Author Response

Reviewer #1 (Public Review):

This is a very interesting paper trying to quantify excess deaths due to the COVID-19 pandemic in the USA. The paper is roughly divided into two main sections. In the first section, the authors estimate age and cause-specific excess mortality. In the second section, using their excess mortality estimates, the authors attempt to disentangle the impact of SARS-CoV-2 infection (direct impact) vs. the impact of NPIs on this excess mortality (indirect impact). I have some concerns, particularly with respect to the second section.

The model used to estimate excess mortality is quite clear. The authors adjust the baseline model to account for low influenza circulation (and deaths) during the COVID-19 pandemic, to avoid underestimating the number of deaths caused by COVID-19. While this makes sense if the authors are trying to estimate the total number of deaths caused by COVID-19, I'm not sure it needs to be accounted for if the authors want to estimate excess/added deaths. A counterfactual scenario would've included influenza. It also raises the question of whether (conceptually) they should be adjusting for other causes of deaths that may have also decreased during the pandemic. The authors briefly acknowledge this in the discussion ("we can't account for changes in baseline respiratory mortality due to depressed circulation of endemic pathogens other than influenza") but my comment goes beyond respiratory diseases. Analyses of excess mortality from other settings have suggested, for example, decreased deaths due to fewer traffic accidents (not in the US) or due to decreased air pollution, and not accounting for these would also lead to an underestimate of the total deaths caused by COVID-19. I understand that it is not feasible to account for all potential factors, so I wonder if they should focus on reporting excess deaths as compared to a counterfactual with influenza.

Thanks. We think it is helpful to “single out” influenza as it causes major fluctuations in mortality from multiple causes in regular years and is a useful reference to contrast the pandemic impact. But the reviewer’s point is well taken. We have clarified our assumptions about the meaning of the baseline in this analysis (methods p 5), discussed the depressed circulation of other pathogens in depth, and mentioned air pollution (p 12-13). We have also slightly reworked our comparison between COVID19 and influenza so that excess mortality estimates are comparable and now cover periods of the same duration (Nov 2017-Mar 2018 for flu and Nov 2020-Mar 2021 for COVID19, see Figure S11).

The second section, trying to estimate direct vs. indirect effects is also very interesting. However, more details are required about the regression model used and, importantly, what the assumptions and limitations of the approach are. Specifically:

• Please provide a bit more information on the regression used for direct vs. indirect effects. I'd like to see explicit discussion of the assumptions and limitations of the approach but also of the stringency index used. Does this model include an intercept? Was the association between stringency index and excess deaths assumed to be linear? Or were different functional forms considered? It is also not clear how well the model fits the data.

Thanks for these comments which helped us improve this section. We have provided more details about the stringency index in methods (it captures the “sum” of interventions), described the model in methods and supplement, and discussed limitations in caveats section, especially regarding effectiveness of these interventions (p13). We had tried different linear models with and without intercepts but elected to use models with intercepts so as not to overly constrain the relationship between interventions, COVID19 activity and excess mortality. These models also incorporate lags in the predictors that are determined by cross-correlation analysis (as detailed in supplement). In the revised version, we now use gam models, where the relationships between excess mortality and predictors do not have to be linear. We can do so since we were able to add several weeks of data (the regression is now based on 96 pandemic weeks from March 1, 2020 to January 1, 2022). The models are described in detail in supplement p 4-5, and we now specify that they have intercepts. We have also provided additional plots of model fits in main text and supplement (Figures 4 and S16-19).

• Related to the above, please provide more details on how the results of the regressions were translated into the results presented. The main text reports percentages, but the methods only briefly explain how numbers of direct deaths were calculated, and the supplementary tables report coefficients. It is not clear if these estimates of direct and indirect deaths were somehow constrained to add up to the total number of excess deaths, but it doesn't seem like it since point estimates cross 100% in some cases.

As discussed in response to one of the editor’s questions, estimates are not constrained to 100%. We have provided more details in the supplement on how we estimate the direct impact of the pandemic. Briefly, we calculate expected deaths in the gam model with all predictors set to their observed values and again with the COVID19 predictor to zero. The direct impact is the difference between the two predictions, divided by the predictions of the full model.

We note that while some of the estimates derived from gam model exceed 100% (and are similar to the linear model estimates presented in the initial analysis, before revision), these estimates echo the findings from a more empirical analysis, in which we compare all-cause excess deaths with official COVID19 deaths tallies. There, in the two oldest age groups, we find more official COVID19 deaths than estimated by the excess mortality models. Hence both analyses point to an underestimation of the direct burden of COVID19 by the excess mortality approach, specific to the oldest age groups. We return to this point in depth in the discussion (p 12-13) and consider the possible effects of harvesting, depressed circulation of non-SARS pathogens, and inaccurate coding of official statistics (as pointed by reviewer #3).

• Please discuss the potential limitations of using the stringency index to quantify NPIs.

Several limitations have been added to caveats (p 13); major issues include aggregation of multiple interventions into a single index, which does not consider the actual implementation nor the effect of interventions. The index is solely based on mandates in place in different locations and time periods. We also assume that the effectiveness of these interventions, for a given level of stringency, does not change over time.

• When estimating direct and indirect effects, the paper assumes that the estimated parameter is time-invariant? Indirect effects might have changed over the course of the epidemic by factors not necessarily captured by the stringency index used, particularly since the index doesn't take into account the implementation of the measures. Have the authors tested this assumption?

This is an interesting point, which we have explored further. The non-linear relationships we find between NPIs and chronic condition excess mortality may suggest that the reviewer is right. We discuss the role of NPIs in the results section much more deeply than we were previously (bottom of p8).

“At lower levels of interventions (Oxford index between 0 and 50), representing the early stages of the lockdown in March 2020, excess mortality rose with interventions. Later in the pandemic, increased interventions were estimated to have a beneficial effect on excess mortality, driven by comparison between the period when interventions were strengthened in response to increasing COVID19 activity in late 2020 (Oxford index above 60) to the period when interventions were relaxed in 2021 (Oxford index between 50 and 60).”

We cannot run an analysis over different time windows because NPI and time are highly conflated (for instance NPI rise from 0-50% in the very early part of the lockdown period, and then stays above 50% for the rest of the study, so we cannot compare the effect of a 25% level in 2020 and 2021). We have added this limitation in the caveat section p.13.

• The authors state "In contrast, the indirect impact of the pandemic measured by the intervention term was highest in youngest age groups, decreased with age, and lost significance in individuals above 65 years" - I'm not entirely sure of where this statement comes from? For example Table S3 suggests that the indirect effect (multivariate or univariate) is higher in 25-64 yo than in <25s? The same table also suggests negative impacts (protective effects?) in >75s in the multivariate model. Please clarify.

There are fewer deaths in the under 25 yo so this is why the coefficients were lower overall in table S3. Yet we find that the proportion of variance explained by interventions is higher in the under 25 yrs than in 25-44 yrs.

We have now changed our modeling strategy to use gam so Table S3 is no longer relevant but the main conclusion that interventions explain a larger relative portion of excess mortality in the under 25 yrs than in the other age groups, and than other covariates, remains valid. The NPI term is now significant is in all groups (although the relative contribution of NPI still declines with age, as in the prior analysis), so we have rephrased this sentence: “In contrast, the relative contribution of indirect effects, via the intervention variable, was highest in youngest age groups and decreased with age”.

• How do the authors interpret "Percents of excess deaths" over 100%? Similarly, I don't fully understand how to interpret "The upper bound of the 95% confidence interval for heart diseases was above 100% (158%), suggesting that for every excess death from heart disease estimated by our model, up to 1.58 death from heart disease could be directly linked to SARS-CoV-2 infection.

We have rephrased this section although the overall conclusions remain unchanged. GAM estimates of the direct COVID 19 impact is statistically significantly above 100% in the 85 yo and over, suggesting that our excess mortality approach is too conservative and does not estimate enough COVID19 excess deaths in this age group. We draw a similar conclusion from a more empirical analysis, in which we compare all-cause excess death estimates with official COVID19 deaths tallies. In this analysis, we find more official COVID19 deaths than estimated by the excess mortality models in the two oldest age groups (point estimates above 100% in the 75-84 and 85+ yrs). Hence both analyses point to an underestimation of the direct burden of COVID19 in the oldest age groups by excess mortality approaches.

Rephrased results section bottom of p.9: “We estimate that the direct contribution of COVID-19 to excess mortality increases with age, from negative and non-statistically significant in individuals under 25 yrs to over 100% in those over 85 years, echoing the gradient seen in official statistics (Table 4). It is also worth noting that our excess mortality estimates may be too conservative (too high) as we did not account for missed circulation of endemic pathogens. This could explain why our estimates of direct COVID-19 contribution exceed 100% in the oldest age group.“

We return to this point in depth in the discussion and consider the possible effects of harvesting and depressed circulation of non SARS pathogens (p 12-13).

• Table 3: The signs of the point estimate vs CI for vehicle accidents are inconsistent.

Thanks, this was a typo. It should have been 4300 (-700, 9300) excess deaths from accidents. This has been updated with more recent data.

Reviewer #3 (Public Review):

Authors examine mortality data in the US and use time-series approaches to estimate excess mortality during the COVID-19 pandemic.

Major comments:

I would encourage authors to discuss the two different concepts of excess mortality:

(#1) what deaths were caused, directly or indirectly, by the pandemic. This is what the authors have aimed to assess, and I have no major concerns with the methodology

(#2) how many additional deaths occurred during the pandemic, compared to what would have been expected in the absence of a pandemic. For such an analysis I think expected annual influenza deaths should be added back to the baseline (or subtracted from the excess)? Some of the discussion seems to relate more to an impression of #2 rather than #1 but I would be interested in the authors' thoughts.

We have added more details about the approach, in particular why we think that #1 is the proper analysis here (see methods p 5). Given the sheer magnitude of COVID19 excess deaths (over 1 million excess deaths at the end of our study), adding back influenza deaths (up to 52,000 deaths in a recent severe season with a mismatched vaccine, as in 2017-18) would not make a large difference. We have also provided a more direct comparison of the impact of influenza and COVID19.

1. Authors estimate fewer excess COVID deaths in the elderly than there were confirmed deaths (Table 3). Could this be an indication of some confirmed deaths being "deaths with COVID" rather than "deaths from COVID"? I'm not sure how to interpret the %s in the final column when they exceed 100%. The authors suggested a harvesting effect but I would suggest "deaths with COVID" might be a more likely explanation? This issue can be a limitation of confirmed-death data.

This is a good point. We have added a comment along these lines in discussion in the middle of p 12. Still, we think harvesting and/or the depressed circulation of endemic pathogens, which would have inflated our baseline, are more likely explanations for these findings. This is because we find similar estimates (exceeding 100%) in gam models that ignore official statistics and rely on COVID19 case data, or COVID19 hospital occupancy data, and this suggests that other mechanisms, beyond coding of official mortality statistics, are at play.

Yet, as more detailed official statistics become available, a tabulation of confirmed deaths by presence of a primary vs secondary COVID (U07) code may be revealing and get more directly at the reviewer’s question.

Author Response*

Reviewer #1 (Public Review):

ARL3 is a small GTPase that localizes to the primary cilium and plays a role in regulating the localization of some specific ciliary membrane proteins, including PDEδ and NPHP3. Mutations in this gene cause Joubert syndrome, a type of ciliopathy characterized by cerebellar malformation, and retinal degeneration. While the majority of the diseases occur in an autosomal recessive manner, two mutations in ARL3 (D67V and Y90C) have been reported to cause autosomal dominant retinal diseases. In the current paper, Travis et al. sought to understand the pathogenesis of the diseases caused by the two autosomal dominant mutations. They found that D67V acts as a constitutive active mutation, whereas Y90C is a fast-cycling mutant, which can be activated in a guanine nucleotide exchange factor (GEF) independent manner. Since the fast-cycle mutant did not bind to the effector proteins in vitro (likely because the guanine nucleotide falls off from the mutant ARL3, which has a lower affinity to GDP/GTP), they developed a method to snapshot the interaction between ARL3 and its effector. Using this method, they showed that the Y90C mutant indeed has increased interaction with the effectors, suggesting that Y90C is an overactive form of ARL3. They then addressed how photoreceptor cells are affected by these two mutations using a mouse model and found that the mutations disrupt the proper migration of the photoreceptor cells.

Strengths:

• The paper is well written, and it was easy to understand what the authors did from the figure legends and the methods section.

• It was easy to find out what is known or unknown, as the paper has accurate references.

• The authors developed a method to analyze a snapshot of the interaction between ARL3 and its interactors.

• The paper has an in vivo model and connects the biochemical characteristics of ARL3 to in vivo cellular phenotypes.

Weaknesses:

(1) I understand that authors focused on nuclear migration defect as the phenotype was first described in ARL3-Q71L transgenic mice. The similar phenotype observed in RP2 knockout mice further supports the idea that the defect is caused by the hyperactivation of ARL3. Indeed, the defect is not reported in the ARL3 knockout mice, however, I feel that it does not necessarily mean that the defect is not caused by loss of function. Although it has not been assessed, ARL3 knockout mice might have the same defect. Therefore, I think analyzing both the migration defect and trafficking defect would be more informative, rather than focusing on the migration defect. The fact that the relationship between nuclear migration defect and the retinal degeneration phenotype is not entirely clear further enhances the importance of analyzing the trafficking defect.

Does the expression of ARL3-Y90C also cause the trafficking defect? If it is the case, you can separate the nuclear migration phenotype from the one caused by the trafficking defect. Would the expression of lipidated cargo(s) rescue the trafficking defect as well?

I think many questions can be addressed by analyzing the localization of the lipidated cargos, such as PDEδ and GRK1.

The effect of Arl3-Y90C expression on trafficking of lipidated cargos is an interesting question. Previous papers showed mislocalization of lipidated outer segment proteins in Arl3-KO rods and down-regulation or subtle mislocalization in Arl3-Q71L overexpressing rods. So, this was one of the first things we investigated; however, we never observed mislocalization of ciliary or outer segment lipidated cargos (i.e. GRK1, transducin, Rab28, and PDE) in wild type mature rods that were overexpressing Arl3 mutants, and many were tested. It was through these experiments that we first identified the pronounced nuclear migration defect. Rod photoreceptor nuclear migration is a developmental process that is completed by P10, so Arl3-Y90C overexpression is causing a developmental defect. When rods are positioning their nuclei in the ONL, they are still “immature” as their primary cilium has not begun to elaborate disc membranes for light capture. All our analysis was performed in mature rods, so it is not surprising that we did not observe any lipidated trafficking defects at this timepoint. Since the developmental timing of the nuclear migration defect is important for our manuscript, we have added this to our introduction. Additionally, we use “immature” photoreceptors for the cartoon diagrams showing how Arl3 activity is altered by different mutation and rescue experiments, since formation of the mature outer segment occurs post-migration.

(2) I am not quite sure if the nuclear migration was assessed properly. Based on the pictures in Fig.1, some of the FLAG-negative cells also seem to be migrating to INL (please see Fig.1C and Fig.1D). Is this biologically normal during development? Could this analysis be affected by the thickness of OPL, the layer between ONL and INL? Also, the picture is cut out in the middle of INL. Could authors include more layers, such as IPL, of the retina in the picture, so that we can evaluate INL and OPL better? Taking this into account, I think it is worth measuring the nuclear position of FLAG-negative cells as a negative control in all the experiments.

Our electroporation technique results in a small population of rods that express our constructs of interest (~5-15% with a patch). All the experiments were performed in wild type retina which develop normal retinal layers, so analysis of the nuclear position of FLAG-positive cells with the retina is cell autonomous. Migration defects are assessed by differences in the skew of FLAG-labeled rods relative to the boundaries of the wild type ONL, which is marked by Hoechst nuclear stain (also a measure of the FLAG-negative rods). Wild type photoreceptors nuclei are not found within the INL, the nuclei in that layer belong to either horizontal cells or bipolar cells both of which are not targeted by our electroporation approach. As a control, we show that when wild type Arl3-FLAG was expressed FLAG-labeled rods were never observed within the INL. We have now included the % of displaced nuclei in Table 1.

(3) The way that the authors showed the Y90C mutant of ARL3 is a fast-cycling mutant is not very compelling. In Figure 2C, the authors showed that ARL3 Y90C can bind to PDEδ, its effector, once it is pre-loaded with GTP. The authors also showed that the mutant can bind to its effector even without EDTA as long as an excess amount of GTP is added. The authors used endogenous ARL3 as a control to compare the effects between wild-type and mutants. I see that this experiment has multiple pitfalls. First, ideally, this type of experiment needs to be done with a purified protein using fluorescent guanine nucleotide/radioactive guanine nucleotide (e.g. nucleotide loading assay or nucleotide exchange assay) to directly access the kinetics of nucleotide exchange. However, I do understand that this is out of the authors' expertise. In the authors' experimental setting, I am not sure loading the protein with GTP in the presence of the EDTA means anything more than confirming that the protein is intact. Theoretically, wild-type and a fast-cycling mutant can load GTP with similar efficiency in the presence of EDTA. Then during immuno-precipitation, GTP falls off from the Y90C mutant faster than wild-type (because a fast-cycling mutant theoretically has a lower affinity to guanine nucleotides), assuming that GTP was not added during immuno-precipitation (GTP addition was not mentioned in the method, but could authors confirm this?). But in this case, the kinetic of GTP dissociation can be affected by many factors, including the presence of GAP in the reaction, the dissociation constant of Y90C, the volume of the buffer used, and the number of washing steps. Thus, it is not very easy to estimate the difference between wild-type and Y90C. Besides, using endogenous ARL3 rather than ARL3-wild type FLAG as a control can be dangerous. I have experienced that a tagged protein is cleaved to a protein that has a similar size to endogenous protein. (I expressed GFP-protein X in knockout cells lacking protein X, and saw the band at the position where the endogenous protein is observed in wild-type cells). So, the endogenous band that the authors showed could come from the cleaved FLAG-Arl3. (Authors can easily confirm this by having wild-type not expressing FLAG-tagged ARL3, though).

An alternative experiment that I would suggest is doing immuno-precipitation in the buffer containing: 1) no guanine nucleotide, 2) 10mM GDP, or 3) 10mM GTP in the cells expressing the following protein: 1) ARL3 wild-type FLAG, 2) ARL3 Y90C FLAG, or 3) ARL3 D129N FLAG. 10mM guanine nucleotide should be added throughout the process including washing. This experiment might also be affected by many factors, but variability should be lower than the experiment presented in Fig 2C. ARL3-wild type FLAG is also a better control here than endogenous protein.

Variability due to the factors you mention is a concern, but we were able to repeatedly obtain the same results using our method—admittedly our method is testing whether the mutated Arl3 can exchange under a certain condition more than exactly how. We know that we are not providing precise kinetics or elucidating the underlying mechanism for how these mutations lead to what we are calling fast cycling. While that information is important, it is outside the scope of this paper.

As you mention, an important conclusion from the PDEδ binding experiments is that we confirm the Arl3-Y90C protein is intact by showing it can indeed bind nucleotide as long as there is an excess of GTP (Fig 2B. The interesting finding from these experiments is that Arl3-Y90C binds GTP even in the presence of magnesium, a behavior not observed for wild type Arl3. We feel that showing that endogenous Arl3 is not activated in the presence magnesium in each of our preparations is a lovely internal control. However, we agree that showing wild type Arl3-FLAG in these assays is an important negative control and have now included this blot as Fig 2-Sup Fig 1.

