuscript edited

p.4, line 44: SARS virus should be referred as to SARS-CoV-1 throughout the whole manuscript. MERS-CoV is the name of the virus causing MERS

Manuscript edited

p.4, lines 61-62: > the selection of the specific compounds seems to be arbitrary... why atazanavir and not darunavir or other? The sentence should be rewritten.

Rewritten as: “There is precedence for targeting the protease, as this approach has been successful in treating both HIV-1 and hepatitis C.”

p.6, line 100: Citing Fig. 2B before completing the description of Fig. 1 is distracting. Authors should think of a better way to describe their results.

This was a mistake and should have cited Fig 1B. Thank you for catching this.

p.7, line 116: It is not clear what "10m-20,810" means

This has been clarified to state: “ΔRFU at 10 minutes = 20,810 relative fluorescence units”

p.7, lines 125-126: These sentences belong to an introduction, not appropriate in results section.

We have removed these sentences.

Figure 2. Part A is not necessary in results (ok for introduction). Black and purple dots in part B is not a good choice since they are difficult to distinguish, maybe orange and black is better.

We have removed panel A, expanded the size of panel B and changed the color.

Table 1: Status should be explained in a footnote (i.e the distinction between launched, P2/P3, phase 2, preclinical is not clear).

The one compound indicated in P2/P3 development is now Phase 3 and the table has been updated. We have added a footnote:

*Launched = compound approved for humans, though may only be approved for veterinary use in some countries

Discussion. I think that subheadings are not necessary.

Subheadings have been removed from the discussion.

**Referees cross-commenting** I agree with reviewer no. 1 on the limited interest of the study. However, it could be published in a specialized lower-impact journal after addressing issues raised by reviewers 2 and 3 (likely to be completed in less than a month)

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

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---

Referee #3

Evidence, reproducibility and clarity

In this report, Baker et al. show that four inhibitors of hepatitis C virus (HCV) NS3/4 protease (ciluprevir, boceprevir, narlaprevir and telaprevir) are also effective inhibitors of the SARS-CoV-2 main protease (Mpro) in enzymatic assays, with lower IC50 values for narlaprevir and boceprevir (around 1 µM in their assay conditions). HCV NS3/4 inhibitors were identified after screening a library of >6,000 compounds of the Broad Institute, including approved drugs. Screening was done with fluorometric proteolytic assays.

Experiments have been apparently well-done and results are sound. The manuscript needs editing.

Significance

Experiments have been apparently well-done and results are sound. However, this is a limited study since there are no data obtained in cell culture and a comparison of IC50 values of the selected drugs against HCV and SARS-CoV-2 proteases is missing. It is difficult to infer whether the drugs would be equally effective against SARS-CoV-2 than against HCV, and otherwise, how much should the doses increase in order to have a therapeutic effect. The manuscript needs editing (see below) and the Discussion is poor. The results reported by authors are not new, and a discussion of the effects of HCV inhibitors on SARS-CoV-2 replication, based on previous publications is necessary to provide the appropriate context for the study. Here are some references on Covid-19 and HCV inhibitors, that in my opinion should be considered for discussion and proper citation. As correctly pointed out by Baker and co-workers, docking studies should be considered with caution, though.

1: Ghahremanpour MM, Tirado-Rives J, Deshmukh M, Ippolito JA, Zhang CH, de Vaca IC, Liosi ME, Anderson KS, Jorgensen WL. Identification of 14 Known Drugs as Inhibitors of the Main Protease of SARS-CoV-2. bioRxiv [Preprint]. 2020 Aug 28:2020.08.28.271957. doi: 10.1101/2020.08.28.271957. PMID: 32869018; PMCID: PMC7457600.

2: Sacco MD, Ma C, Lagarias P, Gao A, Townsend JA, Meng X, Dube P, Zhang X, Hu Y, Kitamura N, Hurst B, Tarbet B, Marty MT, Kolocouris A, Xiang Y, Chen Y, Wang J. Structure and inhibition of the SARS-CoV-2 main protease reveals strategy for developing dual inhibitors against M^pro and cathepsin L. bioRxiv [Preprint]. 2020 Jul 27:2020.07.27.223727. doi: 10.1101/2020.07.27.223727. PMID: 32766590; PMCID: PMC7402059.

3: Ma C, Sacco MD, Hurst B, Townsend JA, Hu Y, Szeto T, Zhang X, Tarbet B, Marty MT, Chen Y, Wang J. Boceprevir, GC-376, and calpain inhibitors II, XII inhibit SARS-CoV-2 viral replication by targeting the viral main protease. Cell Res. 2020 Aug;30(8):678-692. doi: 10.1038/s41422-020-0356-z. Epub 2020 Jun 15. PMID: 32541865; PMCID: PMC7294525.

4: Ke YY, Peng TT, Yeh TK, Huang WZ, Chang SE, Wu SH, Hung HC, Hsu TA, Lee SJ, Song JS, Lin WH, Chiang TJ, Lin JH, Sytwu HK, Chen CT. Artificial intelligence approach fighting COVID-19 with repurposing drugs. Biomed J. 2020 May 15:S2319-4170(20)30049-4. doi: 10.1016/j.bj.2020.05.001. Epub ahead of print. PMID: 32426387; PMCID: PMC7227517.

5: Elzupir AO. Inhibition of SARS-CoV-2 main protease 3CLpro by means of α-ketoamide and pyridone-containing pharmaceuticals using in silico molecular docking. J Mol Struct. 2020 Dec 15;1222:128878. doi: 10.1016/j.molstruc.2020.128878. Epub 2020 Jul 10. PMID: 32834113; PMCID: PMC7347502.

Additional computational studies:

1: Hosseini FS, Amanlou M. Anti-HCV and anti-malaria agent, potential candidates to repurpose for coronavirus infection: Virtual screening, molecular docking, and molecular dynamics simulation study. Life Sci. 2020 Aug 8;258:118205. doi:10.1016/j.lfs.2020.118205. Epub ahead of print. PMID: 32777300; PMCID:PMC7413873.

2: Hakmi M, Bouricha EM, Kandoussi I, Harti JE, Ibrahimi A. Repurposing of known anti-virals as potential inhibitors for SARS-CoV-2 main protease using molecular docking analysis. Bioinformation. 2020 Apr 30;16(4):301-306. doi:10.6026/97320630016301. PMID: 32773989; PMCID: PMC7392094.

3: Chtita S, Belhassan A, Aouidate A, Belaidi S, Bouachrine M, Lakhlifi T. Discovery of Potent SARS-CoV-2 Inhibitors from Approved Antiviral Drugs via Docking Screening. Comb Chem High Throughput Screen. 2020 Jul 30. doi:10.2174/1386207323999200730205447. Epub ahead of print. PMID: 32748740.

4: Alamri MA, Tahir Ul Qamar M, Mirza MU, Bhadane R, Alqahtani SM, Muneer I, Froeyen M, Salo-Ahen OMH. Pharmacoinformatics and molecular dynamics simulation studies reveal potential covalent and FDA-approved inhibitors of SARS-CoV-2 main protease 3CL^pro. J Biomol Struct Dyn. 2020 Jun 24:1-13. doi:10.1080/07391102.2020.1782768. Epub ahead of print. PMID: 32579061; PMCID:PMC7332866.

5: Bafna K, Krug RM, Montelione GT. Structural Similarity of SARS-CoV2 M^pro and HCV NS3/4A Proteases Suggests New Approaches for Identifying Existing Drugs Useful as COVID-19 Therapeutics. ChemRxiv [Preprint]. 2020 Apr 21. doi: 10.26434/chemrxiv.12153615. PMID: 32511291; PMCID: PMC7263768.

6: Eleftheriou P, Amanatidou D, Petrou A, Geronikaki A. In Silico Evaluation of the Effectivity of Approved Protease Inhibitors against the Main Protease of the Novel SARS-CoV-2 Virus. Molecules. 2020 May 29;25(11):2529. doi:10.3390/molecules25112529. PMID: 32485894; PMCID: PMC7321236.

7: Wang J. Fast Identification of Possible Drug Treatment of Coronavirus Disease-19 (COVID-19) through Computational Drug Repurposing Study. J Chem Inf Model. 2020 Jun 22;60(6):3277-3286. doi: 10.1021/acs.jcim.0c00179. Epub 2020 May 4. PMID: 32315171; PMCID: PMC7197972.

8: Chen YW, Yiu CB, Wong KY. Prediction of the SARS-CoV-2 (2019-nCoV) 3C-like protease (3CL ^pro) structure: virtual screening reveals velpatasvir, ledipasvir, and other drug repurposing candidates. F1000Res. 2020 Feb 21;9:129. doi: 10.12688/f1000research.22457.2. PMID: 32194944; PMCID: PMC7062204.

Minor comments:

p.2, line 26: > appears as an attractive

p.2, line 27: > we show that the existing

p.2, line 33: > separate numbers and units, eg. 1.10 µM (this is a persisting error that should be corrected throughout the whole ms)

p.4, line 44: SARS virus should be referred as to SARS-CoV-1 throughout the whole manuscript. MERS-CoV is the name of the virus causing MERS

p.4, lines 61-62: > the selection of the specific compounds seems to be arbitrary... why atazanavir and not darunavir or other? The sentence should be rewritten.

p.6, line 100: Citing Fig. 2B before completing the description of Fig. 1 is distracting. Authors should think of a better way to describe their results.

p.7, line 116: It is not clear what "10m-20,810" means

p.7, lines 125-126: These sentences belong to an introduction, not appropriate in results section.

Figure 2. Part A is not necessary in results (ok for introduction). Black and purple dots in part B is not a good choice since they are difficult to distinguish, maybe orange and black is better.

Table 1: Status should be explained in a footnote (i.e the distinction between launched, P2/P3, phase 2, preclinical is not clear).

Discussion. I think that subheadings are not necessary.

Referees cross-commenting

I agree with reviewer no. 1 on the limited interest of the study. However, it could be published in a specialized lower-impact journal after addressing issues raised by reviewers 2 and 3 (likely to be completed in less than a month)

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---

Referee #2

Evidence, reproducibility and clarity

SARS-CoV-2 pandemic causing serious health crisis globally. There are no specific medicine or vaccines to contain this virus currently. To address this issue, the authors developed one efficient fluorescent Mpro assay system and screened ~6070 previous used drugs in this article. Several compounds with activity against SARS-CoV-2 Mpro in vitro were founded. Most hits are hepatitis C NS3/4A protease inhibitors with fair IC50 value. Besides, the authors found that most identified compounds in in silico screen lack activity against Mpro in kinetic protease assays.

These research results are well proved and reproducible. But there are two minor questions I present below:

1.In your Mpro assay optimization process you said substrate MCA-AVLQSGFR-K(Dnp)-K-NH2 had drastically lower rates of Mpro catalyzed hydrolysis and were not considered further in your assay development. And in your Fig.1 I saw extremely low RFU changes. But several nice inhibitors were screened using this substrate that was reported in April. Can you explain this result?

2.To exclude inhibitors possibly acting as aggregators, a detergent-based control should do at the same time when you do IC50 value measurement.

Significance

Nice work but the significance of this article is losing now. Most screened hits are reported in the last serval months. Some inhibitor complex structures have been published or released on Protein Data Bank. The novelty is missing. I suggest the authors add more results and resubmit it again.