(4) In Fig.3, the authors attempted to take a snapshot of the interaction between ARL3 and multiple effector proteins. The three bands that were enriched in the Q71L cells were found as RP2, UNC119, and BART by mass spec (Fig.3B). These bands were used as a readout for the subsequent experiments. I am not quite sure why the authors used this approach rather than using the cell line that expresses both FLAG-ARL3 and GFP tagged protein of interest, just like what the authors did in Fig3G. The reasons why I prefer the latter approach are the following: FLAG bands that correspond to the three proteins (RP2, UNC119, and BART) in wild-type cells are very close to the detection limit, 2) authors failed to confirm that the lowest band actually comes from BART, 3) authors cannot access some important effector proteins, such as PDEδ because 293 cells might not express them. All of the problems can be solved by using the approach that was taken in Figur 3G.

If the authors chose the former approach because of some specific reason, I would appreciate it if the authors could explain that in the main text of the paper.

In vitro crosslinking experiments were performed to test whether overexpression of Arl3 mutants resulted in an active cellular Arl3 without artificially changing any components of the GTPase cycle. We feel these experiments are highly elegant as they allow us to take a snapshot of native Arl3 activities without compromising the analysis by artificially altering GAP/GEF/effector interactions through overexpression or during lysis (as we show that the concentration of GTP/Mg could alter interactions in Fig 2). While AD293T cells are not rod photoreceptors, we are able to use this system to better understand how the Arl3 mutants alter the level of activity within the cell. Yes, this experimental assay is novel, but we confirmed the identity of the effectors by Western and mass spec, used positive and negative controls in each experiment, and show that the method is highly reproducible. We agree with Reviewers 2 and 3 that using this method to study the cellular activity of fast cycling Arl3 mutants is a strength of our paper.

(5) ALR3 Y90C causes nuclear migration defect. Given that Y90C is a fast-cycling mutant (hyperactive) and has a high affinity to ARL13B, the nuclear migration defect might come from either the increased activity of ARL3 or sequestration of ARL13B, which can act as a GEF for ARL3 but potentially have other functions. If my understanding is correct, the authors concluded that the defect caused by ARL3-Y90C is likely due to hyper-activation of the protein, as Y90C/T31N mutant, which cannot bind to effectors but still retains the ability to capture ARL13B, did not cause migration defect. But I am a little confused by the fact that Y90C/R149H, which is unable to bind to ARL13B (Fig.2C) but still retains the ability to interact with the effectors (Fig.3F), did not have migration defect (Fig.7B). Wouldn't this mean that the sequestration of ARL13B could contribute to the phenotype?

If my understanding is correct, the authors are trying to say that both hyper-activation of cytosolic ARL3 and the defect in endogenous ARL3 activation in cilium is necessary to cause migration defect. I am not very convinced by this hypothesis, and still think that the defect could be caused by sequestration of ARL13B to the cytoplasm.

Then why Y90C/T31N did not cause the defect even though they can sequester ARL13B? This might be explained by the localization of the ARL13B mutants. If Y90C can localize to the cilium while the double mutant, Y90C/T31N, does not, then only Y90C might be able to inhibit the ARL13B function in the cilium. This could explain the lack of the defect in the cells expressing Y90C/T31N.

It would be helpful to understand how exactly the fast-cycling mutant causes the defect if the authors can provide more information, including localization of ARL3 (wild-type and mutants) as well as key proteins, such as ARL13B and the effector proteins. Assessing ARL13B defect seems to be particularly important to me because ARL13B deficiency has been connected to neuronal migration defect (Higginbotham et al., 2012)

What I am trying to say here is that how the defect is caused is likely very complex. So, providing more information without sticking to one specific hypothesis might be important for readers/authors to accurately interpret the data.

Our data shows that for the fast cycling Arl3-Y90C mutation both features: blocking endogenous Arl3 activation in the cilium (through Arl13B binding) and increasing activity of Arl3-Y90C in the cell body are required to produce a nuclear migration defect. We find that we can rescue migration defects by either restoring activation in the cilium or reducing GTP activity outside the cilium. As long as there is more Arl3-GTP activity in the cilium, then the rod can handle aberrant Arl3-GTP activity in the cell body. The Y90C/R149H was a critical result that led to our hypothesis that there is a gradient between the two compartments that is used for proper migration. One interesting point is that absence of any activity does not produce the migration phenotype, further suggesting that an imbalance in the gradient is important.

We performed new experiments to investigate whether Arl3-Y90C is sequestering Arl13B away from the cilium but found that localization of Arl13B (both endogenous and overexpressed) is not altered by expression of Arl3-Y90C – see Fig 3-SupFig 1-2.

It is an interesting question as to how different Arl3-FLAG constructs are localized within the photoreceptor. Sadly, we did not analyze the data in a way that would allow us to draw any conclusion about the localization of different Arl3-FLAG constructs. In general, we observed FLAG localization throughout the photoreceptor cell and focused our imaging on the FLAG staining around the nucleus so we could further analyze ONL position. Looking back through our images, some of mutants might have a more prominent localization within a specific subcellular compartment (e.g. Arl3-D67V is more prominent in the inner segment than outer segment and Arl3-Y90C appears to have dominant outer segment localization). Likely, these differences represent each mutant binding a particular effector: D67V to RP2 and Y90C to Arl13B, which we show biochemically. Ideally, Arl3 mutant localization would be analyzed during development to provide a more direct link to the nuclear migration defect, a future direction for our lab. We have updated our manuscript to be more transparent about the potential differences in rod localization of Arl3 mutants.

(6) The rescue experiments that the authors presented in Fig.5-6 are striking and would build a base for future therapy of the diseases caused by ARL3 defects. However, I believe more examinations are needed to accurately interpret the data. The authors did this rescue experiment by co-injecting ARL3-FLAG and chaperons/cargos if I understand the method section correctly. But I feel we can interpret this data correctly only when ARL3-FLAG and chaperons/cargos are co-expressed in the same cells. I think a better way to analyze the data might be by comparing the nuclear migration phenotype between ARL3-FLAG only and ARL3-FLAG;chaperons/cargos double-positive cells.

Our lab has found that the initial estimates by the Cepko Lab that co-injection of two plasmids results in above 90% of rods expressing both proteins is accurate (see reference Matsuda and Cepko PNAS 2004). Since we only assess nuclear position of FLAG-labeled rods, it is true that a small percentage of cells in this analysis express the Arl3-FLAG mutant and not the chaperone/cargo; however, inclusion of these cells really only bolsters our findings as complete rescue would likely be even more robust than measured.

Reviewer #2 (Public Review):

The small GTPase Arl3 (Arf-like 3) is a well-characterized component of primary cilia, including the outer segment of photoreceptors, which contain specialized cilia. Arl3 is critical for the import of multiple lipid-modified proteins into cilia that are vital to ciliary function. Human mutations in Arl3 are reported to cause both autosomal recessive and dominant inherited retinal dystrophies, but the mechanisms through which these mutations disrupt photoreceptor development are not known. Here the authors show that two dominant Arl3 mutants, Arl3-D67V and Arl3-Y90C exhibit increased activity, but for different reasons. Arl3-D67V is constitutively active (unable to hydrolyze GTP), whereas Arl3-Y90C is a classic rapid-cycling mutant, able to bind GTP spontaneously (independent of its guanine nucleotide exchange factor Arl13) but still able to complete the GTPase cycle by hydrolyzing GTP. Expression of either mutant in developing murine retinas results in a nuclear migration defect, specifically aberrant localization of rod nuclei to the inner rather than outer nuclear layer. In this sense, they phenocopy another well-characterized constitutively active mutant, Arl3-Q71L. Normal nuclear distribution could be restored by overexpression of Arl3 effectors, suggesting that the active mutants disrupt nuclear migration, at least in part, by sequestering Arl3 effectors.

While the data are reasonably clear and convincing, there are several instances where the conclusions drawn are either confusing or problematic. Specifically:

1) Although retinal rod cells are ciliated in their outer segment, the authors never actually examine ciliation here. Their only morphological readout is nuclear migration. How does nuclear migration failure impact ciliogenesis in the outer segment?

Imaging was performed in mature retinas at P21 after outer segment formation is completed. Electroporation only targets a small population of cells for which we observed normal outer segments structures in all conditions tested — therefore we conclude that ciliogenesis is unaffected. Previous literature has also showed that defects in rod nuclear migration do not affect ciliation of the outer segment.

2) The Arl3-Y90C mutant seems to act physiologically more like a dominant-negative than an activated mutant. A second mutation in Y90C (R149H) that blocks binding to the GEF Arl13 abrogates the nuclear migration defect, suggesting that Y90C is preventing activation of endogenous Arl3 by sequestering the GEF. Yet overexpression of effectors or cargos still rescues nuclear migration in the presence of Y90C, suggesting that it also sequesters effectors. How do the authors explain this?

We agree with this interpretation. We have now included language about Arl3-Y90C’s role as a dominant negative in that it blocks Arl13B activity. The interesting caveat to this black and white usage is that blocking Arl13B would suggest a reduction in endogenous Arl3 activity in rods (which we find to be true, see Fig 5A). However, the migration defect phenotype mimics overly active Arl3 (Arl3-Q71L) and not a loss of function in Arl3 (Arl3-T31N). Using in vivo crosslinking experiments, we show that the fast cycling nature of Arl3-Y90C also causes GEF-independent activation of Arl3 (Fig 4D-E) that leads to the migration defect. Our rescue data shows that only the combination of both effects – reduced Arl3 activity in the cilium and GEF-independent Arl3 activation outside the cilium - is enough to disrupt the ciliary gradient and produce the migration defect.

3) Fig. 1 suggests that an Arl3-T31N mutant has no phenotype. This is a canonical mutation in small GTPases that typically renders them dominant negative. The lack of phenotype is surprising since most dominant-negative mutants act by sequestering their GEFs, thereby preventing activation of the endogenous GTPase. Fig. 2C suggests that this may not be the case for Arl3-T31N, which binds Arl13 only weakly. Some of this confusion may arise from the fact that Arl13 is not a typical GEF. It is very unusual for one GTPase to directly promote nucleotide exchange on another. Does Arl3-T31N affect ciliation in the rod outer segment, or in other ciliated cells? Some discussion of this point is warranted here.

Our paper finds that Arl3 mutants must produce an aberrant activity outside the cilium, whether through constitutive activity (seen for D67V and Q71L) or fast cycling (seen for Y90C and D129N) to cause the migration defect. Since T31N does not cause excess Arl3 activity in cells (see Fig 4) even if it does have some dominant negative activity toward Arl13B, then it is still not enough to cause the migration phenotype. This was directly tested in Fig 5, where we increase T31N binding to Arl13B by introducing Y90C/T31N and still do not see migration defect. Our results are also in line with a previous study showing that despite rapid photoreceptor degeneration in a retina-specific conditional Arl3 knockout mouse the outer segments were initially formed, in contrast the retina-specific conditional Arl13B knockout mouse did disrupt photoreceptor ciliogenesis leading to a more rapid degeneration (Hanke-Gogokhia, JBC 2017). Since complete loss of Arl3 activity did not disrupt ciliogenesis, it is unlikely that expression of Arl3-T31N in wild type retinas would alter outer segment formation, and we observed that outer segments formed in all Arl3 mutants.

4) Oddly, Arl3-Y90C does robustly bind Arl13 (Fig. 2C), while at the same time binding to effectors (Fig. 3D/E), although less strongly than the canonical Q71L constitutively active mutant (Fig. 2A). As noted in point #2, the Y90C/R149H double mutant, which fails to bind Arl13, abrogates the nuclear migration defect observed with Y90C alone. Although the authors refer to Y90C as "rapid cycling" its phenotype is more similar to a dominant-negative than an activated mutant.

We agree with this interpretation. We have now included language about Arl3-Y90C’s role as a dominant negative in that it blocks Arl13B activity. However, the rapid cycling behavior is important to cause the phenotype.

5) The authors also mention that loss of Arl3 has no phenotype in their assay, however, Arl3 knockout mice exhibit severe retinal degeneration. How do they explain this?

Our study finds that not all human Arl3 mutations will target the same cellular process even though they all result in degeneration. Arl3 knockout mice show drastic alterations in lipidated protein trafficking to the rod outer segment in mature retinas, a phenotype that we did not observe by expressing the dominant Arl3 mutants in wild type rods. Since our tools are not designed to study degeneration of rods, the precise mechanisms of degeneration caused by loss of function or dominant mutations remains to be determined. We outline some ideas in the discussion, but more work needs to be done before making any big statements regarding this. We hope that our manuscript will inspire clinicians to take a closer look at human patients to determine if there are subtle differences between disease presentation for dominant and recessive forms Arl3 inherited mutations. This is beyond the scope of our expertise.

Reviewer #3 (Public Review):

This work provides mechanistic insights into two recently described dominant variants of Arl3, a small GTPase, namely mutations D67V and Y90C. The authors identified a phenotype of these dominant variants during the development of rod photoreceptors by in vivo experiments in mice. They specifically observed a defect in rod nuclear migration to their final outer nuclear layer. This phenotype has been previously observed in another constitutively active variant of Arl3, Q71L. The authors performed a series of extensive and thorough biochemical assays to clarify the mode of action of these variants, mostly the Y90C variant, comparing the behavior of these variants to previously described mutants and combining multiple variants by mutagenesis. They also developed a new in vivo crosslinking strategy to be able to identify transient states of protein-protein interactions. They finally performed phenotypic rescue experiments by co-expression of various relevant proteins interacting/involved with Arl3. They finally propose a model based on differential subcellular compartmentalization of Arl3 activation which when disrupted leads to rod nuclei misplacement. These data add to the current understanding of contribution of different Arl3 variants causing human retinal degeneration, which has strong potential translational implications.

Strengths:

Relevance of Arl3 dominant variants to human retinal degeneration. Identification of Y90C variant as a "fast cycling" GTPase, and not as a predicted destabilizer of the protein structure.

New method of crosslinking to enable snapshots of endogenous protein-protein interactions.

Weaknesses:

• The relevance of this study is justified by the fact that newly identified dominant variants of Arl3 have been associated to retinal degeneration. However, the authors never assess a degeneration phenotype.

Electroporation technique allows for rapid expression of constructs, but the sparse expression makes it a poor means to study retinal degeneration. This is important to examine in the future using robust genetic mouse models.

• The authors show new dominant variants of Arl3, namely Y90C and D67V, cause rod nuclear mislocalization. This phenotype is interesting but this was previously observed with other constitutively active mutation of Arl3, Q71L, and therefore is not novel.

Yes, the Q71L paper is well cited in our manuscript and set the basis for many of our experiments.

• The main claim of this paper is that subcellular compartmentalization of Alr3 activation to the cilium (the so called gradient by the authors) is required for proper rod nuclear migration to their final outer nuclear layer destination. The authors provide multiple experiments to support this model, but this is never directly demonstrated.

We are not aware of any methods that could be done to directly show the subcellular localization of active Arl3-GTP within rod photoreceptors. We agree that we have provided many experiments that support our hypothesis that altering the Arl3-GTP gradient between cilium and cell body produces a nuclear migration defect. Some of our favorites include Fig 6, where we find that the migration phenotype is only rescued with expression of ciliary cargos and not rescued by non-ciliary cargos. Also, the new data requested by reviewers showing Arl13B expression in the cilium can restore the Y90C defect further supports that the Arl3 ciliary gradient is necessary for proper nuclear migration.

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Reply to the reviewers

Manuscript number: RC-2022-01707

Corresponding author(s): Sarah Butcher, Richard Lundmark

1. General Statements [optional]

We thank the reviewers for their insightful comments. The inclusion of the points raised by the referees have strengthened the manuscript. However, some of the reviewer suggestions are beyond the scope of the work (see below), but will doubtlessly be touched upon in future studies by the authors. In addition to incorporating changes relevant to answering the reviewers’ comments, we have edited the manuscript for increased clarity and precision.

2. Description of the planned revisions

1. Liposome flotation assay Reviewer #1 suggested that we should perform a liposome floatation assay to separate possible C protein aggregation from membrane binding: "I would strongly recommend supplementing the current liposome sedimentation assay by liposome flotation assay. In contrast to liposome co-sedimentation, the flotation assay can discriminate protein aggregates from proteins bound to liposomes. Although the SDS PAGE shown in Fig. 1A looks pretty convincing, a faint protein band in the „P" lane of the middle panel for the (-) sample is evident. Therefore, C protein aggregation cannot be ruled out and it would be indistinguishable from liposome binding examined by mere co-sedimentation assay”

Response: We agree that this is a necessary control experiment to add, and we will perform it with liposomes containing 40 % POPS. As we detected complete C protein co-sedimentation with this lipid composition, performing the flotation experiment with the same composition will prove that the earlier result indicates lipid binding and not protein aggregation.

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

1. Reviewer #1
2. “In addition, it needs to be clarified which TBEV C protein construct, whether full-length or truncated, was used for co-sedimentation fragmentation.”

Response: We have clarified in this section of the manuscript that the full-length C protein construct was used for the liposome co-sedimentation assays by adding “full-length” prior to instances of “C protein” e.g. in the paragraph starting line 118.

1. “How to understand the finding that „the C protein forms a very rigid layer when adsorbed to the membrane". Can the aggregation of C-protein be ruled-out? Following the 1M NaCl wash of C-protein-bound to SLB, the authors stated: „This shows that initial membrane recruitment of C protein is strongly dependent on its interactions with the negatively-charged lipid headgroups. However, once bound, the C protein-membrane interaction is complemented with non-electrostatic interactions such as membrane insertion or protein oligomerization": does it mean that there are several layers of C protein, the first held by electrostatic interactions, overlayed by non-electrostatically bound C protein? If yes, the illustration of single-layered C-protein adsorbed onto SLB in Fig. 2A, B is not correct. ”

Response: We understand the confusion regarding the term “rigid” which was used as a way to describe how we interpret the relatively minor change in the dissipation upon membrane binding. What we intended to describe was that this indicates that the protein is attached in a stable way that does not add viscoelastic properties to the system. These data indicate that the protein does not form large aggregates that non-specifically attach to the membrane in different protrusive orientations. We have clarified this in the manuscript and specified that the as there is no dissipation change, there is no aggregation. We added the following to line 168 “This, in turn, indicates that the C protein does not bind as non-specific aggregates as these would have changed the viscoelastic properties of the system.”

We do not mean that there are several layers of C protein. We consider, due to the highly charged nature of C, that the most likely explanation is that there are multiple modes of C binding but the result is only one layer, with multiple C-proteins interacting with each other within that layer. We have modified the text at line 184 to: “However, once bound, the C protein-membrane interaction is complemented with non-electrostatic interactions such as membrane insertion or protein oligomerization within the bound layer.”

1. “The sentence: “To confirm that the C protein is biologically active, we investigated its ability to bind RNA" seems to be a little odd because it suggests the model membrane binding assays do not require biological active proteins. However, considering that the interactions leading to binding either negatively-charged lipid or negatively-charged RNA are electrostatic - this sentence must be rewritten.” Response: We thank the reviewer and have now rephrased this sentence to the following at line 249 “Since RNA binding is crucial for the NC assembly, we investigated the C protein’s ability to perform this function.”

2. “The authors´ statement in the Abstract: „....we investigate nucleocapsid assembly..." is too speculative because the assembly was not studied in their work. It needs to be reformulated.” Response: We agree, and the statement has been removed from the abstract.

3. “Despite this clear and valuable methodological contribution, the authors' contribution to our knowledge of the coordination of the nucleocapsid components to the sites of assembly and budding is not so obvious. Contrary to the earlier idea that the flavivirus is asymmetrically charged (that is, hydrophobic on one side (α2) and positively charged on the other side (α4), recent studies show that the entire surface of the protein is highly electropositive (Mebus-Antunnes et al., 2022). Therefore, a well-ordered neutralization of the flaviviral C proteins' highly positive surface seems critical for the proper organization and assembly of nucleocapsid. I am afraid that the authors do not shed much light on this issue.” Response: The recent structure of the TBEV C protein, published after we submitted the manuscript, shows that indeed the C protein is highly positively charged on all surfaces (updated Supplementary Figure 1 and Selinger et al., 2022). The recruitment of C protein to the membrane, that we demonstrate is dependent on negatively-charged head groups, provides a biologically relevant mechanism for charge neutralization on the C protein surface that interacts with the lipids. The remaining surface charge can be then neutralized by RNA recruitment. Mebus-Antunnes et al. made their observations with just RNA and C protein from Dengue virus in the context of artificial surfaces e.g. mica. However, our experiments utilize the TBEV C protein and specifically include a membrane, the third critical component of NC assembly. Thus, we build upon the work of Mebus-Antunnes et al. by adding a second biologically relevant charge-neutralising component and comparing with a distantly-related virus. We have changed the discussion section of the manuscript to reflect this new structure and to emphasize the advance here. Starting from line 371 we changed the text to: “Recently, it has been shown that the neutralization of the C protein surface positive charge is important for RNA binding in the distantly-related Dengue virus (DENV) (Mebus-Antunes et al, 2022). The recruitment of C protein to the membrane, that we demonstrate is dependent on negatively-charged head groups, provides a biologically relevant mechanism for charge neutralization on the C protein surface that interacts with the lipids. The remaining surface charge can be then neutralized by RNA recruitment.”

Reviewer #2 1. “What results demonstrate C protein inserts into membrane? The current results support the C protein interacts with membranes with positive charge, but do not seem to demonstrate membrane insertion. If the C protein inserts into the membrane, which regions (helices) play this role?”

Response: The Langmuir-Blodgett trough tensiometry experiments with monolayers directly measure the insertion of a protein into the monolayer. By determining the maximum insertion pressure of the C protein constructs, we also show that the membrane insertion can occur in bilayers. We show that the N-terminus is not inserting into the membrane, further work, beyond the scope of this manuscript, is needed to pinpoint the residues responsible for insertion, for instance by hydrogen-deuterium exchange or FRET measurements that would not affect folding. To clarify the use of the LB trough, we added the following at line 216: “To investigate if the C protein membrane binding includes insertion into the membrane after the initial electrostatic binding, we used Langmuir-Blodgett trough monolayer experiments. In this approach, the insertion of a protein into a lipid monolayer can be detected by following the pressure (π) of the monolayer after protein injection into the aqueous subphase, with increases in π corresponding to protein injection (Brockman, 1999; Liu et al, 2022).“

1. “The authors should discuss several previous papers reporting the effect of partial deletions of the C gene on the replication of TBEV, West Nile virus, and other flaviviruses.” Response: We agree that this is a necessary addition, and have now added a paragraph in the discussion section starting at line 333: “N-terminally truncated flaviviral C proteins have been shown to be assembly competent and in vitro, able to bind RNA, which is consistent with our results with N-terminally truncated TBEV C protein (Khromykh & Westaway, 1996; Kofler et al, 2002; Patkar et al, 2007; Schlick et al, 2009). One role of C is in the modulation of host responses to infection and the N-terminus maybe involved in that (Yang et al, 2002; Limjindaporn et al, 2007; Colpitts et al, 2011; Bhuvanakantham & Ng, 2013; Katoh et al, 2013; Urbanowski & Hobman, 2013; Samuel et al, 2016; Slomnicki et al, 2017; Fontaine et al, 2018). The membrane insertion directly detected in our experiments is central to C protein function. Other studies have found that deletions in the hydrophobic region of the α2 helix significantly impair particle assembly (Kofler et al, 2002; Patkar et al, 2007; Schlick et al, 2009). In the light of this evidence, we consider that the α2 helix could be responsible for membrane insertion (Markoff et al, 1997; Kofler et al, 2002; Nemésio et al, 2011, 2013).”

Reviewer #3 1. “In Figure 4, the band (256:1) that are supposedly in the wells (red arrow) is not clear- it is only slightly darker than the other wells.”

Response: This confusion was the result of unclear wording. We have now revised the figure legend at line 278 to : “The black arrow indicates the bands of freely-migrating RNA, and the red arrow the wells. On lanes 624:1 and 256:1, RNA has been immobilized in the wells.”

1. “Figure S1A, the N-terminal end (which is truncated in the mutant) should be colored on the cyan molecule.” Response: We have coloured the truncated part of the cyan molecule in the figure (now S1B) according to the reviewer’s comment.

Other 1. As the nuclear magnetic resonance structure of the truncated TBEV C protein has recently been released (Selinger et al, 2022), we have updated the manuscript and Figure S1 to include the information from this structure. We have also generated a new homology model of the full-length TBEV C protein using this structure as a template and included that in Figure S1.

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

1. Reviewer #1
2. “However, we do not know whether in the infected cells, the C protein is pre-bound to ER membrane or to viral RNA. Having such a unique assay in their hands, I wonder whether the authors could use the pre-bound C protein with genomic RNA (i.e. the experiment shown in Fig. 4A) ribonucleoprotein complex in the SLB binding assay. If doable, this experiment would be exciting and could bring some important information about NC assembly.”

Response: We agree that it would be very interesting to decipher if the C-protein first binds to RNA or to membranes using the QCM-D methodology. Yet, our data on pre-incubated C-protein and RNA suggests that large aggregates are formed which would hamper the interpretation of the QCM-D data. Furthermore, based on the suggested experiment, we will not be able to firmly conclude whether or not the C-protein first binds to RNA or to membranes since the time of the experiment will allow rearrangement of preformed complexes between C-protein and RNA. Additionally, the QCM-D measurement cannot differentiate if the preformed complexes bind on their own, or if excess unbound C protein binds the membrane and then recruits the complex. Therefore, addressing this question would require major adjustments to the RNA model system and methodology that we feel are beyond the scope of this study.

Reviewer 2 1. “The authors should use the lipids detected in the virions to confirm C protein binding experiments.”

Response: In the mass spectrometry characterization of the TBEV virions, we detected lipids from 9 classes (Car, PE, PS, PI, PG, PC, Cer, HexCer & TG). We have tested four of them (PE, PS, PI, PC) in the liposome sedimentation assay. Additionally, we tested GalCer, which, like HexCer, are cerebrosides. Our liposome binding experiments clearly demonstrate that the C protein does not bind to a specific lipid class, but instead to lipids with negatively-charged headgroups. Therefore, we would argue that doing additional sedimentation experiments with Car, PG, Cer, and TG would not add extra insight to the manuscript.

Additionally, while the population of lipid species in the TBEV envelope is diverse, the diversity mostly comes from differences in the lipid tails, which do not generally affect the head group-mediated binding of proteins. Therefore, performing additional lipid binding experiments with varying tail lengths would not likely lead to new observations.

Finally, to perform the authentic experiment of testing C protein binding to liposomes formed from lipids extracted from purified virions would require orders of magnitude more virus sample than our research laboratory is capable of producing. Therefore, we argue that this experiment is beyond the scope of this study.

1. “The study may be strengthened by performing virus mutagenesis experiments.” Response: While we agree that, ultimately, experiments on virus and cells would help to understand the role of the C protein in the biological context, we think these experiments are beyond the scope of this study. For virus mutagenesis, candidate residues should be first identified with biochemical and biophysical studies, which is already beyond the scope of this work. Additionally, the C protein has multiple functions in the host cell in addition to NC assembly, and interpreting the effect on the mutations on e.g. virus titer is difficult.

Reviewer #3 1. “In all figure legends, authors should write a conclusion line after the description of the experiments - what conclusion is drawn from each experiment.”

Response: While we agree that adding such a conclusion line would make it easier for the reader to understand each figure, the format of the figure legends is highly subject to journal policy. Therefore, we think that the addition of such lines will be an editorial decision and will depend on the journal. We have, however strived to make the figure titles as informative as possible in lieu of such concluding lines.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the author characterizes the lattice of kinesin-decorated microtubule reconstituted from porcine tubulins in vitro and Xenopus egg extract using cryo-electron tomography and subtomogram averaging. Using the SSTA, they looked at the transition in the lattice of individual microtubules. The authors found that the lattice is not always uniform but contains transitions of different types of lattices. The finding is quite interesting and probably will lead to more investigation of the microtubule lattice inside the cells later on for this kind of lattice transition.

The manuscript is easy to read and well-organized. The supporting data is very well prepared.

Overall, it seems the conclusion of the author is justified. However, the manuscript appears to show a lack of data. Only 4 tomograms are done for the porcine microtubules. Increasing the data number would make the manuscript statistically convincing.

One tomogram can contain one to several tens of microtubules. For example, 64 microtubules were analyzed in the Xenopus-DMSO dataset obtained on 5 tomograms, versus 24 microtubules for the GTP-dataset obtained on 4 tomograms (see Table 1). Hence, taking the number of tomograms to assess the statistical relevance of our work cannot be considered as a valid criterion. Tomograms are taken randomly on the EM-grid sample, solely based on ice quality and the covering of microtubules in the holes as determined at low magnification before tomographic acquisition. No prior knowledge of the structure and lattice-type organization of the microtubules can be obtained before acquisition. It appears to us that a more pertinent criterion is the number of events that we characterized, specifically lattice-type transitions along individual microtubules. In the dataset mentioned by the referee (see Figure 2-figure supplement 3-4 and Table I), 24 microtubules were analyzed and further divided into 195 segments, providing an equivalent number of individual 3D reconstructions. For each 3D reconstruction, almost all lateral interactions could be characterized in terms of lattice-type, i.e., 2091 of the B-type, 460 of the A-type, and 112 not determined (essentially at transition regions). Most importantly, we document in this specific dataset 119 transitions in lattice-type, which we think is sufficient to characterize such molecular events and provide solid statistics for this dataset. Adding the GMPCPP and Xenopus data, we end-up with 938 individual 3D reconstructions (not including the full-length microtubule volumes), 12 463 lateral interactions analyzed (A-, B-, or ND-type), and the observation of 172 lattice-type transitions. Therefore, we respectfully disagree with the referee stating that our work lacks data.

To highlight the quantity of data used in our work, we have modified the following sentences: L124-131: ' Analysis of 24 microtubules taken on 4 tomograms, representing 195 segments of ~160 nm length (i.e., 2664 lateral interactions), allowed us to characterize 119 lattice type transitions with an average frequency of 3.69 µm-1 (Table 1), but with a high heterogeneity' L160-164: ' Analysis of 31 GMPCPP-microtubules taken on 6 tomograms, representing 338 segments of ~150 nm in length (i.e., 3236 lateral interactions), and using the same strategy as in the presence of GTP (Figure 5—figure supplement 1-2) revealed a transition frequency of 1.25 µm-1 (Table 1), i.e., ~3 fold lower than microtubules assembled in the presence of GTP.' L200-203: ' A total of 64 microtubules taken on 5 tomograms were analyzed in the Xenopus-DMSO dataset (i.e., 419 segments from which we characterized 5446 lateral interactions), and 15 microtubules taken on one tomogram for the Xenopus Ran-dataset (i.e., 86 segments from which we characterized 1118 lateral interactions), (Table 1).'

In addition, having the same transition with the missing wedge orientation randomly from different subtomograms will allow a better average of transition without the missing wedge artifact.

In this work, we did not aim at averaging transitions. Transitions in lattice-types are highly heterogeneous in nature, and we wonder what additional information an averaging strategy would have provided. Conversely, each transition is a unique event that we characterized to obtain useful statistics, and the missing data at high angle inherent to electron tomography were not an obstacle to fulfill this task.

Another thing that I found lacking is the mapping of the transition region/alignment in the raw data.

In Figure 4, we clearly show the correspondence between the segmented sub-tomogram averages (SSTA) and the raw filtered images at the transition region. This is also the case in Figure 5 where the SSTA (Figure 5A) are compared with the raw tomogram (Figure 5B), and where we clearly visualize the holes that result from the transitions in lattice types.

However, it is not easy for me or the reader to understand how each segment is oriented relative to each other apart from the simplified seam diagrams in the figures, and also the orientation of the seam corresponding to the missing wedge in the average. With these improvements, I think the conclusion of the manuscript will be better justified.

The segmentation process is explained in Figure 2-figure supplement 2 and in the Materials and Methods section, which shows that each segment is linearly related to the next. Small rotations can happen between individual segments, and it is important to check that the same protofilaments are followed during the initial modeling (see the online tutorial referenced in the manuscript for full-length microtubules). The segment models are derived from that of the full-length microtubule, as explained in the Materials and Methods section, using a new routine (splitIntoNsegments) implemented into the PEET program. In addition, a detailed protocol describing our SSTA strategy will be submitted following publication of our manuscript.

Reviewer #2 (Public Review):

Differences in protofilament and subunit helical-start numbers for in vitro polymerized and cellular microtubules have previously been well characterized. In this work, Guyomar et al. analyze the fine organization of tubulin dimers within the microtubule lattice using cryo-electron tomography and subtomogram averaging. Microtubules were assembled in vitro or within Xenopus egg cytoplasmic extracts and plunge frozen after addition of a kinesin motor domain to mark the position of tubulin dimers. By generating subtomogram averages of consecutive sections of each microtubule and manually annotating their lattice geometry, the authors quantified changes in lattice arrangement in individual microtubules. They found in vitro polymerized microtubules often contained multiple seams and lattice-type changes. In contrast, microtubules polymerized in the cytoplasmic extract more frequently contained a single seam and fewer lattice-type transitions.

Overall, their segmented subtomogram averaging approach is appropriately used to identify regions of lattice-type transition and quantify their abundance. This study provides new data on how often small holes in the lattice occur and suggests that regulators of microtubule growth in cells also control lateral tubulin interactions. However, not all of the claims are well supported by their data and the presentation of their main conclusions could be improved.

1 - We have corrected approximative claims and conclusions where necessary. In particular, we now discuss separately the Xenopus-DMSO and the Xenopus-Ran egg extract samples, and have modified our conclusions accordingly. We also deposited onto the EMPIAR all tomograms and PEET models to reproduce the 938 segmented sub-tomogram averages analyzed in this study (see new Supplementary file 2).

Reviewer #3 (Public Review):

Protofilament number changes have been observed in in vitro assembled microtubules. This study by Guyomar and colleagues uses cryo-ET and subtomogram averaging to investigate the structural plasticity of microtubules assembled in vitro from purified porcine brain tubulin at high concentrations and from Xenopus egg extracts in which polymerization was initiated either by addition of DMSO or by adding a constitutively active Ran. They show that the microtubule lattice is plastic with frequent protofilament changes and contains multiple seams. A model is proposed for microtubule polymerization whereby these lattice discontinuities/defects are introduced due to the addition of tubulin dimers through lateral contacts between alpha and beta tubulin, thus creating gaps in the lattice and shifting the seam. The study clearly shows quantitatively the lattice changes in two separate conditions of assembling microtubules. The high frequency of defects they observe under their microtubule assembly conditions is much higher than what has been observed in vivo in intact cells. Their observations are clear and supported by the data, but it is not at all clear how generalizable they are and whether the defect frequencies they see are not a result of the assembly conditions, dilutions used and presence of kinesin with which the lattice is decorated. The study definitely has implications for mechanistic studies of microtubules in vitro and raises the question of how these defects vary for protocols from different labs and between different tubulin preparations.

1 - High tubulin concentration: It has been documented by many laboratories since the discovery of tubulin and the characterization of its assembly properties that a sufficient concentration of free tubulin is necessary to self-assemble microtubules. This is called the critical concentration for self-assembly (the CC, i.e., the critical concentration to overcome the nucleation barrier), and has been reported to be in the range 14~25 µM in the presence of GTP depending on laboratories. For example, in the seminal work of Mitchison and Kirschner the CC was estimated at 14 µM (Fig. 5 of ref. (Mitchison & Kirschner, 1984b)) and self-assembly was induced at concentrations in the range 32-59 µM (Mitchison & Kirschner, 1984a). Our own estimate of the CC for porcine brain tubulin was 21 µM (Fig 2C of (Weis et al., 2010)), and we routinely use a tubulin concentration slightly above the CC when we aim at robust microtubule self-assembly. Hence, we argue that 40 µM, which is ~twice the CC, cannot be considered as a "very high" tubulin concentration to induce microtubule self-assembly.

2 - Protofilament number and lattice-type transitions in cells: While microtubules with protofilament numbers different than 13 have been observed in different cell types and species (reviewed in (Chaaban & Brouhard, 2017)), we are aware of only one recent study where changes in protofilament numbers along individual microtubules have been reported in cells (Foster et al., 2021), but with no statistics concerning their frequencies. Hence, we cannot compare changes in protofilament number frequencies in Xenopus egg extracts with those that occur in intact cells. Concerning lattice-type transitions, we are not aware of any previous study that documented such features, whether in vitro or in cells.

3 - Generalization of our results, source of tubulin and protocols: Multi-seams in microtubules assembled in vitro have been reported by several groups in the past (see our Introduction, L49-62), starting from (Kikkawa et al., 1994), the Milligan group (Dias & Milligan, 1999; Sosa et al., 1997), and more recently by the Sindelar group (Debs et al., 2020). In Kikkawa et al. (1994), the authors purified tubulin from porcine brain by three cycles of assembly/disassembly followed by phosphocellulose chromatography. Assembly was carried out at 24 µM in the presence of Taxol. In Sosa and Milligan (1996-1997), the authors used a commercial source (Cytoskeleton) and assembled the microtubules at 30 µM in the presence of Taxol. In Debs et al. (2020), the authors used tubulin purified from porcine brain according to (Castoldi & Popov, 2003), as we did, to assemble GMPCPP microtubules, and bovine brain tubulin (Cytoskeleton) to assemble Taxol-stabilized microtubules. Noticeably, they used an initial tubulin concentration of 100 µM to initiate microtubule polymerization and then added Taxol to continue the reaction.

We add to these previous studies that microtubules with different numbers of seams are not unique ones, but that both the number and location of seams can vary within individual microtubules. The reason why this was not observed before is that the analytical tools used in those previous studies were not suited to reveal this structural heterogeneity within individual microtubules. By contrast, the SSTA approach that we designed was specifically developed towards this aim. Even in the recent work by Debs et al. (2020) that provides the most comprehensive characterization of multi-seams in microtubules assembled in vitro and that obtained a seam distribution very similar to ours (compare their Figure 3C with our new Figure 10C for GDP microtubules, dark blue bars), their protofilament-based approach could not reveal changes in the number and location of seams within individual microtubules. Yet, they probably could have done it if they had asked whether segments with different seam numbers had been extracted from the same microtubules.

Here, we designed a specific approach to tackle the structural heterogeneity of individual lattices that permitted this discovery. Not only do we confirm results obtained by others, but we also propose a molecular mechanism that explains how multi-seams form in microtubules assembled in vitro and how they change in location in a cytoplasmic environment. By doing so, we propose a novel molecular event - formation of unique lateral interactions without longitudinal ones - that was not envisioned before, and which to our opinion, must be incorporated in further modelling studies concerning microtubule nucleation and assembly, including the mechanism of dynamic instability (see the Ideas and speculation section).

4 - Dilution: A 50X dilution was used only for Xenopus egg cytoplasmic extracts to decrease their density on the EM grid just before freezing. These conditions were settled by cryo-fluorescence microscopy to ensure that we had the adequate density of microtubules onto the EM-grid (Figure 7 and Figure 2—figure supplement 1D). Of note, the microtubules analyzed by SSTA were assembled in extracts that were not supplemented with fluorescent tubulin. While we could imagine that dilution may induce the removal of dimers from the microtubule lattice, we cannot foresee how this could change the register between tubulin subunits within the microtubule lattice.

5 - Kinesin decoration: Like many other laboratories (see the Table in Figure 3 of (Manka & Moores, 2018)), we use the non-processive motor domain of kinesin 1 to decorate microtubules, with the aim to differentiate the - and -tubulin monomers within the microtubule lattice. In particular, it has been shown that lattice parameters such as the protofilament skew and lattice spacing are unmodified when kinesin motor domains are added to GMPCPP- or GDP-microtubules (Zhang et al., 2015, 2018). In addition, we cannot envisage how this non processive motor added to preformed microtubules could change the registry of the -tubulin heterodimers within the microtubule lattice.