Referees Cross-commenting

I agree with the other two reviewers' comments. The significance of this work is losing but still has something interest. I think it can be published in the lower-impact journal if they complete our suggestions

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

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this manuscript, Baker et al. report the screening of a collection of ~6,070 drugs for their inhibitory activity against the enzymatic activity of the SARS-SoV-2 Mpro protein in vitro using two peptide substrates. 50 compounds with activity against Mpro were identified and tested for their dose-dependent effect in the same assay. Several hits were identified, among which are approved drugs that target the HCV protease.<br> Indeed, there is an urgent need for effective drugs for SARS-CoV-2 infection, and high throughput screenings can discover novel candidates. However, the novelty of this work is quite limited, as former screens have been published with the same target using the same substrates. Moreover, as discussed below the translational impact of the hits discussed is also quite limited, particularly in the absence of antiviral data. Lastly, there are several overstatements in the write up and it will require major editing.

Major comments:

1.Were there any positive controls previously shown to potently inhibit the SARS-CoV-2 Mpro included in the screen (e.g. ebselen)? How did these perform in this assay?

2.It will be helpful if the authors would provide info re the 50 hits from prior screens conducted with this library of compounds - how promiscuous are they across screens? How toxic in cell based assays?

3.The translational potential of the findings appears to be limited. The calculated IC50s for these drugs in the Mpro assay are very high (10-1000 fold higher) relative to their IC50 in an enzymatic assay involving the HCV proteast (Boceprevir: IC50 = 0.95 μM vs. 0.084 μM in HCV), Ciluprevir (IC50 = 20.77 μM vs. 0.0087 in HCV), Telaprevir (IC50 = 15.25 μM vs. 0.050 μM in HCV) (https://aac.asm.org/content/aac/57/12/6236.full.pdf ). In the absence of antiviral data, the main statement of the manuscript that "the work presented here supports the rapid evaluation of previous HCV NS3/4A inhibitors for repurposing as a COVID-19 therapy." is thus an overstatement. Even is there is some activity, since likely to be limited, as with the HIV protease inhibitors, its chances to elicit a meaningful clinical effect is low. Moreover, when used in monotherapy, some of these protease inhibitors have a very low genetic barrier to resistance.

4.There are additional inaccurate or overstatements - e.g. line 61 "Probably the most successful approved antivirals are protease inhibitors such as atazanavir for HIV-1 and simeprevir for hepatitis C. [reviewed in 10 and 11]."

5.The manuscript requires editing - e.g. structure of sentences, commas, spacing (including in the abstract) etc.

6.What is the take home message? The statement "Taken together this work suggests previous large-scale commercial drug development initiatives targeting hepatitis C NS3/4A viral protease should be revisited because some previous lead compounds may be more potent against SARS-CoV-2 Mpro than Boceprevir and suitable for rapid repurposing." is unclear.

Significance

Limited. As discussed above

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Reply to the reviewers

Response to Reviewers and Revision Plan

We thank all three reviewers for their time and their comments on our manuscript.

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

Here Ryan et al. have used localization analysis following induced rapid relocalization of endogenous proteins to investigate the composition and recruitment hierarchy of a clathrin-TACC3-based spindle complex that is important for microtubule organization and stability.

The authors generate different HeLa cell lines, each with one of four complex members (TACC3, CLTA, chTOG and GTSE1) endogenously tagged with FKBP-GFP via Cas9-mediated editing. This tag allows rapid recruitment to the mitochondria upon rapamycin addition ("knocksideways"). They ultimately quantify each of the 4 components' localization to the spindle following knocksideways of each component using fluorescently-tagged transfected constructs. The authors' interpretation of the results of this analysis are summarized in the last model figure, in which a core MT-binding complex of clathrin and TACC3 recruit the ancillary components GTSE1 and chTOG. In addition, the authors investigate the contribution of individual clathrin-binding LIDL motifs in GTSE1 to the recruitment of clathrin and GTSE1 to spindles. Their findings here largely agree with and confirm a recent report regarding the contribution of these motifs to GTSE1 recruitment to the spindle. They further analyzed GTSE1 fragments for interphase and mitotic microtubule localization, and identified a second region of GTSE1 required (but not sufficient) for spindle localization. Finally, the authors report that PIK3C2A is not part of this complex, contradicting (correcting) a previously published study.

**Major comments:**

1.The chTOG-FKBP-GFP cell line the authors generate has only a small fraction of chTOG tagged, and thus should not be used for any conclusions about protein localization dependency on chTOG. Because they were unable to construct a HeLa cell line with all copies tagged, the authors expect that the homozygous knock-in of chTOG-FKBP-GFP is lethal, and thus their experience is appropriate to report. However, the authors should not use this cell line alone to make statements about chTOG dependency. They would have to use similar localization analysis, but after another method to disrupt chTOG (as a second-best approach), such as RNAi. In fact, they have reported this in a previous publication (Booth et al 2011). However, the result was different. There, loss of chTOG resulted in reduced clathrin on spindles, suggesting it may stabilize or help recruit the complex. Alternatively, they could remove their chTOG data, but this would compromise the "comprehensive" nature of the work.

The referee is correct. The point here is to show the results we had using this approach for all four proteins under study. For this reason, we do not want to remove this data and prefer to show our results “warts-and-all”. We feel that the shortcomings of our approach are honestly presented and discussed in the manuscript. While only a fraction of chTOG was tagged, we should expect some co-removal after its induced mislocalization. Since we saw no change, we concluded that chTOG is auxiliary.

The “second best” approach suggested (RNAi of chTOG) is problematic for two reasons. First, chTOG RNAi results in gross changes to spindle structure (multipolar spindles) and it is difficult to pick apart differences in protein partner localization that result from loss of chTOG from those resulting from changes in spindle structure. Second, the paper is about induced mislocalization as a method for determining protein complexes once a normal spindle has formed. So, removing chTOG prior to mitosis is not comparable. If we get the same or different result, does it confirm or conflict with the data we have? Nonetheless, given the discrepancy with our earlier work, we should investigate this further.