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Reply to the reviewers

Overall comments

We are pleased by the reviewers’ comments and appreciate their suggestions for improvements. In addition to correcting small typos throughout the manuscript, the major changes we did in response to their comments are as follows:

• Changed the title of our paper to reflect the strong evolutionary correlation more accurately between sex chromosomal meiotic drive and gains/losses of SNBP genes in
• New experiments to test the role of the well-conserved, universally retained SNBP, CG30056, in male fertility in * melanogaster*. Although reviewers had suggested we could eliminate this section, we felt that this would add a lot of weight to the unexpectedly inverse relationship between age/retention and fertility functions of SNBP genes. Thus, over the past few months, we have carried out new experiments with increased sample sizes, better controls, and sperm exhaustion. These new results strengthen our earlier analyses.
• Better clarification of the X-Y chromosome fusion, which is a new observation, in the montium group via careful rewriting as partly suggested by Reviewer #2.

• Highlighting that the genetic conflicts hypothesis does not rule out a role for sperm competition or other conflicts in shaping SNBP evolution in a revised Discussion. All changes in response to the reviewer’s comments have been detailed in our point-by-point response (below). You will see that we have addressed almost all the suggestions made, including with new experiments. The only reviewer suggestions (all optional from Reviewer 3), which we did not directly address in our revision are:

• __Branch specific protamine evolution analyses for sex chromosome amplified SNBP genes: __given the state of SNBP gene annotation and the difficulties of assembling these genes in large tandem arrays, this will require considerable work and is beyond the scope of the paper.

• Covariation between SNBP evolution and sperm morphology: We cannot perform these experiments as there is a paucity of sperm morphology data currently. Obtaining this data reliably is a significant undertaking.
• Are SNBP genes more prone to be lost than average in the montium group: We have not comprehensively examined all loss events in the montium group or any other Drosophila This is also a non-trivial analysis, albeit it would be very interesting. However, we believe the more relevant comparison is whether these lost SNBP genes are more likely to be retained in non-montium species, which they are, as we now highlight. We hope you will favorably judge our good faith efforts to address all other reviewers’ comments, and their laudatory comments during the previous round of reviews.

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

Chang and Malik present a comprehensive evolutionary analysis of sperm nuclear basic proteins (SNBPs) in Drosophila. In addition, they provide a preliminary functional characterization of one such protein (CG30056) and describe a newly discovered X-Y chromosomal fusion in the Drosophila montium species group. All of these findings are interesting and important, but the headline from this study is the well-supported possibility that SNBPs, or at least a large fraction of them, function in suppressing X vs. Y chromosome meiotic drive. While this hypothesis is challenging to test experimentally, the authors provide strong correlational evidence that SNBPs are associated with drive by documenting these proteins' rapid evolution. This rapid evolution takes the form of sequence changes (as predicted by coevolution between drivers and suppressors of drive), gene amplification in cases when SNBPs move to sex chromosomes (consistent with the SNBP becoming a potential agent of drive for its new "home chromosome"), and gene loss in species with X-Y chromosome fusions (in which drive is not predicted to occur).

Overall, this is an excellent, comprehensive study. The phylogenetic and genomic analyses are first-rate (and one of the first to make use of the new 101 Drosophila genomes); the logic is very well explained; conclusions are supported by multiple lines of evidence; the writing and figures are clear and accessible; and, the findings are fascinating. It's a good sign that it is easy to imagine several experiments one could do to follow up on this study, but I do not feel any are required in revision, as the manuscript is comprehensive as is. Thus, I have just a few minor points the authors may wish to consider in making revisions and a few suggestions for clarity/typos.

__

We thank the reviewer for their positive comments on our work.

1. I would be interested in whether the authors think that all SNBPs in a given Drosophila species function(ed) in meiotic drive, or whether some fraction may play other roles, such as sexual selection or chromatin compaction, which have been the traditional hypotheses for SNBP function. Relatedly, given the high turnover of SNBPs the authors observe and the fact that some melanogaster-essential SNBPs are younger genes, would they like to comment on whether the subsets of SNBPs involved in drive/suppression vs. chromatin packaging/sperm traits/Wolbachia defense are likely to differ from across fly species? The reviewer raises an excellent point. In our revised discussion, we now speculate that different SNBPs might have distinct functions. For example, the same subset of SNBPs is subject to gene amplification and loss whereas other SNBPs are subject to less turnover. Moreover, even this stable set of SNBPs evolves rapidly, including in the montium group of species that have undergone dramatic SNBP loss. As the reviewer suggests, sperm competition or pressures from Wolbachia toxins might be is a driving force for sperm evolution. We discuss these possibilities and conclude in our discussion: “Our findings do not rule out the possibility that forces other than meiotic drive are also important for driving the rapid evolution and turnover of SNBP genes in Drosophila species.”

What do the authors make of the lower isoelectric points for a few of the SNBPs (e.g., CG31010 with pI = 4.77 in Table 1)? These proteins have identifiable HMG box domains, so is the pI driven lower by other parts of the protein sequence?

We thank the reviewer for raising this point. We found that the pI of HMG domains can range from 6 to 12. Thus, the pI is driven by both HMG domains and other parts of proteins. We now include the pI of the whole SNBP protein and the HMG domain alone in Table 1. We do not have enough biochemical information to speculate on how these differences could alter SNBP function.

__3. For readers less familiar with the field, it may help to spell out (e.g., on p. 6) why the authors consider ProtA/B to be important for fertility. Some of the previous papers on these genes describe them as dispensable - though the present authors are correct that these previous studies do detect fertility defects of various magnitudes under some conditions.

__

We agree with the reviewer. Previous studies are in disagreement about the importance of ProtA/ProtB for male fertility- while no significant effects were seen under standard fertility assays, sperm exhaustion conditions (mating with excess females) did reveal fertility effects. We have now added these references and discussed ProtA/ProtB more fully in our revision.

On p. 9, paragraph 2, the data showing that "six different SNBP genes underwent 11 independent degeneration events in the montium group" are shown in Fig. 6A, not 5A.

Thank you. This has been fixed in our revision.

5. The summary Table 2 is useful, but I wonder whether including relative levels of expression and dN/dS in addition to ordinal rankings might help clarify. For instance, if there were a drop off in mean expression level between the 5th and 6th most highly expressed SNBP, this wouldn't be evident from the table.

We agree with this suggestion and have now added this information.

In Fig. 3, I like the use of the clean CG31010 figure in panel A to illustrate the circular representations. In addition, though, it might be useful to show Prot's graph at this same, larger size, since it's the most complicated and will likely be most closely examined.

We agree with this suggestion and have now amended this figure in line with the reviewer’s suggestion.

In Fig. 4, the end of the legend says that the species tree is shown "on the right," but it's on the left in the figure.

Thank you. This has been fixed in our revision.

__CROSS-CONSULTATION COMMENTS • I agree with both Reviewers 2 and 3 that the title could be changed to be a bit more tentative. I'd had this thought as well.

__

We agree with this suggestion. We have now amended this title to “Expansion and loss of sperm nuclear basic protein genes in Drosophila correspond with genetic conflicts between sex chromosomes.”

• I agree with Reviewer 2 that the fertility assay could be conducted with a larger sample size and a better control in order to be better compared with how the authors described other published fertility phenotypes for SNBPs. For the control, crossing the deletion line to y w (or w1118) and using the resulting heterozygotes (KO/+) would be better than using the mutation over the balancer chromosome (KO/CyO). We agree with both suggestions. We now compare fertility between KO/KO and KO/+ males in sperm exhaustion assays. Our more stringent fertility assays find no evidence of CG30056 role in male fertility, strengthening our previous findings. We have now added the motivation for the new assays and the new results to our Revision.

• I agree with Reviewer 3's third bullet point about spending a bit more time on the different possible roles that SNBPs could play in spermatids. (This is a more eloquent version of my review point #1.)

We have now expanded our discussion of other possibilities in our revision.

• I agree in principle with Reviewer 3's first bullet point about examining whether SNBP evolution correlates with changes in sperm morphology, but this feels like it could be a whole, fascinating study on its own, while this manuscript is already packed with data. I'd welcome the authors' thoughts about this in discussion, but wouldn't personally require a formal analysis of this to be added prior to publication.

We also agree that this would be an interesting test. However, we are not able to do the test due to the scarcity of sperm phenotype data in Drosophila. We also think that our original version unintentionally downplayed this possibility. Our revised discussion makes clear that the rapid evolution of some Drosophila SNBP genes may be driven by sperm competition, just as in mammals, and influence the evolution of sperm morphologies.

__Reviewer #1 (Significance (Required)):

This study describes an important conceptual advancing in our understanding of the evolution and potential functions of sperm nuclear basic proteins (SNBPs) in Drosophila, which stands in interesting contrast to the functional roles of equivalent proteins in primates. It should be of broad interest to biologists studying spermatogenesis, meiotic drive, and genome evolution, both in and out of Drosophila. __

We thank the reviewer for their positive appraisal.

__ To contextualize the work, paternal DNA is typically compacted during spermatogenesis. This process involves the replacement of histones with other small, positively charged proteins in a sequential order, ending with protamines that bind DNA in mature sperm. In Drosophila, work over the last two decades (largely from the labs of R. Renkawitz-Pohl, B. Loppin and B. Wakimoto) has identified more than a dozen sperm nuclear basic proteins that localize to condensing/condensed spermatid nuclei. Two interesting observations have been that many of these proteins are dispensable for male fertility, and the proteins vary in their degree of evolutionary conservation. Recent work from Eric Lai's lab (J Vedanayagam et al. 2021, Nat Ecol Evol) showed that in D. simulans and sister species, at least one of these SNBP genes (Prot) underwent gene amplification and now acts in those species as a meiotic driver. This finding suggested the hypothesis, tested thoroughly in the present study, that the rapidly evolving SNBP gene family could be involved in causing or suppressing meiotic drive. Consistent with this idea, the authors here find that SNBP genes expand in copy number more frequently when they move from autosomes to sex chromosomes (consistent with the idea that they may cause or contribute to drive), and that otherwise well-conserved SNBP genes are lost in a group of species in which sex chromosome meiotic drive is not expected to occur. These findings are based on a thorough and well conducted phylogenomic and molecular evolutionary analysis of SNBPs across dozens of Drosophila species. Overall, this work generates exciting new hypotheses about the function of SNBPs and should be widely read both within and outside of the field.

__

We are grateful for the reviewer’s accurate summary of our work and its significance. We share the reviewer’s excitement and expect that more studies will explore the new function of SNBPs in multiple taxa soon.

Keyword describing my field of expertise: Drosophila, molecular evolution, reproduction, genetics, genome evolution.

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

The paper describes interesting patterns on the evolution of Drosophila SNBP genes, and proposes a very interesting explanation, namely, that meiotic drive is the main evolutionary force behind these patterns. Some of these observations have recently been made by other authors in a single case (the Dox genes in D. simulans), but not in the scale and breadth of the present ms. The ms combines an extensive investigation of available genomes with expert analysis, and new experimental data. In particular, the finding that the ancestral Y became incorporated into de X in montium species is very exciting, and may provide a smoking gun for the explanation proposed by the authors. Overall, I think it is a very good paper. I do have several criticisms and suggestions that may help to improve it.

__

We are grateful for the positive comments of the reviewer and for their constructive criticism and suggestions, which we have incorporated into our revision.

__The paper has a speculative side that it almost unavoidable given its novelty and breadth. I do not see this as a problem per se, but I think the uncertain/unsupported/problematic points should be more openly presented to the readers. The main cases I noted are:

1. The title of the ms states that "Genetic conflicts between sex chromosomes drive expansion and loss of sperm nuclear basic protein genes in Drosophila", but the evidence is somewhat circumstantial, and the patterns may be explained also by other known phenomena (e.g., demasculinization of the sex chromosomes; below). I think the tone of the end of the Introduction reflects more faithfully the strength of the evidence ("Thus, we conclude that rapid diversification of SNBP genes might be largely driven by genetic conflicts between sex chromosomes in Drosophila."). I understand the temptation of writing a bold title, but I think it is a bit misleading in the present case. I.e., it would be desirable that the title conveys the uncertainties of the data and their interpretation. __

We agree with this suggestion. We have now amended this title to “Expansion and loss of sperm nuclear basic protein genes in Drosophila correspond with genetic conflicts between sex chromosomes.”

However, we also want to highlight that de-masculinization of the X chromosome cannot explain the observed amplification and loss patterns of SNBP genes, except in cases of sex chromosome fusions. We now highlight the de-masculinization hypothesis for the latter case, but still strongly favor the genetic conflicts hypothesis.

"In contrast, we found no instances of pseudogenization or subsequent translocation to the X chromosome of SNBP genes that are still preserved on their original autosomal locations or involved in chromosome fusions between autosomes (0/16). This difference is highly significant (Fig 5 and Table S11; 3:5 versus 0:16, Fisher's exact test, P=0.03). " Readers should be warned that this pattern can also be explained by the well-known demasculinization of X chromosomes (e.g., Sturgill et al. Nature 2007, 450, 238-241)

We agree with this point and thank the reviewer for pointing this out. We now expressly raise the ‘de-masculinization of X chromosomes’ as one potential explanation of the pattern we observe here.

"Indeed, no meiotic drive has been documented in the montium species even though it is rampant in many other Drosophila lineages [38]." Two remarks here: a) the authors should make clear that they are referring to sex-chromosome meiotic drive. b) I think the evidence is much weaker than the sentence implies. Sex-chromosome meiotic drive is known in less than 20 Drosophila species, scattered throughout the phylogeny. As far as I know all cases were discovered by accident, so the sampling is biased towards model species (e.g., the obscura group, which was very popular around 1930-1960). So we do not know the true frequency of sex-ratio meiotic drive among Drosophila species, nor, say, if it is more common in the Drosophila or Sophophora species, if it is suspiciously absent in the montium group (as suggested by the authors), etc. I think these uncertainties should be acknowledged or, perhaps, given the weakness of the argument, the sentence should be deleted or attenuated.

We agree with this comment and have now removed this argument in our revision.

__ "X-Y chromosome fusions eliminate the extent of meiotic drive and may lead to the degeneration of otherwise conserved SNBP genes, whose functions as drive suppressors are no longer required. Thus, unlike in mammals, sex chromosome-associated meiotic drive appears to be the primary cause of SNBP evolutionary turnover in Drosophila species." The authors found that in the montium species the ancestral Y became incorporated into de X chromosome, and that montium species seem to have an inordinate amount of SNBP gene losses. They combine these two observations by suggesting that these SNBP became dispensable or deleterious because they originally were involved in XY meiotic drive. I think many readers will think that males in montium species are X/0, whereas in fact in all of them carry a Y chromosome (just, in most cases, more gene poor than "normal" Y-chromosomes). I do not think this is a fatal flaw for the explanation proposed by the authors, but certainly is a difficulty that should be acknowledged.

__

We agree with this point. It was not our intention to suggest that montium group males are X/O, but this could be misinterpreted as we originally stated. We now add a clarification that montium group males still harbor a Y chromosome, which is missing most ancestrally Y-linked genes.

__Problems/suggestions with experiments and data analysis

1. There is a section titled "CG30056 is universally retained in Drosophila but dispensable for male fertility in D. melanogaster". In this section and in the figures, it is stated, "Although CG30056 is the most conserved SNBP we surveyed, we found no clear difference in offspring number between heterozygous controls and homozygous knockout males (Fig 2B). (...) We found either no or weak evidence of fertility impairments in two different crosses with homozygous CG30056 knockout males.". I think the fertility data are weak for the purpose of the authors, and I strongly suspect that this conclusion is wrong. Let me explain why. At other passages of the ms, the authors classify the SNPB genes in three groups. (i) essential/important for male fertility: "Three genes (Mst77F, Prtl99C and ddbt) are essential for male fertility while knockdown or knockout of two other SNBP genes (ProtA, and ProtB) leads to significant reduction in male fertility [27-30, 32]." (ii) genes that do not appear to impair male fertility at all. (iii) untested. CG30056 was in the last group, and hence the authors produced knockouts, tested their effect in male fertility, and concluded that it belongs to the second group. Now, look at Fig. 3B. The numbers of tested males are too small (it seems to range from 3 to 10), and male fertility is known to be a very noisy phenotype (as shown by the huge scatter in the authors' data). Furthermore, two different knockouts were tested, and both were nominally less fertile than the controls, and in one of them the difference is statistically significant. Taken at the face value, the knockouts seem to be perhaps ~25% less fertile than the controls. Another potentially big problem is that the "control males" actually carry visible dominant mutants (the balancers CyO or SM6) which certainly reduce their fitness, whereas the experimental males are wild-type for these mutants. Without the detrimental effect of these visible mutants in the controls, the difference to the CG30056 knockouts will probably be even larger. Note that the fertility effects of the genes ProtA, and ProtB (a.k.a. "Mst35B") , which the authors put in group "essential/important for male fertility" would not had been detected if assayed as the CG30056 gene: Tirmarche et al (2014; the reference cited by the authors) stated that: "In fact, the impact of Mst35B on male fertility was only revealed when mutant males were allowed to mate with a large excess of virgin females (1 for 10; Figure 3F) but not with a 1:1 sex ratio (not shown). " The authors' fertility test did not used this type of challenge. My general impression is that the fertility effects of CG30056 may actually be similar to ProtA and ProtB. I think the authors should do a proper fertility test of CG30056, or remove this section. Another possibly useful approach would be to classify the SNPB genes in those essential for male fertility and those that are not essential, because "experimentally speaking" this is a safer distinction (e.g., the fertility testes reported by other authors may also had been quick tests). Since these genes only function in sperm and are under purifying selection (otherwise they would have been lost; also, all have dN/dS We are very appreciative of the many important points raised by the reviewer. Rather than removing this conclusion, which is not central to our paper, we have now performed additional, well-controlled experiments to address the reviewer’s concerns, which we summarize below:

2. We agree with the reviewer that it is easier classification to identify SNBP genes that are essential for male fertility versus those that are not.

3. We also agree with the reviewer and now include more details about earlier studies to highlight that ProtA/ProtB fertility effects were only revealed in a sperm exhaustion setting.
4. We agree with the reviewer’s suggestion and have now included sample sizes for all our experiments in a new supplementary Table (Supplementary file 8).
5. We agree with the reviewer that a comparison between KO/KO and KO/Bal males is non-ideal given that Balancer chromosomes carry many deleterious mutations. We now include new experiments in our revision that compare KO/KO and KO/wt chromosomes.
6. We agree with the reviewer that standard fertility assays may be too noisy to detect subtle fertility effects. We therefore now carry out much more stringent fertility assays under sperm exhaustion conditions with a male: female ratio of 1:10 and at least 10 males tested per genotype Despite this higher stringency, we detect no difference in fertility between KO/KO males and KO/wt controls for CG30056 (>10 males were tested for each). Thus, our original conclusion is even stronger that CG30056 has no detectable effect on male fertility. We have not tested the possibility of sperm storage or precedence being affected in our assays. However, we do believe that the finding that one of the best conserved and retained SNBP genes has no detectable effect on male fertility is an important conclusion which greatly increases the impact of our study, especially since most fertility-essential genes are either young or not universally conserved. We hope these changes will satisfy the reviewer's concerns about this section of our paper.

"Our phylogenomic analyses also highlighted one Drosophila clade- the montium group of species (including D. kikkawai)- which suffered a precipitous loss of at least five SNBP genes that are otherwise conserved in sister and outgroup species (Fig 3). (...) Given our hypothesis that autosomal SNBP genes might be linked to the suppression of meiotic drive (above), we speculated that the loss of these genes in the montium group of Drosophila species may have coincided with reduced genetic conflicts between sex chromosomes in this clade." The montium data is an important part of the paper. I think the authors should test the statistical significance of this pattern.