To address this concern, we will stain endogenous clathrin, TACC3 and GTSE1 following chTOG RNAi and measure their relative levels at the spindle.

Making the chTOG-FKBP-GFP cell line was difficult. As described in the paper, we only recovered heterozygous clones despite repeated attempts. Since submission, we have been made aware of a HCT116 chTOG-FKBP-GFP cell line that is reported to be homozygously tagged (Cherry et al. 2019 doi: 10.1002/glia.23628).

A note about this cell line has been added to the paper (Results section, final sentence of 1st paragraph).

2.The authors initially analyze complex member localization after knocksideways experiments by antibody staining, which has the advantage of analyzing endogenous proteins (versus the later transfected fluorescent constructs). Setting aside potential artefacts from fixation, this would seem to be a better method for controlled analysis to take advantage of their setup (short of generating stable cell lines with second proteins endogenously tagged in a second color - a huge undertaking). The authors conclude that antibody specificity problems confounded their analysis and explained unusual results. However, I think is worth investing a little more effort to sort this out, rather than bringing doubt to the whole data set. Verifying and then using another antibody for chTOG localization would be informative. Of course, the negative control should not be their chTOG-FKBP-GFP line, as it does not relocalize most of chTOG.

In the case of GTSE1, an alternative explanation to antibody specificity issues would be that the GTSE1-FKBP-GFP cell line is not in fact homozygously tagged. Given the low expression levels on the western provided, and the detection of GTSE1 on the spindle in the induced GTSE1-FKBP-GFP cell line (but not TACC3-FKBP-GFP), it seems plausible that an untagged copy remains. If there are multiple copies of GTSE1 in Hela cells, one untagged copy could represent a small fraction of total GTSE1. This should thus be ruled out. GTSE1 clones should be analyzed with more protein extracts loaded - dilutions of the extracts can determine the sensitivity of the blot to lower protein levels. In addition, sequencing of genomic DNA can reveal a small percentage with different reads.

We used a two-pronged approach for assessing relocalization of protein partners (staining vs transfected constructs). The staining approach is superior since endogenous proteins are examined, but it is limited by antibody specificity. The transfection approach overcomes this limitation but is in turn limited by effects of overexpression and tagging. Together the two approaches allow us, and anyone employing this method, to get a picture of protein complexes. We didn’t want to create the impression that one or other approach is confounded, but the referee is correct that this analysis would benefit from further work.

Specifically, to address these concerns:

• We will verify and use alternative chTOG antibodies to try to improve this dataset.
• We will test the possibility that an untagged allele of GTSE1 remains. We will use western blotting and a summary of our genomic analysis will be added to the paper.

  3.There is a lot of data contained in the small graphs summarizing quantification of localization in Figs 3 and 4. They would be more accessible to the reader if they were larger and/or an "example" of the chart with labels was present explaining it (essentially what is in the figure legends). Furthermore, there is no statistical test applied to this data that I see. This is needed. How do authors determine whether there is an "effect"?

Our aim was to compress a lot of information into a small space, while still showing some example primary data. All reviewers raised the same concern which tells us that we went too far towards “data visualization”.

To address this point, we will rework these figures.

**Minor issues:**

1.The GTSE1 constructs used for mutation and localization analysis are 720 amino acids long. A recent study analyzing similar mutations uses a 739 amino acid construct (Rondelet et al 2020). The latter is the predominant transcript in NCBI and Ensembl databases. It appears the construct used by the authors omits the first 19 a.a.. I do not think using the truncated transcript affects conclusions of the manuscript, but it could generate confusion when identifying residues based on a.a.#s of mutant constructs (Fig 6). This should be somehow clarified.

We were aware of the longer transcript but were using the 720 residue form since it is the canonical sequence in Uniprot (https://www.uniprot.org/uniprot/Q9NYZ3). We did not know that the 739 form is the predominant transcript. We agree this is unlikely to affect our work but that the numbering may cause confusion.

We have added a note to the Methods (Molecular Biology section) to accurately describe what we and Rondelet et al. have used.

2.The labeling of constructs in Fig 6C/D is confusing, and appears shifted by eye at places. Please relabel this more clearly.

Apologies for the error.

We have relabeled Figure 6C,D and also made a similar alteration to Figure 5C.

The recommended new experimental data (Analysis complex member levels on spindles after full perturbation of spindle chTOG; new chTOG antibody stainings in the FKBP lines; reanalysis of GTSE1 DNA/protein in GTSE1-FKBP line) should only require a new antibody/siRNA, plus a few weeks time to repeat the analyses already in the paper with new reagents.

Reviewer #1 (Significance (Required)):

While multiple individual components of this complex have been previously characterized, the structure and nature of the complex formation and its recruitment to microtubules/spindles remains a complex problem that has yet to be solved.

Overall this study represents a comprehensive localization-dependency analysis of the Clathrin-TACC3 based spindle complex using a consistent methodology. Although several of the conclusions of the findings echo previous reports, some of the previous literature is contradictory within itself as well as with the conclusions here. Analyzing all components with a single, rapid-perturbation technique thus has great value to present a clear data set, given that the experimental setup conditions and analysis are solid (a goal to which the majority of comments refer).

Beyond the complex localization/recruitment analysis, two novel findings of this study that emerge are:

a)GTSE1 contains a second, separate protein region, distinct from the clathrin-binding motifs that is required for its localization to the spindle, and most likely a microtubule-interaction site. This suggests that GTSE1 recruitment to the spindle is more complex than previously reported.

b)PI3KC2A, which has been reported previously to be a stabilizing member of this complex, is in fact not a member, nor localizes to spindles, nor displays a mitotic defect after loss. This is important conclusion to be made as it would correct the literature, and avoid future confusion.

--

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

In this paper, the authors investigate the nature of interactions between members of the TACC3-chTOG-clathrin-GTSE1 complex on the mitotic spindle. By using a series of HeLa cell lines that they have created by CRISPR/Cas9 editing to enable spatial manipulation (knocksideways) of either TACC3, chTOG, clathrin and GTSE1, they show that on spindle microtubules TACC3 and clathrin represent core complex members whereas chTOG and GTSE1 bind to them respectively but not to each other. Additionally, the authors find that the protein PIK3C2A, which has been implicated in this complex previously is in fact not a component of this complex in mitotic cells. The main advance of the paper in my opinion is the endogenous tagging of the proteins for knocksideways experiments since former experiments depended on RNAi silencing and expression of tagged proteins from plasmids, which introduced issues of protein silencing efficiency and plasmid overexpression problems. This approach seems to alleviate these problems, except in the case of chTOG which seems to be lethal in its homozygous variant.

**Major comments:**

I find the key conclusions regarding the localization of the components of the complex convincing. There are some issues regarding the specificity of antibodies in immunostaining experiments (Fig 3.) and the influence of mCherry-TACC3 expression on distorted localization of the complex prior to knocksideways. However, I think the general conclusion about which complex components (clathrin and TACC3) influence the localization of the other proteins in the complex (chTOG and GTSE1) stands. One thing that I miss from the paper is the data on the consequences on the spindle shape and morphology after knocksideways. I have noticed on images in both Figure 3 and Figure 4 that in some cases distribution of the signal seems to influence quite a bit the spindle morphology. Also, In Figure 3 I have noticed what seems to me a quite big variation in spindle size in tubulin signal in both untreated and rapamycin cells. Since authors have many of these images already, I believe it would be realistic, not costly and of additional value for the paper to provide more data on the consequences of the knocksideways experiments. Change of spindle size, tubulin intensity and DNA/kinetochore misalignment upon knocksideways would be helpful to appreciate more the findings of the paper. More so since the authors on more than one occasion find their motivation in the field of cancer research and spindle stability relation to it. Some data connection to this motivation would be of value. Experiments seem reproducible.

The focus of the paper is on using the knocksideways methodology to understand a protein complex during mitosis, rather than looking at its function. We are not keen to do new experiments that are not part of the central message of the paper. However, the Reviewer is correct that we do already have a dataset that can be mined in the manner described.

To address this point, we will analyze spindle size parameters and also the intensity of tubulin. Our analysis will be limited to the short timeframe of our experiments, but it should reveal or refute any changes in spindle structure that may result from loss of complex members.

**Minor comments:**

I have some problems with the clarity of Figure 3 and 4. For Figure 3. In Figure 3 plots on the right are a bit small and not easy to read. Some reorganization of the figure might be beneficial. In Figure 4 plots to the right are also too small to be clear. Also, I miss the number of cells (n) I can't see the number of individual arrows because of the size of graphs.

Our aim was to compress a lot of information into a small space, while still showing some example primary data. All reviewers raised the same concern which tells us that we went too far towards “data visualization”.

To address this point, we will rework these figures.

Reviewer #2 (Significance (Required)):

I find that the biggest significance of the paper is in the creation of new tools (cell lines) to study the localization of proteins TACC3, chTOG, clathrin and GTSE1. Cell lines where endogenous proteins can be delocalized rapidly will be of value for scientist working not only in mitosis but such as in the case of clathrin research, vesicle formation and trafficking or p53-dependent apoptosis in the case of GTSE1. In the field of mitosis it will surely help and speed up the research concerning the role of these proteins in spindle assembly and stability.

Field of expertise: mitotic spindle

--

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

**Summary:**

This papers analyses the chTog/TACC3/clathrin/GTSE1 complex that crosslinks and stabilises microtubule bundles in the mitotic spindle. The authors have developed an elegant knock sideways approach to specifically analyse the effects of removing individual components of the complex from the spindle and study the effect this has on the other interactors. They report, based on these assays that the core of the complex is formed by TACC3 and Clathrin while GTSE1 and chTog are auxiliary interactors. They also refute previous evidence that this complex also incorporates PIK3C2A. Overall, this is an interesting study that distinguishes itself predominantly by its methodology. However, some of the reported results need more thorough analysis to allow convincing conclusions.

**Major comments:**

1)The knockside way method is the main highlight if this paper. Unlike previous studies by the PI, this time endogenous genes are tagged which is a key advance and allows much better interpretation of the results. I am not sure why the authors have chosen HeLa cells as their model here, given the messed up genome of these cells. A non-transformed cell line would have been preferable, but as a proof of principle study, I think HeLa are acceptable, and I wouldn't expect the authors to repeat all the experiment in another system.

Figure 1,2 and S1 are describing and validating this approach in some detail, but this will require some more work.

The authors state that gene targeting was validated using a combination of PCR, sequencing, Western blotting, but show only the results for westerns. PCR analysis that demonstrates homozygous or heterozygous gene targeting should be shown here.

Another issue is the penetrance of the phenotypes induced by Rapamycin. The authors show nice data of the system working in individual cells but do not give us an idea if this happens in all cells. The localisation of the individual tagged genes should be quantified (ideally with line plots) in 50 randomly chosen mitotic cells with 3 repeats before and after rapamycin treatment. Moreover, the analysis of mitotic duration (Figure S1D) should be extended to include a plus Rapamycin cohort and this should be moved in the main Figure.

If the system works only in a small proportion of cells, this should be clearly stated. I don't think this would prevent publication, but it is an important piece of information that is missing.

The Reviewer raises two issues here.