We appreciate the reviewer’s suggestion. However, we are unable to perform the statistical tests suggested for technical reasons. We note that three loss events occurred in the ancestor of D. montium species, while two happened in the ancestors of most D. montium species. Since it’s hard to estimate the evolutionary rates using these internal branches, we can’t directly compare them to other branches using statistics. However, in response to the reviewer’s comments, we now more clearly contrast the fate of SNBPs between D. montium species and other melanogaster group species, noting that three of five genes lost in the montium group are retained in all other melanogaster group species.

__Other points:

1. "The five remaining SNBP genes (Mst33A, CG30056, CG31010, CG34269, and CG42355) remain cytologically uncharacterized [30]." I think it will be interesting if the authors look at other potentially useful resources: Vibranovski et al papers which looked at gene expression in mitotic, meiotic and post-meiotic cells (_https://mnlab.uchicago.edu/sppress/index.php), and the papers by several labs on testis single-cell transcriptomic data (Witt et al 2021 PLOS Genetics. 17(8):e1009728 ; Nat Commun. 2021;12: 892). These may provide additional clues on the function of SNBP genes. There is also a recent report on sperm proteome (doi: _https://doi.org/10.1101/2022.02.14.480191) __

We are grateful to the reviewer for this suggestion. We now add the data from single-cell expression analyses from Witt et al. in Table 1-figure supplement 1. We found most SNBPs are expressed at late spermatocytes and early spermatids, although CG30056 is primarily expressed in late spermatids, whereas CG34269 is expressed earlier in late spermagonia. The data from Vibrranovski et al. also show similar patterns but don’t have four of these genes, including CG34269. The data from Mahadevaraju et al. are from larva testes, and lack some critical stages during spermatogenesis. Thus, we only report the data from Witt et al.

We also surveyed the proteome data as the reviewer suggested, but we only found 3 SNBPs (ProtA, ProtB, and Prtl99C) in the data. This did not include, Mst77F, which is the most highly expressed (see Table 2) and well-studied SNBP, so we suspect the proteomic study might be biased toward proteins from sperm tails. Therefore, we decide not to include this analysis.

____ "Our inability to detect homologs beyond the reported species does not appear to result from their rapid sequence evolution. Indeed, abSENSE analyses [45] support the finding that Prtl99C, Mst77F, Mst33A, Tpl94 and CG42355 were recently acquired in Sophophora within 40 MYA. For example, the probability of a true homolog being undetected for Prtl99C and Mst77F is 0.07 and 0.18 (using E-value=1), respectively (Table S1, Methods)." This should be complemented by synteny analysis.

It may not have been clear from our original version that we did perform synteny analyses for all SNBP genes. We have now restated this more clearly in our revision.

I found the following sentence unclear: "However, we could only ascribe a sex chromosomal linked location for species if no data was available from either BUSCO genes or females (only males and mixed-sex flies)."

We modified the sentence to make it clearer: “However, we could not ascribe a sex-chromosomal linked location of a contig to either the X or Y chromosome in cases where there was no linkage information from BUSCO genes and no read data available from females, only from males and mixed-sex flies.”

"Using the available assemblies with Illumina-based chromosome assignment, we surprisingly found that most ancestrally Y-linked genes are not linked to autosomes as was previously suggested [by Dupim et al 2018] (Fig 6A)."

The new result of X-linkage is exciting, but the sentence is not exact: Dupim et al 2018 made clear that they could only separate X/A from Y-linkage. E.g., the legend of their Fig 3: "Phylogeny and gene content of the Y chromosome in the montium subgroup. "M" means amplification only in males (i.e., Y-linkage), whereas "MF" means amplification in both sexes (autosomal or X-linkage)."

We are grateful to the reviewer for this correction. We now modified the sentence to make clear that Dupim et al had “showed that many ancestrally Y-linked genes are present in females because of possible relocation to other chromosomes in the montium group.”

"The most parsimonious explanation for these findings is a single translocation of most of the Y chromosome to the X chromosome via a chromosome fusion in the ancestor of the montium group of species. Afterward, some of these genes relocated back to the Y chromosome in some species (Fig S6; Supplementary text)." Explanations for this pattern of "return to the Y" have been extensively discussed and tested in Dupim et al 2008 (see their section "Why genes seem to return to the Y chromosome after Y incorporations?" ) The available evidence strongly suggests that it is not a case of relocation to the Y.

We thank the reviewer for raising this point. However, our conclusions disagree slightly with those from Dupim et al. 2018, in part because of additional sequencing in this clade. Dupim et al. suggested the possibility that most Y chromosomal loci duplicated to other chromosomes in the ancestor of the D. montium clade, following which each species degenerated either Y-linked or autosomal copies of genes. If this was the case, Y-linked copies should have diverged from X-linked copies since the ancestor of the D. montium clade. In contrast to this expectation, our phylogenetic analyses found that D. kikkawai Y-linked PRY is more closely related to X-linked PRY in all other related species (Figure 6- figure supplement 1). This result is much less parsimoniously explained by the ancient duplication event proposed by Dupim et al. and is more consistent with a ‘return-to-Y’ that we propose. We also make clear that, unlike PRY, we can’t differentiate the two hypotheses in the case of kl-2.

Fig 6B suggests that the authors assembled the "translocated Y" in D. triauraria. However, no direct data or account for this assembly is provided. Please clarify.

This was not our assembly. We searched all publicly available assemblies in the montium group and found one assembly (NCBI accession GCA_014170315.2) that assembled all ancestral Y-linked regions. We now clarify this in our revision.

__ "Why would meiotic drive only influence Drosophila, but not mammalian, SNBP evolution? One important distinction may arise from the timing of SNBP transcription. In D. melanogaster, SNBP genes are transcribed before meiosis but translated after meiosis [29, 43, 57]. Thus, SNBP transcripts from a single allele, e.g., Xlinked allele, are inherited and translated by all sperm, regardless of which chromosomes they carry. Consequently, they can act as meiotic drivers by causing chromatin dysfunction in sperm without the allele, e.g., Y-bearing sperm." During spermatogenesis Drosophila haploid cells actually are syncytial, which has interesting consequences for the evolution of male genes (Raices et al, Genome Res. 1115-1122, 2019). This may be relevant for the present paper.

__

We thank the reviewer for this suggestion. We now gratefully include this citation in our revision.

__Reviewer #2 (Significance (Required)):

see above __ __Reviewer #3 (Evidence, reproducibility and clarity (Required)):

This manuscript by Chang & Malik consider the evolution of HMG-box-containing sperm nuclear basic proteins (SNBPs) across Drosophila species in phylogenetic context.

Previous work in mammals had highlighted fast evolution of proteins involved in chromatin remodeling during spermatogenesis. Here, the authors provide evidence for widespread positive selection and likely involvement in genetic conflict in a set of proteins with analogous functions in Drosophila. Amongst other findings, the authors highlight biased amplification of SNBP paralogs on sex chromosomes along several Drosophila lineages, a tendency towards loss/pseudogenization following translocation onto a sex chromosome, and an intriguing concerted SNBP loss event in the montium group where parts of the Y chromosome have become fused to the X, thus nullifying the chance that genetic conflicts can play out via distorted segregation of sex chromosomes. The authors suggest that, taken together, their findings support widespread of SNBPs involvement (as instigators and repressors) in meiotic drive. Overall, I found the manuscript to be well written and thorough in its exploration of the evolutionary dynamics of SNBPs in this clade.

__

We thank the reviewer for the accurate summary and the kind comments.

__Below, I have highlighted some aspects that I think would benefit from further attention, none of them major.

• Following their exploration of patterns of SNBP evolution in Drosophila, the authors highlight support of their data for genetic conflict between sex chromosomes. They also rightly acknowledge that other evolutionary drivers such as sperm competition might also play a role in, for example, fast evolution of certain SNBPs. Yet those (not mutually exclusive) alternatives are never pitted directly against each other. The focus is firmly on exploring the support for the sex chromosome genetic conflict model. Given that the authors highlight Drosophila as a great model in part because of its well characterized sperm biology (including comparative morphology), I wondered why the authors had not made an explicit attempt to see if SNBP evolution covaries with aspects of sperm morphology across Drosophila. __

We do agree with the reviewer that it will be very interesting to test whether SNBP evolution covaries with sperm morphology in Drosophila. However, data on sperm morphology is scant in most Drosophila species. Indeed, this trait has only been well studied in clades with heteromorphic (different-sized) sperm but we agree this will be an exciting topic to consider in the future.

We also clarify better in our revised discussion that our analyses do not rule out a role for sperm competition or sperm morphology in driving the evolution of at least some SNBP genes. We note that a subset of SNBP genes undergo gene amplifications and loss, but most SNBP genes evolve rapidly including in species with gene loss. Thus, the meiotic drive hypothesis is not to the exclusion of other hypotheses.

• The most intriguing part of the manuscript for me was the exploration of SNBP fate in the montium group, where the authors find evidence for an ancestral fusion event between the X and parts of the Y chromosome. The loss of SNBPs is certainly consistent with the conflict model but I was wondering to what extent this lineage is characterized more broadly by unusual evolution at the chromosomal level. Is there simply a lot of upheaval in montium, with more frequent gain/loss across the board? How specific is SNBP loss in the context of other orthologous groups? This could be investigated by looking at retention of other genes in other orthologous groups (in montium and some other control group) or perhaps by looking at synteny conservation. This is a good suggestion. Using the same methodology as used in this paper, we found that very few D. melanogaster essential genes (2000) are lost in any single species we surveyed here (unpublished data). However, we have not carried out similar analyses for all genes; given vastly different rates of evolution, this would be a significant undertaking. Thus, we are not able to make a direct comparison between SNBP genes and a control group, that would include other testes-specific or fertility-essential genes. Instead, we highlight the fact that since we identify SNBPs using syntenic analyses, we have known that the neighboring genes of SNBPs are much better conserved than the SNBP genes themselves in the montium group species.

• In introducing SNBPs, the authors focus on their role as packaging agents. Clearly, SNBPs do package the genome in the sense that they bind to DNA and lead to reduced chromosome volume. But is this all packaging for packaging's sake (as portrayed by the sperm shape hypothesis)? Or is the situation a bit more nuanced, where condensation leads to a reduction of volume but also to a shutdown of transcription, protection from DNA damage, etc.? I think the focus on packaging alone is somewhat limiting when it comes to imagining how these proteins might act in the context of genomic conflicts. The authors may want to broaden their description of SNBPs in the Introduction accordingly. We completely agree with the reviewer and are currently exploring these possibilities in follow-up studies on SNBP function. However, it is fair to add that this hypothesis has not been well-recognized, and we, therefore, prefer to include it in our revised Discussion rather than Introduction. However, we also think that SNBP packaging function might be targeted by Wolbachia-encoded toxins, speeding up their evolution (revised Discussion). We think there are many molecular possibilities for SNBPs.

• The authors highlight that some SNBPs are expressed in mature sperm whereas others are transition proteins. The evidence for positive selection chiefly comes from the latter group (and "undefined" proteins that could also be transition proteins). Can the authors comment on whether this is expected/unexpected? Along the same lines, the authors highlight differences between Drosophila and mammals when it comes to the timing of transcription/translation during meiosis, suggesting that meiotic drive can happen in Drosophila because alleles are expressed early and can exert an effect after meiosis regardless of whether the associated locus is present in the gamete. I wonder how this relates, if at all, to the author's finding that transition SNBPs are more likely to be part of conflicts (as indicated by positive selection signals) compared to SNBPs in mature sperm. We thank the reviewer for this comment. We expect that many genes expressed explicitly in spermatogenesis, including SNBP genes, would be under position selection, regardless of whether they are associated with X-Y conflicts. The positive selection signals could come from either X-Y conflicts, sperm competition, or conflicts with Wolbachia; we now discuss all of these in the Discussion.

In contrast, the amplification and loss of a subset of Drosophila SNBPs are more likely associated with X-Y conflicts. We note that known SNBPs retained in mature sperm are more likely to be subject to amplification than known transition proteins.

Regarding the timing of expression, it is true that transition SNBPs act earlier in spermatogenesis than SNBPs retained in mature sperm. However, for the meiotic drive hypothesis to apply, all it requires is for SNBP expression to precede sperm individualization, which it does for most SNBPs, including transition proteins.

• ____ It is not entirely clear from the text (and also e.g. Table S4) how dN and dS (and subsequently dN/dS) where calculated. I presume as a single estimate across the whole phylogeny? If so, how heterogeneous is dN/dS across the phylogeny and can the authors identify specific branches on which selective regimes are different? A branch-level analysis should be better powered than the site-level analysis the authors present, which requires repeated selection on the same set of sites to get a strong enough signal. A branch-specific assessment of evolution would be particularly valuable in combination when combined with the assessment of amplifications/losses. We thank the reviewer for this question. The reviewer is correct. We estimated dN and dS in Supplementary file 4 across the whole phylogeny. We conducted branch tests for the amplification of tHMG only in the Dsim clade (Supplementary file 11).

We are interested in how SNBP amplification happened across species, but we need better gene annotation for their structure in many of these 19 independent cases. Moreover, we hope to combine these with transcriptomic analyses with detailed sequence analyses to reveal how the event happened and how gene conversion, gene duplication, and mutations affect their evolution. Each of these analyses requires extensive additional resources and analyses, and we feel are beyond the scope of this current paper.

• The authors suggest that young SNBPs are more likely to encode essential, non-redundant male fertility functions (p7, third paragraph). I'm not sure whether this generalization is appropriate given the small sample. Tpl94D is as young as Mst77F/Prtl99C, tHMG and CG14835 homologs have been lost along different lineages and most of the events are in a single lineage leading up to D. kikkawai. Do the authors really feel that this generalization is warranted? We agree with the reviewer. However, it is striking that the known fertility essential genes are either young or not universally conserved. We have therefore reworded our conclusion to make this contrast more accurate.__

• How do the sex-chromosomal amplifications differ in sequence from the ancestral autosomal copies? The authors suggest that the sex chromosomal copies might be involved in meiotic drive? Does the sequence offer a function as to how? (e.g. loss of charged residues/DNA-binding capacity?__

These are good questions. We do not know mechanistically how the sex-chromosome amplifications may cause meiotic drive. We did not observe the loss of positive charge or HMG domain in most sex-chromosomal amplified copies (Supplementary file 3). Our current working hypothesis is that they compete for the DNA binding with autosomal SNBP, and might interact with other proteins, e.g., heterochromatin proteins, to disturb sperm function. How they might function to cause meiotic drive is an active area of investigation in our and other labs.

• I think it would be nice to have a final table/figure to summarizing the different lines of evidence for all the genes in Table 1 (i.e. positive selection yes/no, amplification in some lineages yes/no, sex chromosome translocations yes/no), for different lineages, including whether any of the HMG-box genes are unlikely to act as SNBPs. We agree with this suggestion. We have now significantly revised and added to Table 2 to include this added information.

• The evidence the authors present is often consistent with genetic conflicts between sex chromosomes. Is it cogent? Arguably not (since direct tests of the mechanism are provided. I would therefore suggest a more cautious title than one stating that conflicts drive expansion and loss of SNBPs. We agree with all three reviewers and have amended our title to highlight the correlation. We also discuss other possibilities that can drive SNBP evolution in our revised Discussion.

__Typographical errors etc.:

• P3. First paragraph: "One of the driving forces ... " I found this sentence a bit odd in terms of causality (changes in composition being portrayed as a force that leads to selection) __

We thank the reviewer for pointing out the confusing construction. We modified the sentence to “The positive selection of SNBPs results in changes to their amino acid composition.”

- P3. Second paragraph: should be "HMG-box" rather than "HMB-box"

Fixed.

- P3. Fourth paragraph "..., consistent with the observation in mammals". I think "consistent" should be reserved for two observations that speak to the same phenomenon. SNBPs could evolve with no evidence for positive selection in Drosophila and that wouldn't exactly be "inconsistent" with mammals. It would just be different.

Fixed. We changed “consistent with” to “similar to”.

____- P5. Fifth paragraph: should be "in the PAML package" rather than "in PAML package"

Fixed.

- P9. Second paragraph: "... montium group (Fig 5A)...)" should be Fig 6A.

Fixed.

__CROSS-CONSULTATION COMMENTS I have not much to add. The other reviews seem fair and well-informed from my somewhat-outside perspective. I don't know how tricky/time-consuming the suggested additional fly mating experiments are but want to note that, in general, I'm loath to "punish" authors of principally bioinformatic work for including some experiments. If experimental shortcomings can be addressed with appropriate caveats, that should be an option, as should removal of experimental data that - by the experts - would be considered too preliminary.

__

We thank the reviewer for their support. However, we felt that improved experiments on CG30056 role in fertility could broaden the scope of this paper, despite the additional time and labor commitment. We have now finished these experiments and they do reinforce our original conclusions with much greater support.

__It is my policy to sign my reviews.

Tobias Warnecke

Reviewer #3 (Significance (Required)):

I'm not enough of an expert in the field of SNBPs to assess the level of advance provided by this study. __

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Referee #2

Evidence, reproducibility and clarity

The paper describes interesting patterns on the evolution of Drosophila SNBP genes, and proposes a very interesting explanation, namely, that meiotic drive is the main evolutionary force behind these patterns. Some of these observations have recently been made by other authors in a single case (the Dox genes in D. simulans), but not in the scale and breadth of the present ms. The ms combines an extensive investigation of available genomes with expert analysis, and new experimental data. In particular, the finding that the ancestral Y became incorporated into de X in montium species is very exciting, and may provide a smoking gun for the explanation proposed by the authors. Overall, I think it is a very good paper. I do have several criticisms and suggestions that may help to improve it.

The paper has a speculative side that it almost unavoidable given its novelty and breadth. I do not see this as a problem per se, but I think the uncertain/unsupported/problematic points should be more openly presented to the readers. The main cases I noted are:

1. The title of the ms states that "Genetic conflicts between sex chromosomes drive expansion and loss of sperm nuclear basic protein genes in Drosophila", but the evidence is somewhat circumstantial, and the patterns may be explained also by other known phenomena (e.g., demasculinization of the sex chromosomes; below). I think the tone of the end of the Introduction reflects more faithfully the strength of the evidence ("Thus, we conclude that rapid diversification of SNBP genes might be largely driven by genetic conflicts between sex chromosomes in Drosophila."). I understand the temptation of writing a bold title, but I think it is a bit misleading in the present case. I.e., it would be desirable that the title conveys the uncertainties of the data and their interpretation.
2. "In contrast, we found no instances of pseudogenization or subsequent translocation to the X chromosome of SNBP genes that are still preserved on their original autosomal locations or involved in chromosome fusions between autosomes (0/16). This difference is highly significant (Fig 5 and Table S11; 3:5 versus 0:16, Fisher's exact test, P=0.03). " Readers should be warned that this pattern can also be explained by the well-known demasculinization of X chromosomes (e.g., Sturgill et al. Nature 2007, 450, 238-241)
3. "Indeed, no meiotic drive has been documented in the montium species even though it is rampant in many other Drosophila lineages [38]." Two remarks here: a) the authors should make clear that they are referring to sex-chromosome meiotic drive. b) I think the evidence is much weaker than the sentence implies. Sex-chromosome meiotic drive is known in less than 20 Drosophila species, scattered throughout the phylogeny. As far as I know all cases were discovered by accident, so the sampling is biased towards model species (e.g., the obscura group, which was very popular around 1930-1960). So we do not know the true frequency of sex-ratio meiotic drive among Drosophila species, nor, say, if it is more common in the Drosophila or Sophophora species, if it is suspiciously absent in the montium group (as suggested by the authors), etc. I think these uncertainties should be acknowledged or, perhaps, given the weakness of the argument, the sentence should be deleted or attenuated.
4. "X-Y chromosome fusions eliminate the extent of meiotic drive and may lead to the degeneration of otherwise conserved SNBP genes, whose functions as drive suppressors are no longer required. Thus, unlike in mammals, sex chromosome-associated meiotic drive appears to be the primary cause of SNBP evolutionary turnover in Drosophila species." The authors found that in the montium species the ancestral Y became incorporated into de X chromosome, and that montium species seem to have an inordinate amount of SNBP gene losses. They combine these two observations by suggesting that these SNBP became dispensable or deleterious because they originally wee involved in XY meiotic drive. I think many readers will think that males in montium species are X/0, whereas in fact in all of them carry a Y chromosome (just, in most cases, more gene poor than "normal" Y-chromosomes). I do not think this is a fatal flaw for the explanation proposed by the authors, but certainly is a difficulty that should be acknowledged.