• PCR analysis should be shown. This issue was also partly raised by Reviewer 1. A summary of our PCR analysis was actually included in Table 1, since the analysis we did is pretty unwieldy. We agree though that presenting our evidence for homozygosity of the cell lines would be useful. To address this point, we will add more detail of the PCR and sequencing work done to validate these cell lines.
• Does knocksideways happen in all cells? The answer to this depends on the transient expression of MitoTrap and sufficient application of rapamycin. We agree that this will be a useful piece of information to add to the manuscript. A related issue is whether knocksideways of complex members affects mitotic progression. We have established through other experiments that rapamycin application to wild-type cells alters mitotic progression, although application of Rapalog does not have this effect. Our plan to address these points is 1) to analyze the efficacy of knocksideways that readers can expect to achieve using these, or similar cells, and 2) analyze mitotic duration in rapalog-treated cells expressing a rapalog sensitive MitoTrap.

  2)Apart from a simple quantification of mitotic duration, I believe a more detailed mitotic phenotype analysis for each knock-side way gene, especially the homozygous targeted clones, should be included. This can involve more high-resolution live cell imaging of mitotic progression with SiR-DNA and GFP-tubulin, using the dark mitotrap.

We don’t agree that such an analysis should be included. The focus of this paper is on using the knocksideways methodology to understand a protein complex during mitosis, and not looking at its function. There are several papers on the mitotic phenotypes of these genes probed using RNAi in different cellular systems (examples for chTOG: 10.1101/gad.245603; TACC3/clathrin: 10.1038/emboj.2011.15, 10.1242/jcs.075911, 10.1083/jcb.200911091, 10.1083/jcb.200911120; GTSE1: 10.1083/jcb.201606081). Moreover, our 2013 paper used knocksideways (with RNAi and overexpression) and has a detailed analysis of mitotic progression, microtubule stability, checkpoint activity and kinetochore motions (Cheeseman et al., 2013 doi: 10.1242/jcs.124834).

New experiments that are not part of the central message of the paper and are unlikely to give new insight are not the best use of our revision efforts for this paper (especially during the pandemic). Having said this, Reviewer 2’s suggestion to use our existing dataset to investigate mitotic phenotypes, will largely answer Reviewer 3’s request.

We will analyze spindle size parameters and also the intensity of tubulin. Our analysis will be limited to the short timeframe of our experiments, but it should reveal or refute any changes in spindle structure that result from the loss of complex members.

3)Overall, the quantitative analysis in Figure 3 ,4 and 7 is not good enough and sometimes doesn't fully support the conclusions. In Figure 3,4 a convoluted way of demonstrating the change in localisation is shown and this panel is so small that is almost impossible to read. Also, there is no statistical analysis, and the sample size seems very small . At least 25 cells should be analysed here in 3 repeats. I would suggest to unify the quantification in the MS and use the line plots shown in Figure 5 and 6 and compare each protein before and after rapamycin addition. This is much easier to read and more convincing. The images of the cells panels can be moved to a supplement as they contain very little information. This would generate space to expand the size and depth of the quantitative analysis. Instead of Anova tests, I would recommend using a simple t-test comparing each condition to its relevant control since this is the only relevant comparison in the experiment. Statistical significance should be calculated for each experiment with sufficient sample size. It would also be better to show the individual data points from the three repeats in different colours so that the reproducibility between repeat can be judged.

This type of statistical analysis should be uniformly done throughout the MS and also extended to Figure 7.

The referee raises several issues here with our data presentation and statistical analysis.

• Our aim in Figures 3 and 4 was to compress a lot of information into a small space, while still showing some example primary data. All reviewers raised the same concern about these figures which tells us that we went too far towards “data visualization”. To address this point, we will rework Figures 3 and 4 to provide more clear data presentation.
• The Reviewer’s comments about statistical analysis however are not sound. First, it is incorrect to state that simple t-tests can be applied (this is a form of p-hacking). Correction for multiple testing must be done on these datasets. Second, the reviewer arbitrarily states numbers for cells and experimental repeats without considering the effect size or it seems, understanding the structure of the data that we have collected. Sample sizes are small but they are taken from many independent replicates. Third, and related to the previous point, the fixed and live cell data are structured differently which means that a uniform data presentation is not possible. The live data has a paired design and each cell is an independent replicate (with replicates done over several trials). The fixed data is unpaired and we have taken measures from several experiments (independent replicates). The point about applying statistical tests to the data is also made by Reviewer 1 and we will use appropriate tests (NHST or estimation statistics) as we re-work the figures.

  Reviewer #3 (Significance (Required)):

In my opinion, the most interesting aspect of the MS is the methodology. Based on this, publication is justified and will be of interest to a wider audience. That is why a more detailed analysis of the penetrance of this manipulation across the cell population will be critical.

The application of this method to analyse the composition of the TACC3/Clathrin complex on the spindle is the main biological advance, and the novel information is rather limited but not unimportant.

Overall, if these results can be properly quantified I would recommend publication.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This papers analyses the chTog/TACC3/clathrin/GTSE1 complex that crosslinks and stabilises microtubule bundles in the mitotic spindle. The authors have developed an elegant knock sideways approach to specifically analyse the effects of removing individual components of the complex from the spindle and study the effect this has on the other interactors. They report, based on these assays that the core of the complex is formed by TACC3 and Clathrin while GTSE1 and chTog are auxiliary interactors. They also refute previous evidence that this complex also incorporates PIK3C2A. Overall, this is an interesting study that distinguishes itself predominantly by its methodology. However, some of the reported results need more thorough analysis to allow convincing conclusions.