Problems/suggestions with experiments and data analysis

1. There is a section titled "CG30056 is universally retained in Drosophila but dispensable for male fertility in D. melanogaster". In this section and in the figures, it is stated, "Although CG30056 is the most conserved SNBP we surveyed, we found no clear difference in offspring number between heterozygous controls and homozygous knockout males (Fig 2B). (...) We found either no or weak evidence of fertility impairments in two different crosses with homozygous CG30056 knockout males.". I think the fertility data are weak for the purpose of the authors, and I strongly suspect that this conclusion is wrong. Let me explain why. At other passages of the ms, the authors classify the SNPB genes in three groups.
   • (i) essential/important for male fertility: "Three genes (Mst77F, Prtl99C and ddbt) are essential for male fertility while knockdown or knockout of two other SNBP genes (ProtA, and ProtB) leads to significant reduction in male fertility [27-30, 32]."
   • (ii) genes that do not appear to impair male fertility at all.
   • (iii) untested. CG30056 was in the last group, and hence the authors produced knockouts, tested their effect in male fertility, and concluded that it belongs to the second group. Now, look at Fig. 3B. The numbers of tested males are too small (it seems to range from 3 to 10), and male fertility is known to be a very noisy phenotype (as shown by the huge scatter in the authors' data). Furthermore, two different knockouts were tested, and both were nominally less fertile than the controls, and in one of them the difference is statistically significant. Taken at the face value, the knockouts seem to be perhaps ~25% less fertile than the controls. Another potentially big problem is that the "control males" actually carry visible dominant mutants (the balancers CyO or SM6) which certainly reduce their fitness, whereas the experimental males are wild-type for these mutants. Without the detrimental effect of these visible mutants in the controls, the difference to the CG30056 knockouts will probably be even larger. Note that the fertility effects of the genes ProtA, and ProtB (a.k.a. "Mst35B") , which the authors put in group "essential/important for male fertility" would not had been detected if assayed as the CG30056 gene: Tirmarche et al (2014; the reference cited by the authors) stated that: "In fact, the impact of Mst35B on male fertility was only revealed when mutant males were allowed to mate with a large excess of virgin females (1 for 10; Figure 3F) but not with a 1:1 sex ratio (not shown). " The authors' fertility test did not used this type of challenge. My general impression is that the fertility effects of CG30056 may actually be similar to ProtA and ProtB. I think the authors should do a proper fertility test of CG30056, or remove this section. Another possibly useful approach would be to classify the SNPB genes in those essential for male fertility and those that are not essential, because "experimentally speaking" this is a safer distinction (e.g., the fertility testes reported by other authors may also had been quick tests). Since these genes only function in sperm and are under purifying selection (otherwise they would have been lost; also, all have dN/dS < 1 ), they all most likely affect male fertility to some extent. In case the section on male fertility stays, it will be necessary to provide more details. How many males were crossed for each genotype? In some cases in Fig 2B, it seems that as low as 3, but it may be data superposition in the graph. Please provide the raw data in the supplementary material.
2. "Our phylogenomic analyses also highlighted one Drosophila clade- the montium group of species (including D. kikkawai)- which suffered a precipitous loss of at least five SNBP genes that are otherwise conserved in sister and outgroup species (Fig 3). (...) Given our hypothesis that autosomal SNBP genes might be linked to the suppression of meiotic drive (above), we speculated that the loss of these genes in the montium group of Drosophila species may have coincided with reduced genetic conflicts between sex chromosomes in this clade." The montium data is an important part of the paper. I think the authors should test the statistical significance of this pattern.

Other points:

1. "The five remaining SNBP genes (Mst33A, CG30056, CG31010, CG34269, and CG42355) remain cytologically uncharacterized [30]." I think it will be interesting if the authors look at other potentially useful resources: Vibranovski et al papers which looked at gene expression in mitotic, meiotic and post-meiotic cells (https://mnlab.uchicago.edu/sppress/index.php), and the papers by several labs on testis single-cell transcriptomic data (Witt et al 2021 PLOS Genetics. 17(8):e1009728 ; Nat Commun. 2021;12: 892). These may provide additional clues on the function of SNBP genes. There is also a recent report on sperm proteome (doi: https://doi.org/10.1101/2022.02.14.480191)
2. "Our inability to detect homologs beyond the reported species does not appear to result from their rapid sequence evolution. Indeed, abSENSE analyses [45] support the finding that Prtl99C, Mst77F, Mst33A, Tpl94 and CG42355 were recently acquired in Sophophora within 40 MYA. For example, the probability of a true homolog being undetected for Prtl99C and Mst77F is 0.07 and 0.18 (using E-value=1), respectively (Table S1, Methods)." This should be complemented by synteny analysis.
3. I found the following sentence unclear: "However, we could only ascribe a sex chromosomal linked location for species if no data was available from either BUSCO genes or females (only males and mixed-sex flies)."
4. "Using the available assemblies with Illumina-based chromosome assignment, we surprisingly found that most ancestrally Y-linked genes are not linked to autosomes as was previously suggested [by Dupim et al 2018] (Fig 6A)." The new result of X-linkage is exciting, but the sentence is not exact: Dupim et al 2018 made clear that they could only separate X/A from Y-linkage. E.g., the legend of their Fig 3: "Phylogeny and gene content of the Y chromosome in the montium subgroup. "M" means amplification only in males (i.e., Y-linkage), whereas "MF" means amplification in both sexes (autosomal or X-linkage)."
5. "The most parsimonious explanation for these findings is a single translocation of most of the Y chromosome to the X chromosome via a chromosome fusion in the ancestor of the montium group of species. Afterward, some of these genes relocated back to the Y chromosome in some species (Fig S6; Supplementary text)." Explanations for this pattern of "return to the Y" have been extensively discussed and tested in Dupim et al 2008 (see their section "Why genes seem to return to the Y chromosome after Y incorporations?" ) The available evidence strongly suggests that it is not a case of relocation to the Y.
6. Fig 6B suggests that the authors assembled the "translocated Y" in D. triauraria. However, no direct data or account for this assembly is provided. Please clarify.
7. "Why would meiotic drive only influence Drosophila, but not mammalian, SNBP evolution? One important distinction may arise from the timing of SNBP transcription. In D. melanogaster, SNBP genes are transcribed before meiosis but translated after meiosis [29, 43, 57]. Thus, SNBP transcripts from a single allele, e.g., Xlinked allele, are inherited and translated by all sperm, regardless of which chromosomes they carry. Consequently, they can act as meiotic drivers by causing chromatin dysfunction in sperm without the allele, e.g., Y-bearing sperm." During spermatogenesis Drosophila haploid cells actually are syncytial, which has interesting consequences for the evolution of male genes (Raices et al, Genome Res. 1115-1122, 2019). This may be relevant for the present paper.

Significance

see above

I disagree with this. I don't think it is a particularly relevant argument to make, as something like a medical condition or diagnosis does not correlate ot something like being gay. Being gay is not something people "suffer from"

It's always interesting for a student to challenge their own thinking and questions the things that may be thought of as "absolute truths". Growth and understanding, empathy even, comes from these realizations.

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Reply to the reviewers

Manuscript number: #RC-2022-01697

Corresponding author(s): William Roman; Edgar R. Gomes

[The “revision plan” should delineate the revisions that authors intend to carry out in response to the points raised by the referees. It also provides the authors with the opportunity to explain their view of the paper and of the referee reports.

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1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

We would like to thank the reviewers for their careful evaluation of our study. The goal of this work is to demonstrate that fiber type composition can be altered with exercise of in vitro muscle cultures. These findings provide an additional strategy to better mimic muscle in vitro for biological investigation and disease modelling. The reviewers’ comments will strengthen the conclusions of our study.

In this point-by-point answer, we also include a statement on the feasibility of each comment based on preliminary work we have performed since receiving the reviews. We expect experiments can be achieved within 2 – 3 months.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

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

The manuscript by Henning et al describes a method to induce myofiber subtype specification in vitro based on optogenetics and particle image velocimetry. The work is well performed and the manuscript is clear. The findings might be useful to the muscle community, but there are some issues which should be addressed in order to improve the quality and impact of the manuscript.

My main concern is that the whole work is performed in murine cells. Although I appreciate that the authors have used primary myoblasts rather than cell lines, I also think that the key advantage of such in vitro platforms is the possibility to "humanise" the experiments as much as possible. In this context, the key findings of this work should be reproduced using human myoblasts. This will significantly enhance the relevance of the work. *

Point 1.1) We thank the reviewer for his suggestion and have already performed some pilot experiments to “humanize” experiments. We infected hiPSC-derived myotubes (van der Wal et al., 2018) and human immortalized myotubes (Mamchaoui et al., 2011) with AAV9-pACAGW-ChR2-Venus-AAV. After infection, human immortalized myotubes did not express ChR2, not permitting optogenetic training on these cultures. For hiPSC-derived myotubes, the infection rate was very low and insufficient to perform a bulk analysis to evaluate the effect of long term intermittent light stimulation. Moreover, the contractile behavior of hiPSC-derived myotubes expressing ChR2 significantly differed from primary mouse myotubes. They underwent a single and slow contraction when compared to the cyclic contractions observed in mouse myotubes. This suggests that the maturation of the contractile apparatus of 2D hiPSC-derived myotubes is insufficient to perform consistent in vitro training studies.

As such, we agree with the reviewer that reproducing our key findings with human cells would improve the relevance of this work. However, due to the experimental limitations described above, significant improvements in human myotube maturation in vitro are required to perform such experiments. We will attempt to increase infection efficiency by using another AAV serotype in hiPSC-derived myotubes but this has a low probability of solving all the technical limitations. Our work is a proof of principal that fiber type composition can be influenced in vitro through contraction stimulation. We expect these findings to be the translated to human cultures when the field has discovered the necessary protocols to push human myotube maturation.

Feasibility: run additional tests but probability of success is low due to technical limitations.

*Other issues: *

1) From a methodological perspective, I think some clarifications are needed on the western blots shown in Fig 4K-L, as the pattern of Myh3 and Myh8 in both panels appear very similar. This could easily be ruled out by providing raw data/images. Please accept my apologies if this is simply caused by similar migration patterns in the gels (worth checking).

Point 1.2) The very similar appearance of both patterns is due to the same molecular weight (220 kDA) of distinct myh isoforms. After an initial staining of western blot membranes, primary and secondary antibodies were stripped off and the membrane was subsequently re-probed using a primary and secondary antibody. We incubated stripped membranes with secondary antibodies only and observed no signal, confirming the stripping was efficient. We have updated the representative images of the Western Blot membranes in Figure 4 and included the α-actinin loading controls on which the bands are normalized to account for sarcomerogenesis (Figure 4 K-M).

Feasibility: Accomplished

*2) Figure 3K-L (BTX): better imaging should be performed to assess morphology of NMJ (eg. pretzel-shaped as in mature/adult NMJ?) *

Point 1.3) We agree with the point raised by the reviewer. However, a morphological assessment of the NMJ is difficult in this in vitro system due to our inability to generate mature muscle end plates as seen in in vivo adult NMJs. We will nevertheless perform a more quantitative evaluation of BTX stainings imaged with high spatial resolution by measuring the size and shape of the AChR clusters. The technical pipeline to do this quantitative approach is already established.

Feasibility: will be accomplished

*3) Figure 3 N-P: Why did the authors used a relatively complex techniques such as smFISH to answer a question more simply addressable with more conventional (and perhaps less operator dependent) techniques such quantitative PCR?

*

Point 1.4) We agree with the reviewer that the more conventional qPCR technique would highlight similar results to the smFISH quantifications. Due to the heterogeneity of our primary myotube cultures (presence of non-muscle cell types and varying degrees of muscle cell maturation), we opted to monitor AChR expression by conserving a spatial dimension. This allows us to observe ChrnE and ChrnG expression in mature muscle cells selected to perform the contraction analysis. Nevertheless, performing a bulk RNA expression analysis would be informative to show a significant increase in AChR expression across the culture. This point will be fully addressed by qPCR assays of ChrnE and ChrnG.

Feasibility: will be accomplished

*Reviewer #1 (Significance (Required)):

Nature and significance: as mentioned in the previous section, the work can be very significant if expanded to human myoblasts/myotubes, which can have different slow/fast myosin expression pattern. The work is clearly methodological/descriptive, so showing an application of this technique using diseased/mutant cells may increase its relevance even more (but I do not believe it is a key barrier to publication). *

We thank the reviewer for his comments as the “other issues” raised will significantly improve the manuscript and will all be tackled. With regards to using human myotubes, we will attempt a few more strategies to translate our findings to human cultures, but our preliminary data suggests that many technical barriers need to be overcome to perform such experiments. Nevertheless, it is our opinion that the main contribution of this manuscript is to show that fiber switching can be achieved in vitro and that this will be routinely used in the next generation of human in vitro muscle systems.

*

*

*Comparison with other methods: Similar methods have been published but not with this level of resolution.

Expertise: muscle disease and regeneration, in vitro and in vivo models.*

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

* The work presented shows that muscle stem cells isolated from 5-day-old mice can be transduced with a DNA coding for a Channelrhodopsin2-Venus which will allow the muscle cell to be excited by a light beam (475nm) and to induce the contraction of myotubes. The authors measure the speed of contraction, relaxation and fatigability of such cells as a function of a more or less long excitation time. In particular, they show that myotubes in culture, excited at a frequency of 5 Hz, 8 hours per day for 7 days are larger than unstimulated myotubes and are more resistant to fatigue. Surprisingly, they show that myotubes stimulated at the low frequency of 5Hz express the neonatal Myosin heavy chain more than the slow Myh whose expression is known in adult muscle to be specifically strong in muscle fibers stimulated at low frequency. As the authors do not apply a high stimulation frequency (100Hz) to their culture, it is difficult to conclude whether the stimulation frequency applied in the study induces a specific phenotypic specialization of the myofiber, or a more general role. In this respect, the size of the myotubes obtained after training seems to be increased, showing a hypertrophic effect on the cultured myotubes. This study does not allow us to conclude, beyond the expression of the Myh8 gene, on the “gain” of the fast-twitch specialization of the myofiber by repeated stimulation over several days. A complementary study would certainly provide elements to better understand the role of muscle fiber stimulation, apart from the trophic contribution provided in vivo by the motoneuron. If the study is well conducted, some points are nevertheless important to address before publication.*

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

* - Figures 4F/G are difficult to understand: the Myh7 signal seems much higher in trained myonuclei (F), but the histogram shows the opposite (G).*

__Point 2.1) __We apologize for the confusion. The apparent higher Myh7 signal in trained cells in Figure 4F is due to background noise in the image. When mRNA is expressed, the smFISH probes are visible as small round dots. For clarity, we updated the representative images for the smFISH probes and highlighted the smFISH dots with arrows. We also adapted the y-axis of each graph to better represent the analysis of mRNA counts per myonuclei.

Feasibility: Accomplished

*- Figures 4L, the western blot shows the same increase in Myh3 and Myh8 at day 4, while the graph shows an increase at d4 only in Myh8, why? *

Point 2.2) We have chosen another western blot to better reflect the quantification. It is important to note that we have normalized the band intensity to a-actinin instead of a house keeping gene to account for changes in sarcomerogenesis over the lifetime of the cultures. As such, although we observe an increase in Myh3 intensity, it is counter balanced by an increase in a-actinin expression. We have now added the a-actinin bands.

- For immunocytochemistry against fMyh (Fig4 H, I) as well as for Western blots (Fig 4M, N), the authors have to provide arguments regarding the specificity of the antibodies used: some fMyh-specific antibodies recognize, Myh 3, 8, 1, 2, and 4, some only Myh 8, 1, 2, and 4, so it is quite difficult to conclude on the experiments using sc-32732 antibodies, (clone F59) which Myh are actually recognized in Western blot or immunocytochemistry.

Point 2.3) According to the manufacturer, the sc-32732 antibody is specific for fast Myh (Myh1, 2, 4 and 6). Nevertheless, we will ensure the specificity of the sc-32732 antibody against fast Myosins by staining neonatal and adult TA/EDL muscle sections with anti-Myh3 (embryonic), anti-Myh8 (neonatal) and anti-fMyh antibodies.

Feasibility: will be accomplished

While 10Hz stimulation is known in vivo to increase the slow program, and Myh7 expression in adult muscles, the authors show that ex vivo this is not the case with primary myotubes, with Myh7 protein level not being upregulated in the 7 day stimulation paradigm, while on the contrary Myh8 expression is upregulated. I think it would be important to quantify the mRNA of each of the Myh genes to be sure that there is no problem with the antibodies, which could recognize several Myh proteins, in the absence of a resolving acrylamide gel allowing visualization and relative level of each isoform according to its migration. Nevertheless, this is an interesting observation that could be related to the early phases of muscle contraction in vivo. Indeed, it has been shown in rats that early postnatal development animals are essentially sedentary and whose muscles (Sol and EDL) are stimulated by short intermittent bursts similar to 10Hz (doi: 10.1111/j.0953-816X.2004.03418.x) during the first 2-3 weeks of life. This should be compatible with Myh8 expression. It would be relevant in this idea to verify that the paradigm presented leads to myotubes with a "neonatal" phenotype. Quantification of the expression level of *genes specifically expressed during the neonatal period, compared with those expressed in adult slow or fast myofibers, would enhance the conclusions drawn by the authors. *

Point 2.4) The reviewer raises an important technical limitation of observing Myh proteins to identify fiber types due to the cross-reactivity of antibodies. Despite our best efforts to select the appropriate antibodies, we agree that investigating mRNA expression of individual Myh isoforms would strengthen the conclusion of our study. We will design specific primers and perform qPCR for distinct Myh isoforms on untrained and trained cultures.

With regards to the “neonatal” phenotype of these in vitro cultures, this does indeed seem to be the case as the cultures transition from embryonic and neonatal myosins to adult myosins during the lifetime of the cultures.

Feasibility: will be accomplished

*Should we also be cautious about bulk analysis since, as shown in Figure S1, not all myotubes express ChR2? *

Point 2.5) Although 10% of myotubes do not express ChR2, we believe that 90% of infected myotubes is sufficient for bulk analysis. We nevertheless combine in our study bulk analysis with single cell assays such as smFISH and immunofluorescence, which are in line with the bulk analyses.

Feasibility: Accomplished

May the authors correlate the ex vivo neonatal phenotype observed with the neonatal muscles they used to prepare myogenic stem cells?

Point 2.6) We understand from this that the reviewer would like us to check the expression of distinct Myh isoforms in our in vitro system and compare it to neonatal muscle. We will perform Myh staining of muscle sections from 6-day old mouse pups (time of myogenic stem cell isolation) and compare the expression of Myosin heavy chains with what we observe in our in vitro cultures.

Feasibility: will be accomplished

Overall, we will address all the points of the reviewer. Those ensuring the specificity of antibodies used are particularly relevant. With regards to the comparison between our in vitro cultures with neonatal muscle, we believe this will help contextualize our findings with the literature.

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

*Summary: *

*In this work, the authors propose an in vitro model describing a strategy to alter fiber type composition of myotubes with a long-term, intermittent mechanical training. The authors present a model of myotubes transfected with an adenovirus, which makes them photosensitive; in this way, fibers contraction can be induced upon stimulation with blue LEDs. *

*Even though ChR2 expressing myotubes have previously been used by other groups (Asano T, Ishizua T, Yawo H. Optically controlled contraction of photosensitive skeletal muscle cells. Biotechnol Bioeng. 2012 Jan;109(1):199-204), no one has ever used it in the way proposed by the authors. For this reason, this work opens new perspectives on the possible use for clinical and therapeutic purposes for this in vitro muscle system. *

*Major comments: *

*I believe that the authors have presented their results, conclusion and methods in a fair and clear way, so that the experiment could also be reproduced. *

*However, I think there are some adjustments that could be done in order to improve and strengthen the quality of this work: *

*- The authors have analysed the expression of different myosin heavy chain isoforms, both regarding the slow and fast twitch fibers. Though, I think it would be interesting to investigate also the expression of Myh4, which is mainly expressed in type IIB fast twitch fibers; *

Point 3.1) We agree with the reviewer’s comment. We will add the analysis for Myh 4 (western blots and qPCR) to our manuscript.

Feasibility: will be accomplished

The authors have observed a switch in the fiber type upon prolonged intermittent stimulation with blue LEDs, which translates into a higher number of type II fibers. It is known that exercise helps rescuing the loss of type II fibers, which is typical of age-related physiological processes, such as sarcopenia (Brunner F, Schmid A, Sheikhzadeh A, Nordin M, Yoon J, Frankel V. Effects of aging on Type II muscle fibers: a systematic review of the literature. J Aging Phys Act. 2007 Jul;15(3):336-48). However, I believe that providing a deeper analysis of the metabolism of the type II fibers (i.e. oxidative or glycolytic) could be helpful in order to have a clearer view on the specific subset of fibers that are generated with the given experimental conditions;

Point 3.2) We agree with the reviewer's suggestion that an additional metabolic analysis would strengthen our observation. We propose to perform lactate measurements in cell lysate and supernatant to monitor a switch from oxidative to glycolytic metabolism. Specific inhibitors of the glycolytic pathway (2-DG, UK5099, Rotenone and AntimycinA) will be used as a control to prevent trained cells to shift towards a fast fiber type.

Alternatively, we will assess the protein expression levels of key metabolic proteins involved in oxidative phosphorylation and in pyruvate and lactate production (e.g. OxPhos, …). All these techniques are routinely performed in an adjacent laboratory and we foresee no technical limitations.

Feasibility: will be accomplished

*Minor comments: *

*The text and the figures are clear and well written, and help to explain better the experimental setup and procedures. Still, I would suggest some minor adjustments: *

- I would suggest providing more information on the pH used for the experiments, since it plays a pivotal role in regulating myosin ATPase activity and, thus, muscular contractility. This would improve the replicability of your experiment.

We thank the reviewer for this comment. We will provide information regarding the pH and add it in the method and materials section.

Feasibility: will be accomplished

The caption of Figure 1 is missing a description of panel E, even if it has been addressed in the text.

Point 3.3.) We apologize for this mistake. We added the missing description of Fig. 1E.

Feasibility: Accomplished

*Reviewer #3 (Significance (Required)): *

*This model opens new perspectives on in vitro muscle systems for the study of pathologies. The authors have been able to assess that myofibers contraction is able to induce a shift towards type II fibers, reproducing in vitro what is also known in vivo. For this reason, I believe that this model could be useful for further clinical approaches. It is important, though, to keep in mind that muscular disorders are not all characterized by a loss of type II fibers; for instance, myotonic dystrophies type I and type 2 exhibit similar phenotypes, even if different types of muscle fibers are affected. *

*For this reason, it would be interesting to investigate the versatility of this model in terms of giving rise to different fiber types. *

Point 3.4.) We added a sentence in the introduction that highlights an example of muscle disorders in which slow muscle fibers are predominately affected. Concerning the versatility of the model, we will add a paragraph to the discussion elaborating on how different stimulus frequency and durations could influence the specialization of fiber types.

Feasibility: Accomplished

Overall, we will address all major and minor comments from the reviewer. We have identified the experiments required for the metabolic analysis and agree that it will bolster our findings.

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

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

We have already carried out the following changes in the manuscript, which were proposed by the reviewers:

Point 1.2: pattern of Myh3 and Myh8 in both panels appear very similar - We updated the representative images of Myh 3 and Myh8 in Figure 4 K-N __and included the loading controls Myh 8 and fMyh images in __Figure 4K-N __and to __supplementary Figure 4 A, B.

Point 2.1: Figures 4F/G: representative images of Myh7 smFISH probe and the graph showing opposite trends – We have updated the representative images of Figure 4F and we have changed the x-axis of the graph in Figure 4E and G.

__Point 2.5: __caution around bulk analysis – we consider that based on the high percentage of contracting cells in response to blue light (~90%), this concern is not warranted.

Point 3.3: caption of Figure 1 is missing a description of panel E – We have added the missing description to the manuscript (Figure 1E).

Point 3.4: muscular disorders are not all characterized by a loss of type II fibers – we have added an example of a muscle disorder, in which slow fibers are predominantly affected, to the introduction (line 42-44) of the manuscript.

investigate the versatility of this model in terms of giving rise to different fiber types – we added a paragraph to the discussion elaborating on how different stimulus frequency can lead to different fiber types (line 264-275).

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

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

Point 1.1: Reproducing our key findings with human cells – we ran pilot experiments on immortalized human cell lines and human iPSC-derived myotubes but were not able to mature these cells sufficiently nor infect them to allow long-term in vitro training. Increased maturation of myotubes derived from hiPSCs is an endeavor currently undertaken by many laboratories. Although we will attempt a few more trials, we believe the technical limitations are too important to address this point.

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Referee #2

Evidence, reproducibility and clarity

The work presented shows that muscle stem cells isolated from 5-day-old mice can be transduced with a DNA coding for a Channelrhodopsin2-Venus which will allow the muscle cell to be excited by a light beam (475nm) and to induce the contraction of myotubes. The authors measure the speed of contraction, relaxation and fatigability of such cells as a function of a more or less long excitation time. In particular, they show that myotubes in culture, excited at a frequency of 5 Hz, 8 hours per day for 7 days are larger than unstimulated myotubes and are more resistant to fatigue. Surprisingly, they show that myotubes stimulated at the low frequency of 5Hz express the neonatal Myosin heavy chain more than the slow Myh whose expression is known in adult muscle to be specifically strong in muscle fibers stimulated at low frequency. As the authors do not apply a high stimulation frequency (100Hz) to their culture, it is difficult to conclude whether the stimulation frequency applied in the study induces a specific phenotypic specialization of the myofiber, or a more general role. In this respect, the size of the myotubes obtained after training seems to be increased, showing a hypertrophic effect on the cultured myotubes. This study does not allow us to conclude, beyond the expression of the Myh8 gene, on the "gain" of the fast-twitch specialization of the myofiber by repeated stimulation over several days. A complementary study would certainly provide elements to better understand the role of muscle fiber stimulation, apart from the trophic contribution provided in vivo by the motoneuron.

If the study is well conducted, some points are nevertheless important to address before publication.

Significance

• Figures 4F/G are difficult to understand: the Myh7 signal seems much higher in trained myonuclei (F), but the histogram shows the opposite (G).
• Figures 4L, the western blot shows the same increase in Myh3 and Myh8 at day 4, while the graph shows an increase at d4 only in Myh8, why?
• For immunocytochemistry against fMyh (Fig4 H, I) as well as for Western blots (Fig 4M, N), the authors have to provide arguments regarding the specificity of the antibodies used: some fMyh-specific antibodies recognize, Myh 3, 8, 1, 2, and 4, some only Myh 8, 1, 2, and 4, so it is quite difficult to conclude on the experiments using sc-32732 antibodies, (clone F59) which Myh are actually recognized in Western blot or immunocytochemistry.
• While 10Hz stimulation is known in vivo to increase the slow program, and Myh7 expression in adult muscles, the authors show that ex vivo this is not the case with primary myotubes, with Myh7 protein level not being upregulated in the 7 day stimulation paradigm, while on the contrary Myh8 expression is upregulated. I think it would be important to quantify the mRNA of each of the Myh genes to be sure that there is no problem with the antibodies, which could recognize several Myh proteins, in the absence of a resolving acrylamide gel allowing visualization and relative level of each isoform according to its migration. Nevertheless, this is an interesting observation that could be related to the early phases of muscle contraction in vivo. Indeed, it has been shown in rats that early postnatal development animals are essentially sedentary and whose muscles (Sol and EDL) are stimulated by short intermittent bursts similar to 10Hz (doi: 10.1111/j.0953-816X.2004.03418.x) during the first 2-3 weeks of life. This should be compatible with Myh8 expression. It would be relevant in this idea to verify that the paradigm presented leads to myotubes with a "neonatal" phenotype. Quantification of the expression level of genes specifically expressed during the neonatal period, compared with those expressed in adult slow or fast myofibers, would enhance the conclusions drawn by the authors.
• Should we also be cautious about bulk analysis since, as shown in Figure S1, not all myotubes express ChR2?
• May the authors correlate the ex vivo neonatal phenotype observed with the neonatal muscles they used to prepare myogenic stem cells?

Author Response

Reviewer #1 (Public Review):

The authors are trying to determine how time is valued by humans relative to energy expenditure during non-steady-state walking - this paper proposes a new cost function in an optimal control framework to predict features of walking bouts that start and stop at rest. This paper's innovation is the addition of a term proportional to the duration of the walking bout in addition to the conventional energetic term. Simulations are used to predict how this additional term affects optimal trajectories, and human subjects experiments are conducted to compare with simulation predictions.

I think the paper's key strengths are its simulation and experimental studies, which I regard as cleverly-conceived and well-executed. I think the paper's key weakness is the connection between these two studies, which I regard as tenuous for reasons I will now discuss in detail.

The Title asserts that "humans dynamically optimize walking speed to save energy and time". Directly substantiating this claim would require independently manipulating the (purported) energy and time cost of walking for human subjects, but these manipulations are not undertaken in the present study. What the Results actually report are two findings:

1. (simulation) minimizing a linear combination of energy and time in an optimal control problem involving an inverted-pendulum model of walking bouts that (i) start and stop at rest and (ii) walk at constant speed yields a gently-rounded speed-vs-time profile (Fig 2A);

2. (experiment) human subject walking bouts that started and stopped at rest had self-similar speed-vs-time profiles at several bout lengths after normalizing by the average duration and peak speed of each subject's bouts (Fig 4B).

If the paper established a strong connection between (1.) and (2.), e.g. if speed-vs-time trajectories from the simulation predicted experimental results significantly better than other plausible models (such as the 'steady min-COT' and 'steady accel' models whose trajectories are shown in Fig 2A), this finding could be regarded as providing indirect evidence in support of the claim in the paper's Title. Personally, I would regard this reasoning as rather weak evidence - it would be more accurate to assert 'brief human walking bouts look like trajectories of an inverted-pendulum model that minimize a linear combination of energy and time' (of course this phrasing is too wordy to serve as a replacement Title -- I am just trying to convey what assertion I think can be directly substantiated by the evidence in the paper). But unfortunately, the connection between (1.) and (2.) is only discussed qualitatively, and the other plausible models introduced in the Results are not revisited in the Discussion. To my naive eye, the representative 'steady min-COT' trace in Fig 2A seems like a real contender with the 'Energy-Time' trace for explaining the experimental results in Fig 4, but this candidate is rejected at the end of the third-to-last paragraph in the 'Model Predictions' subsection of Results based on the vague rationale that is never revisited.

We have addressed most of this comment above, but respond here regarding Fig. 4. The argument against steady min-COT should also point out the peak speed. The Results have been revised thus: “In contrast to the min-COT hypothesis, the human peak speeds increased with distance, many well below the min-COT speed of about 1.25 m/s. The human speed trajectories did not resemble the trapezoidal profiles of the steady min-COT hypothesis for all distances, nor the triangular profiles of steady acceleration.”

An additional limitation of the approach not discussed in the manuscript is that a fixed step length was prescribed in the simulations. The 'Optimal control formulation' subsection in the Methods summarizes the results of a sensitivity analysis conducted by varying the fixed step length, but all results reported here impose a constant-step-length constraint on the optimal control problem. Although this is a reasonable modeling simplification for steady-state walking, it is less well-motivated for the walking bouts considered here that start and stop at rest. For instance, the representative trial from a human subject in Figure 8 clearly shows initiation and termination steps that differ in length from the intermediate steps (visually discernable via the slope of the dashed line interpolating the black dots). Presumably different trajectories would be produced by the model if the constant-step-length constraint were removed. It is unclear whether this change would significantly alter predictions from either the 'Energy-Time' or 'steady min-COT' model candidates, and I imagine that this change would entail substantial work that may be out of scope for the present paper, but I think it is important to discuss this limitation.

This is addressed elsewhere (Essential Revisions 2), but we explain more here. One of the parameter studies included step length increasing with speed according to the human preferred relationship. This is included in Fig. 3, and so we concluded that variable step lengths are not critical to the speed trajectories. A related assumption is that the energetic cost of modulating step length/frequency is small compared to the step-to-step transition cost. We believe that humans expend substantial energy for both costs, but that the overall cost of walking is still dominated by step-to-step transitions.

With my concerns about the paper's framing and through-line noted as above, I want to emphasize that I regard the computational and empirical work reported here to be top-notch and potentially influential. In particular, the experimental study's use of inexpensive wearable sensors (as opposed to more conventional camera-based motion capture) is an excellent demonstration of efficient study design that other researchers may find instructive. To maximize potential impact, I encourage the authors to release their data, simulations, and details about their experimental apparatus (the first two I regard as essential for reproducibility - the third a selfless act of service to the scientific community).

I think the most important point to emphasize is that the bulk of prior work on human walking has focused on steady-state movement - not because of the real-world relevance (since one study reports 50% of walking bouts in daily life are < 16 steps as summarized in Fig 1B), but rather because steady walking is a convenient behavior to study in the laboratory. Significantly, this paper advances both our theoretical and empirical understanding of the characteristics of non-steady-state walking.

It is also significant to note the relationship between this study, where time was incorporated as an additive term in the cost of walking, with previous studies that incorporated time in a multiplicative discount in the cost of eye and arm movements. There is an emerging consensus that time plays a key role in the generation of movement across the body - future studies will discern whether and when additive or multiplicative effects dominate.

We have acknowledged this in a brief sentence: “Indeed, we have found a similar valuation of time to explain how reaching durations and speed trajectories vary with reaching distance (Wong et al., 2021).” As an aside, in that reference we measured metabolic cost of cyclic arm reaching, combined it with a linear time cost, and predicted reaching durations vs. distance and bell-shaped hand speed trajectories. Others (Shadmehr et al. Curr Biol. 2016) have proposed multiplicative (hyperbolic) temporal discounting to explain durations, but the cost formulas are not dynamical, and cannot produce trajectories. We agree with reviewer’s point, but we think the evidence for hyperbolic discounting is not strong. Linear time costs are simpler and work at least as well. This is of great interest to us, but we didn’t discuss beyond the brief mention above, because we fear it is too far afield.

Reviewer #2 (Public Review):

This paper provides a novel approach to quantifying the tradeoff between energetic optimality during walking and the valuation of time to travel a given distance. Specifically, the authors investigated the relationships between walking speed trajectories, distance traveled, and the valuation of (completion) time. Time has been proposed as a potential factor influencing movement speed, but less is understood about how individuals balance energetic optimality and time constraints during walking. The authors used a simple, sagittal-plane walking model to test competing hypotheses about how individuals optimize gait speed from gait initiation to gait termination. Their approach extends literature in the space by identifying optimal gaits for shorter, partially non-steady speed walking bouts.

The authors successfully evaluated three competing walking objectives (constant acceleration, minimum cost of transport at steady speed, and the energy-time objective), showing that the energy-time objective best matched experimental data in able-bodied adults. Although other candidate objectives may exist, the paper's findings provide a likely-generalizable explanation of how able-bodied humans select movement strategies that encompass studies of steady-speed walking.

Overall, this paper provides a foundation for future studies testing the validity of the energy-time hypothesis for human gait speed selection in able-bodied and patient populations. Extensions of this work to patient populations may explain differences in walking speed during clinical assessments and provide insight into how individual differences in time valuation impact performance on assessments. For example, understanding whether physical capacity or time valuation (or something comparable) better explains individual differences in walking speed may suggest distinct approaches for improving walking speed.

Strengths:

The authors presented a compelling rationale for the tradeoffs between energetic optimality and time and their results provide strong support for a majority of their conclusions. In particular, significant reductions in the variance of experimental speed trajectories provides good support for the scaling of speeds across individuals and the plausibility of the energy-time hypothesis. Comparison to theoretical (model-based) reductions across difference time valuation (cT) parameters would further enhance confidence in the practical significance of the variance reductions. Further, while additional work is needed to determine the range of "normal" valuations of time, the authors present experimental ranges that appear reasonable and are well explained. The computational and analytical methods are rigorous and are supported by the literature. Overall, the paper's conclusions are consistent with experimental and computational results.

The introduction of a model-based analytical approach to quantify the effects of time valuation of walking could generalize to test other cost functions, populations, or locomotion modes. Further, models of varying complexity could be implemented to test more individualized estimates of metabolic cost, ranging from 3D dynamic walking models (Faraji et al., Scientific Reports, 2018) or physiologically-detailed models (Falisse et al., Journal of The Royal Society Interface. 2019). The relatively simple set of analyses used in this paper is consistent with prior literature and should generalize across applications and populations.

The authors justified simplifications in the analysis and addressed major limitations of the paper, such as using a fixed step length in model predictions, using a 2D model, and basing energy estimates on the mechanical work of a simple model. It is unlikely that the paper's conclusions would change given additional model complexity. For example, a 3D walking model would need to control frontal plane stability. However, in able-bodied adults, valuation of frontal-plane stability during normal walking would not likely alter the overall shape of the predicted speed profiles.

Weaknesses:

The primary weakness of this work is that alternative objectives may provide similar speed profiles and thus be plausible objectives for human movement. For example, the authors tested an objective minimizing the steady-speed cost of transport. This cost function is consistent with the literature, but (as predicted) unlikely to explain acceleration and deceleration during gait. An objective more comparable to the energy-time hypothesis would be to minimize the net energy cost over the entire bout, including accelerations and decelerations. This may produce results similar to the energy-time hypothesis. However, a more complex model that incorporates non-mechanical costs (e.g., cost of body weight support) may be needed to test such objectives. Therefore, the energy-time hypothesis should be considered in the context of a simple model that may be incapable of testing certain alternative hypotheses.

We have addressed some of this comment in Essential Revisions 4.

We are unsure what is meant by “net energy over the entire bout, including accelerations and decelerations.” Our hypothesis uses total (gross) energy over the entire bout, and already includes accelerations and decelerations. If “net” refers to the customary definition of metabolic energy minus resting, then it differs from our gross cost (Fig. 6A) only in the amount of constant offset, namely resting cost. Removing the offset is equivalent to a decrease in C_T. As shown in Fig. 3, this would reduce peak speeds magnitudes but not change the shape of the speed, peak speed, and duration patterns. There is also another interpretation where the cost of walking includes only net energy, and the cost of time includes the resting metabolic rate (Fig. 6C). This interpretation yields the same predictions, the only difference is whether resting rate is treated as an energy or a time cost. We have not made further changes, because we are unsure what the reviewer meant. The difference between net and total is at most one of degree, not of qualitatively different behavior.