Major comments:

1)The knockside way method is the main highlight if this paper. Unlike previous studies by the PI, this time endogenous genes are tagged which is a key advance and allows much better interpretation of the results. I am not sure why the authors have chosen HeLa cells as their model here, given the messed up genome of these cells. A non-transformed cell line would have been preferable, but as a proof of principle study, I think HeLa are acceptable, and I wouldn't expect the authors to repeat all the experiment in another system. Figure 1,2 and S1 are describing and validating this approach in some detail, but this will require some more work. The authors state that gene targeting was validated using a combination of PCR, sequencing, Western blotting, but show only the results for westerns. PCR analysis that demonstrates homozygous or heterozygous gene targeting should be shown here. Another issue is the penetrance of the phenotypes induced by Rapamycin. The authors show nice data of the system working in individual cells but do not give us an idea if this happens in all cells. The localisation of the individual tagged genes should be quantified (ideally with line plots) in 50 randomly chosen mitotic cells with 3 repeats before and after rapamycin treatment. Moreover, the analysis of mitotic duration (Figure S1D) should be extended to include a plus Rapamycin cohort and this should be moved in the main Figure. If the system works only in a small proportion of cells, this should be clearly stated. I don't think this would prevent publication, but it is an important piece of information that is missing.

2)Apart from a simple quantification of mitotic duration, I believe a more detailed mitotic phenotype analysis for each knock-side way gene, especially the homozygous targeted clones, should be included. This can involve more high-resolution live cell imaging of mitotic progression with SiR-DNA and GFP-tubulin, using the dark mitotrap.

3)Overall, the quantitative analysis in Figure 3 ,4 and 7 is not good enough and sometimes doesn't fully support the conclusions. In Figure 3,4 a convoluted way of demonstrating the change in localisation is shown and this panel is so small that is almost impossible to read. Also, there is no statistical analysis, and the sample size seems very small . At least 25 cells should be analysed here in 3 repeats. I would suggest to unify the quantification in the MS and use the line plots shown in Figure 5 and 6 and compare each protein before and after rapamycin addition. This is much easier to read and more convincing. The images of the cells panels can be moved to a supplement as they contain very little information. This would generate space to expand the size and depth of the quantitative analysis. Instead of Anova tests, I would recommend using a simple t-test comparing each condition to its relevant control since this is the only relevant comparison in the experiment. Statistical significance should be calculated for each experiment with sufficient sample size. It would also be better to show the individual data points from the three repeats in different colours so that the reproducibility between repeat can be judged. This type of statistical analysis should be uniformly done throughout the MS and also extended to Figure 7.

Significance

In my opinion, the most interesting aspect of the MS is the methodology. Based on this, publication is justified and will be of interest to a wider audience. That is why a more detailed analysis of the penetrance of this manipulation across the cell population will be critical. The application of this method to analyse the composition of the TACC3/Clathrin complex on the spindle is the main biological advance, and the novel information is rather limited but not unimportant. Overall, if these results can be properly quantified I would recommend 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

In this paper, the authors investigate the nature of interactions between members of the TACC3-chTOG-clathrin-GTSE1 complex on the mitotic spindle. By using a series of HeLa cell lines that they have created by CRISPR/Cas9 editing to enable spatial manipulation (knocksideways) of either TACC3, chTOG, clathrin and GTSE1, they show that on spindle microtubules TACC3 and clathrin represent core complex members whereas chTOG and GTSE1 bind to them respectively but not to each other. Additionally, the authors find that the protein PIK3C2A, which has been implicated in this complex previously is in fact not a component of this complex in mitotic cells. The main advance of the paper in my opinion is the endogenous tagging of the proteins for knocksideways experiments since former experiments depended on RNAi silencing and expression of tagged proteins from plasmids, which introduced issues of protein silencing efficiency and plasmid overexpression problems. This approach seems to alleviate these problems, except in the case of chTOG which seems to be lethal in its homozygous variant.

Major comments:

I find the key conclusions regarding the localization of the components of the complex convincing. There are some issues regarding the specificity of antibodies in immunostaining experiments (Fig 3.) and the influence of mCherry-TACC3 expression on distorted localization of the complex prior to knocksideways. However, I think the general conclusion about which complex components (clathrin and TACC3) influence the localization of the other proteins in the complex (chTOG and GTSE1) stands. One thing that I miss from the paper is the data on the consequences on the spindle shape and morphology after knocksideways. I have noticed on images in both Figure 3 and Figure 4 that in some cases distribution of the signal seems to influence quite a bit the spindle morphology. Also, In Figure 3 I have noticed what seems to me a quite big variation in spindle size in tubulin signal in both untreated and rapamycin cells. Since authors have many of these images already, I believe it would be realistic, not costly and of additional value for the paper to provide more data on the consequences of the knocksideways experiments. Change of spindle size, tubulin intensity and DNA/kinetochore misalignment upon knocksideways would be helpful to appreciate more the findings of the paper. More so since the authors on more than one occasion find their motivation in the field of cancer research and spindle stability relation to it. Some data connection to this motivation would be of value. Experiments seem reproducible.

Minor comments:

I have some problems with the clarity of Figure 3 and 4. For Figure 3. In Figure 3 plots on the right are a bit small and not easy to read. Some reorganization of the figure might be beneficial. In Figure 4 plots to the right are also too small to be clear. Also, I miss the number of cells (n) I can't see the number of individual arrows because of the size of graphs.

Significance

I find that the biggest significance of the paper is in the creation of new tools (cell lines) to study the localization of proteins TACC3, chTOG, clathrin and GTSE1. Cell lines where endogenous proteins can be delocalized rapidly will be of value for scientist working not only in mitosis but such as in the case of clathrin research, vesicle formation and trafficking or p53-dependent apoptosis in the case of GTSE1. In the field of mitosis it will surely help and speed up the research concerning the role of these proteins in spindle assembly and stability.

Field of expertise: mitotic spindle

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---

Referee #1

Evidence, reproducibility and clarity

Here Ryan et al. have used localization analysis following induced rapid relocalization of endogenous proteins to investigate the composition and recruitment hierarchy of a clathrin-TACC3-based spindle complex that is important for microtubule organization and stability. The authors generate different HeLa cell lines, each with one of four complex members (TACC3, CLTA, chTOG and GTSE1) endogenously tagged with FKBP-GFP via Cas9-mediated editing. This tag allows rapid recruitment to the mitochondria upon rapamycin addition ("knocksideways"). They ultimately quantify each of the 4 components' localization to the spindle following knocksideways of each component using fluorescently-tagged transfected constructs. The authors' interpretation of the results of this analysis are summarized in the last model figure, in which a core MT-binding complex of clathrin and TACC3 recruit the ancillary components GTSE1 and chTOG. In addition, the authors investigate the contribution of individual clathrin-binding LIDL motifs in GTSE1 to the recruitment of clathrin and GTSE1 to spindles. Their findings here largely agree with and confirm a recent report regarding the contribution of these motifs to GTSE1 recruitment to the spindle. They further analyzed GTSE1 fragments for interphase and mitotic microtubule localization, and identified a second region of GTSE1 required (but not sufficient) for spindle localization. Finally, the authors report that PIK3C2A is not part of this complex, contradicting (correcting) a previously published study.

Major comments:

1.The chTOG-FKBP-GFP cell line the authors generate has only a small fraction of chTOG tagged, and thus should not be used for any conclusions about protein localization dependency on chTOG. Because they were unable to construct a HeLa cell line with all copies tagged, the authors expect that the homozygous knock-in of chTOG-FKBP-GFP is lethal, and thus their experience is appropriate to report. However, the authors should not use this cell line alone to make statements about chTOG dependency. They would have to use similar localization analysis, but after another method to disrupt chTOG (as a second-best approach), such as RNAi. In fact, they have reported this in a previous publication (Booth et al 2011). However, the result was different. There, loss of chTOG resulted in reduced clathrin on spindles, suggesting it may stabilize or help recruit the complex. Alternatively, they could remove their chTOG data, but this would compromise the "comprehensive" nature of the work.

2.The authors initially analyze complex member localization after knocksideways experiments by antibody staining, which has the advantage of analyzing endogenous proteins (versus the later transfected fluorescent constructs). Setting aside potential artefacts from fixation, this would seem to be a better method for controlled analysis to take advantage of their setup (short of generating stable cell lines with second proteins endogenously tagged in a second color - a huge undertaking). The authors conclude that antibody specificity problems confounded their analysis and explained unusual results. However, I think is worth investing a little more effort to sort this out, rather than bringing doubt to the whole data set. Verifying and then using another antibody for chTOG localization would be informative. Of course, the negative control should not be their chTOG-FKBP-GFP line, as it does not relocalize most of chTOG.

In the case of GTSE1, an alternative explanation to antibody specificity issues would be that the GTSE1-FKBP-GFP cell line is not in fact homozygously tagged. Given the low expression levels on the western provided, and the detection of GTSE1 on the spindle in the induced GTSE1-FKBP-GFP cell line (but not TACC3-FKBP-GFP), it seems plausible that an untagged copy remains. If there are multiple copies of GTSE1 in Hela cells, one untagged copy could represent a small fraction of total GTSE1. This should thus be ruled out. GTSE1 clones should be analyzed with more protein extracts loaded - dilutions of the extracts can determine the sensitivity of the blot to lower protein levels. In addition, sequencing of genomic DNA can reveal a small percentage with different reads.

3.There is a lot of data contained in the small graphs summarizing quantification of localization in Figs 3 and 4. They would be more accessible to the reader if they were larger and/or an "example" of the chart with labels was present explaining it (essentially what is in the figure legends). Furthermore, there is no statistical test applied to this data that I see. This is needed. How do authors determine whether there is an "effect"?

Minor issues:

1.The GTSE1 constructs used for mutation and localization analysis are 720 amino acids long. A recent study analyzing similar mutations uses a 739 amino acid construct (Rondelet et al 2020). The latter is the predominant transcript in NCBI and Ensembl databases. It appears the construct used by the authors omits the first 19 a.a.. I do not think using the truncated transcript affects conclusions of the manuscript, but it could generate confusion when identifying residues based on a.a.#s of mutant constructs (Fig 6). This should be somehow clarified.

2.The labeling of constructs in Fig 6C/D is confusing, and appears shifted by eye at places. Please relabel this more clearly.

The recommended new experimental data (Analysis complex member levels on spindles after full perturbation of spindle chTOG; new chTOG antibody stainings in the FKBP lines; reanalysis of GTSE1 DNA/protein in GTSE1-FKBP line) should only require a new antibody/siRNA, plus a few weeks time to repeat the analyses already in the paper with new reagents.

Significance

While multiple individual components of this complex have been previously characterized, the structure and nature of the complex formation and its recruitment to microtubules/spindles remains a complex problem that has yet to be solved.

Overall this study represents a comprehensive localization-dependency analysis of the Clathrin-TACC3 based spindle complex using a consistent methodology. Although several of the conclusions of the findings echo previous reports, some of the previous literature is contradictory within itself as well as with the conclusions here. Analyzing all components with a single, rapid-perturbation technique thus has great value to present a clear data set, given that the experimental setup conditions and analysis are solid (a goal to which the majority of comments refer).

Beyond the complex localization/recruitment analysis, two novel findings of this study that emerge are:

a)GTSE1 contains a second, separate protein region, distinct from the clathrin-binding motifs that is required for its localization to the spindle, and most likely a microtubule-interaction site. This suggests that GTSE1 recruitment to the spindle is more complex than previously reported.

b)PI3KC2A, which has been reported previously to be a stabilizing member of this complex, is in fact not a member, nor localizes to spindles, nor displays a mitotic defect after loss. This is important conclusion to be made as it would correct the literature, and avoid future confusion.

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