We do not address the proposed “cost of body weight support” because we are unsure of the definition. There is a hypothesis by Kram & Taylor (1990) that defines a metabolic cost rate proportional to body weight divided by ground contact time. It is unclear if this is what reviewer is referring to, so we did not include it in the manuscript. However, IF this is what reviewer means, we do not consider the Kram & Taylor (“K&T”) cost to be a viable hypothesis for computational models. It is a correlation observed from data, which is inadequate as a model, for several reasons. First, in a model optimization, it leads to absurd predictions, because metabolic cost could then be reduced simply by increasing stance (contact) time. A model could do so simply by walking with very long double support phases, or running with a very brief aerial phase, both of which people clearly do not do. In walking, extended double support durations result in much higher metabolic cost (Gordon et al., APMR 2009). Models must operate quite literally on whatever objective they are given, and here, a literal interpretation of K&T makes absurd predictions.

Another issue with the K&T cost is that it is not mechanistic. A mechanistic model is concerned with the forces and work performed by an actuator such as muscle. Muscles experience forces far greater than body weight, not captured by the K&T cost. Of course, overall cost for animal locomotion is roughly proportional to body weight, but what a model needs is a cost associated with its control inputs, e.g. actuator forces.

We have also examined the K&T hypothesis in previous publications. In Schroeder & Kuo (Plos Comp Biol 2021), we used a simple model of running that minimizes an energetic cost dominated by mechanical work. Even though the model has no cost similar to K&T, its predicted metabolic cost is correlated with the K&T cost. Correlation does not imply causation, which is known in this model.

We have also examined the K&T hypothesis in experimental data. In Riddick & Kuo (Sci Rep 2022), we examined human data and found that there are many variables that correlate quite well with metabolic cost, including the K&T correlate. We use human data to show how mechanical work could explain metabolic cost, and even if it does, the K&T cost appears as a correlate. In our interpretation, both model and data that experience an energetic cost proportional to mechanical work may have a number of variables correlated to energy cost. Those correlates need not have any causal influence.

There are, of course, many similar correlates that could be or have been proposed to explain the metabolic cost of running. Most such correlates are not operational enough to work in a model, and it is also difficult to predict what a reader might consider plausible, even if we do not.

We agree with this statement: “the energy-time hypothesis should be considered in the context of a simple model that may be incapable of testing certain alternative hypotheses.” In fact, in Discussion of limitations we listed other potential factors (e.g. forced leg motion, stability, 3D motion), and stated “We did not explore more complex models here, but would expect similar predictions to result if similar, pendulum-like principles of work and energetic cost apply.” We had also cited other models that include such factors and are compatible with the step-to-step transition concept. Finally, we already stated, “the Energy-Time hypothesis should be regarded as a subset of the many factors that should govern human actions, rendered here in a simple but quantitative form.” We believe this is already aligned with reviewer’s comment.

An experimental design involving an intervention to perturb the valuation of time would provide stronger support for time being a critical factor influencing gait speed trajectories. The authors noted this limitation as an area of future work.

While the results are compelling, the limited sample size and description of participants limit the obvious generalizability of the results. Older adults tend to have higher metabolic costs of walking than younger adults, which may alter the predicted time-energy relationships (Mian OS, et al., Acta physiologica. 2006). As noted in the introduction, differences in walking speeds have been observed in different living environments. General information on where participants lived (city, small town, etc...) may provide readers with insight into the generalizability of the paper's conclusions. Additionally, the experimental results figures show group-level trends, but individual-specific trends and the existence of exceptional cases are unclear.

We wish to defend the “limited sample size.” The present sample size was (in our opinion) sufficient to test the hypothesis, and we have reported confidence intervals and other statistics where appropriate. (As always, it is up to the individual reader to decide whether they are convinced or not.) It is true that the data may be insufficient for other purposes, but we cannot anticipate or address all other purposes.

We appreciate the relevant connection to aging. We have added to Discussion, “We do not know whether that family [of trajectories] also applies to older adults, who prefer slower steady speeds and expend more energy to walk the same speed (Malatesta, 2003). Perhaps an age-related valuation of time might explain some of the differences in speed.”

We agree about the participants, and have added “Subjects were recruited from the community surrounding the University of Calgary; the city has a moderately affluent population of about 1.4 M, with a developed Western culture.”

No specific reviewer recommendation was made about individual-specific trends, but there are several indicators already included in the manuscript. First, all trials from all subjects are shown in Fig. 4A. Any truly exceptional cases should be visible as substantial deviations from the group. Second, the normalization by peak speed in Fig. 4B shows how individuals tend to be fairly consistent in their preferred speeds, in that shorter and longer bouts of an individual are consistent with each other, even if some walk faster than others. Third, this observation is analyzed more quantitatively by the reduction in standard deviations with normalization (Results). Fourth, we will provide a data repository with all the data, to allow readers to inspect individuals more carefully (Data availability statement).

The authors' interpretation of clinical utility is vague and should be interpreted with caution. A simple pendulum-based walking model is unlikely to generalize to patient populations, whose gait energetics may involve greater positive and negative mechanical work (Farris et al., 2015; Holt et al., 2000). Additionally, the proposed analytical framework based on mechanical work as a proxy for the metabolic cost may not generalize to patient populations who have heterogeneous musculotendon properties and increased co-contraction (e.g., children with cerebral palsy; Ries et al., 2018). Consequently, the valuation of time for an individual could be incorrectly estimated if the estimates of metabolic cost were inaccurate. Therefore, as the authors noted for their able-bodied participants, more precise measures of metabolic rates will be critical for translating this work into clinical settings.

We agree, and did not intend to say that clinical populations must walk the same way, rather that the Normal patterns could be used as a basis of comparison. To make this clearer, we have amended the Discussion of clinical implications (new text emphasized): “it may be possible to predict the duration and steady speed for another distance, referenced from a universal family of walking trajectories. We have identified one such family that applies to healthy individuals with pendulum-like gait. Of course, some clinical conditions might be manifested by a deviance from that family, perhaps in the acceleration or deceleration phases, or in how the trajectories vary with distance. If quantified, such deviance might prove clinically useful… the characterization of distance-dependent speed trajectories can potentially provide more information than available from steady speed alone.”

We agree that the valuation of time can be inaccurate if the metabolic cost is inaccurate. That is why we did not make a precise estimate of the valuation. We have amended the text to help clarify that our rough estimates are based on previous data. In addition, our general scientific intent is to reveal behavioral sensitivities, for example of walking duration to bout distance, as opposed to absolute numerical quantities.

Author Response

Reviewer #1 (Public Review):

1) One nagging concern is that the category structure in the CNN reflects the category structure baked into color space. Several groups (e.g. Regier, Zaslavsky, et al) have argued that color category structure emerges and evolves from the structure of the color space itself. Other groups have argued that the color category structure recovered with, say, the Munsell space may partially be attributed to variation in saturation across the space (Witzel). How can one show that these properties of the space are not the root cause of the structure recovered by the CNN, independent of the role of the CNN in object recognition?

We agree that there is overlap with the previous studies on color structure. In our revision, we show that color categories are directly linked to the CNN being trained on the objectrecognition task and not the CNN per se. We repeated our analysis on a scene-trained network (using the same input set) and find that here the color representation in the final layer deviates considerably from the one created for object classification. Given the input set is the same, it strongly suggests that any reflection of the structure of the input space is to the benefit of recognizing objects (see the bottom of “Border Invariance” section; Page 7). Furthermore, the new experiments with random hue shifts to the input images show that in this case stable borders do not arise, as might be expected if the border invariance was a consequence of the chosen color space only.

A crucial distinction to previous results is also, is that in our analysis, by replacing the final layer, specifically, we look at the representation that the network has built to perform the object classification task on. As such the current finding goes beyond the notion that the color category structure is already reflected in the color space.

2) In Figure 1, it could be useful to illustrate the central observation by showing a single example, as in Figure 1 B, C, where the trained color is not in the center of the color category. In other words, if the category structure is immune to the training set, then it should be possible to set up a very unlikely set of training stimuli (ones that are as far away from the center of the color category while still being categorized most of the time as the color category). This is related to what is in E, but is distinctive for two reasons: first, it is a post hoc test of the hypothesis recovered in the data-driven way by E; and second, it would provide an illustration of the key observation, that the category boundaries do not correspond to the median distance between training colors. Figure 5 begins to show something of this sort of a test, but it is bound up with the other control related to shape.

We have now added a post-hoc test where we shift the training bands from likely to unlikely positions using the original paradigm: Retraining output layers whilst shifting training bands from the left to the right category-edge (in 9 steps) we can see the invariance to the category bounds specifically (see Supp. Inf.: Figure S11). The most extreme cases (top and bottom row) have the training bands right at the edge of the border, which are the interesting cases the reviewer refers to. We also added 7 steps in between to show how the borders shift with the bands.

Similarly, if the claim is that there are six (or seven?) color categories, regardless of the number of colors used to train the data, it would be helpful to show the result of one iteration of the training that uses say 4 colors for training and another iteration of the training that uses say 9 colors for training.

We have now included the figure presented in 1E, but for all the color iterations used (see SI: Figure S10. We are also happy to include a single iteration, but believe this gives the most complete view for what the reviewer is asking.

The text asserts that Figure 2 reflects training on a range of color categories (from 4 to 9) but doesn’t break them out. This is an issue because the average across these iterations could simply be heavily biased by training on one specific number of categories (e.g. the number used in Figure 1). These considerations also prompt the query: how did you pick 4 and 9 as the limits for the tests? Why not 2 and 20? (the largest range of basic color categories that could plausibly be recovered in the set of all languages)?

The number of output nodes was inspired by the number of basic color categories that English speakers observe in the hue spectrum (in which a number of the basic categories are not represented). We understand that this is not a strong reason, however, unfortunately the lack of studies on color categories in CNNs forced us to approach this in an explorative manner. We have adapted the text to better reflect this shortcoming (Bottom page 4). Naturally if the data would have indicated that these numbers weren’t a good fit, we would have adapted the range. (if there were more categories, we would have expected more noise and we would have increased the number of training bands to test this). As indicated above, we have now also included the classification plots for all the different counts, so the reader can review this as well (SI: Section 9).

3) Regarding the transition points in Figure 2A, indicated by red dots: how strong (transition count) and reliable (consistent across iterations) are these points? The one between red and orange seems especially willfully placed.

To answer the question on the consistency we have now included a repetition of the ResNet18, with the ResNet34, ResNet50 and ResNet101 in the SI (section 1). We have also introduced a novel section presenting the result of alternate CNNs to the SI (section S8). Despite small idiosyncrasies the general pattern of results recurs.

Concerning the red-orange border, it was not willfully placed, but we very much understand that in isolation it looks like it could simply be the result of noise. Nevertheless, the recurrence of this border in several analyses made us confident that it does reflect a meaningful invariance. Notably:

• We find a more robust peak between red and orange in the luminance control (SI section 3).

• The evolutionary algorithm with 7 borders also places a border in this position.

• We find the peak recurs in the Resnet-18 replication as well as several of the deeper ResNets and several of the other CNNs (SI section 1)

• We also find that the peak is present throughout the different layers of the ResNet-18.

4) Figure 2E and Figure 5B are useful tests of the extent to which the categorical structure recovered by the CNNs shifts with the colors used to train the classifier, and it certainly looks like there is some invariance in category boundaries with respect to the specific colors uses to train the classifier, an important and interesting result. But these analyses do not actually address the claim implied by the analyses: that the performance of the CNN matches human performance. The color categories recovered with the CNN are not perfectly invariant, as the authors point out. The analyses presented in the paper (e.g. Figure 2E) tests whether there is as much shift in the boundaries as there is stasis, but that’s not quite the test if the goal is to link the categorical behavior of the CNN with human behavior. To evaluate the results, it would be helpful to know what would be expected based on human performance.

We understand the lack of human data was a considerable shortcoming of the previous version of the manuscript. We have now collected human data in a match-to-sample task modeled on our CNN experiment. As with the CNN we find that the degree of border invariance does fluctuate considerably. While categorical borders are not exact matches, we do broadly find the same category prototypes and also see that categories in the red-to-yellow range are quite narrow in both humans and CNNs. Please, see the new “Human Psychophysics” (page 8) addition in the manuscript for more details.

5) The paper takes up a test of color categorization invariant to luminance. There are arguments in the literature that hue and luminance cannot be decoupled-that luminance is essential to how color is encoded and to color categorization. Some discussion of this might help the reader who has followed this literature.

We have added some discussion of the interaction between luminance and color categories (e.g., Lindsay & Brown, 2009) at the bottom of page 6/ top of page 7. The current analysis mainly aimed at excluding that the borders are solely based on luminance.

Related, the argument that “neighboring colors in HSV will be neighboring colors in the RGB space” is not persuasive. Surely this is true of any color space?

We removed the argument about “neighboring colors”. Our procedure requires the use of a hue spectrum that wraps around the color space while including many of the highly saturated colors that are typical prototypes for human color categories. We have elected to use the hue spectrum from the HSV color space at full saturation and brightness, which is represented by the edges of the RGB color cube. As this is the space in which our network was trained, it does not introduce any deformations into the color space. Other potential choices of color space either include strong non-linear transformations that stretch and compress certain parts of the RGB cube, or exclude a large portion of the RGB gamut (yellow in particular).

We have adapted the text to better reflect our reasoning (page 6, top of paragraph 2).

6) The paper would benefit from an analysis and discussion of the images used to originally train the CNN. Presumably, there are a large number of images that depict manmade artificially coloured objects. To what extent do the present results reflect statistical patterns in the way the images were created, and/or the colors of the things depicted? How do results on color categorization that derive from images (e.g. trained with neural networks, as in Rosenthal et al and presently) differ (or not) from results that derive from natural scenes (as in Yendrikhovskij?).

We initially hoped we could perhaps analyze differences between colors in objects and background like in Rosenthal, unfortunately in ImageNet we did not find clear differences between pixels in the bounding boxes of objects provided with ImageNet and pixels outside these boxes (most likely because the rectangular bounding boxes still contain many background pixels). However, if we look at the results from the K-means analysis presented in Figure S6 (Suppl. Inf.) of the supplemental materials and the color categorization throughout the layers in the objecttrained network (end of the first experiment on page 7) as well as the color categorization in humans (Human Psychophysics starting on page 8), we see very similar border positions arise.

7) It could be quite instructive to analyze what's going on in the errors in the output of the classifiers, as e.g. in Figure 1E. There are some interesting effects at the crossover points, where the two green categories seem to split and swap, the cyan band (hue % 20) emerges between orange and green, and the pink/purple boundary seems to have a large number of green/blue results. What is happening here?

One issue with training the network on the color task, is that we can never fully guarantee that the network is using color to resolve the task and we suspected that in some cases the network may rely on other factors as well, such as luminance. When we look at the same type of plots for the luminance-controlled task (see below left) presented in the supplemental materials we do not see these transgressions. Also, when we look at versions of the original training, but using more bands, luminance will be less reliable and we also don’t see these transgressions (see right plot below).

8) The second experiment using an evolutionary algorithm to test the location of the color boundaries is potentially valuable, but it is weakened because it pre-determines the number of categories. It would be more powerful if the experiment could recover both the number and location of the categories based on the "categorization principle" (colors within a category are harder to tell apart than colors across a color category boundary). This should be possible by a sensible sampling of the parameter space, even in a very large parameter space.

The main point of the genetic algorithm was to see whether the border locations would be corroborated by an algorithm using the principle of categorical perception. Unfortunately, an exact approach to determining the number of borders is difficult, because some border invariances are clearly stronger than others. Running the algorithm with the number of borders as a free parameter just leads to a minimal number of borders, as 100% correct is always obtained when there is only one category left. In general, as the network can simply combine categories into a class at no cost (actually, having less borders will reduce noise) it is to be expected that less classes will lead to better performance. As such, in estimating what the optimal category count would be, we would need to introduce some subjective trade-off between accuracy and class count.

9) Finally, the paper sets itself up as taking "a different approach by evaluating whether color categorization could be a side effect of learning object recognition", as distinct from the approach of studying "communicative concepts". But these approaches are intimately related. The central observation in Gibson et al. is not the discovery of warm-vscool categories (these as the most basic color categories have been known for centuries), but rather the relationship of these categories to the color statistics of objects-those parts of the scene that we care about enough to label. This idea, that color categories reflect the uses to which we put our color-vision system, is extended in Rosenthal et al., where the structure of color space itself is understood in terms of categorizing objects versus backgrounds (u') and the most basic object categorization distinction, animate versus inanimate (v'). The introduction argues, rightly in our view, that "A link between color categories and objects would be able to bridge the discrepancy between models that rely on communicative concepts to incorporate the varying usefulness of color, on the one hand, and the experimental findings laid out in this paragraph on the other". This is precisely the link forged by the observation that the warmcool category distinction in color naming correlates with object-color statistics (Gibson, 2017; see also Rosenthal et al., 2018). The argument in Gibson and Rosenthal is that color categorization structure emerges because of the color statistics of the world, specifically the color statistics of the parts of the world that we label as objects, which is the same approach adopted by the present work. The use of CNNs is a clever and powerful test of the success of this approach.

We are sorry we did not properly highlight the enormous importance of these two earlier papers in our previous version of the manuscript. We have now elaborated our description of Gibson’s work to better reflect the important relation between the usefulness of colors and color categories (Page 2, middle and Page 19 par. above methods). We think our work nicely extends the earlier work by showing that their approach works even at a more general level with more color categories,

Reply to Andy https://forum.zettelkasten.de/discussion/comment/16865#Comment_16865

Andy, I'll take you at your word. You're right that none of it requires extraordinary genius--though many who seem to exhibit extraordinary genius do have variations of these practices in their lives, and the largest proportion of them either read about them or were explicitly taught them.

With these patterns and practices being so deeply rooted in our educational systems for so long (not to mention the heavy influences of our orality and evolved thinking apparatus even prior to literacy), it's a bit difficult for many to truly guarantee that they've done these things independently without heavy cultural and societal influence. As a result, it's not a far stretch for people to evolve their own practices to what works for them and then think that they've invented something new. The common person may not be aware of the old ideas of scala naturae or scholasticism, but they certainly feel them in their daily lives. Commonplacing is not much different.

By analogy, Elon Musk might say he created the Tesla, but it's a far bigger stretch for him to say that he invented a new means of transportation, or a car, or the wheel when we know he's swimming in a culture rife with these items. Humans are historically far better at imitation than innovation. If people truly independently developed systems like these so many times, then in the evolutionary record of these practices we should expect to see more diversity than we do in practice. We might expect to see more innovation than just the plain vanilla adjacent possible. Given Margolin's age, time period, educational background, and areas of expertise, there is statistically very little chance that he hadn't seen or talked about versions of this practice with several dozens of his peers through his lifetime after which he took that tacit knowledge and created his own explicit version which worked for him.

Historian Keith Thomas talks about some of these traditions which he absorbed himself without having read some of the common advice (see London Review of Books https://www.lrb.co.uk/the-paper/v32/n11/keith-thomas/diary). He also indicates that he slowly evolved to some of the often advised practices like writing only on one side of a slip, though, like many, he completely omits to state the reason why this is good advice. We can all ignore these rich histories, but we'll probably do so at our own peril and at the expense of wasting some of our time to re-evolve the benefits.

Why are so many here (and in other fora on these topics) showing up regularly to read and talk about their experiences? They're trying to glean some wisdom from the crowds of experimenters to make improvements. In addition to the slow wait for realtime results, I've "cheated" a lot and looked at a much richer historical record of wins and losses to gain more context of our shared intellectual history. I'm reminded of one of Goethe's aphorisms from Maxims and Reflections "Inexperienced people raise questions which were answered by the wise thousands of years ago."

This line reminded me of something a friend told me recently. The last few generations of humans will be the first generations that will have living memories (Videos and audio) of them living their lives. To think that in several hundred years, someones great great great great grandchild may be able to pull up a video of us today and say to their grandchildren that this is how we used to be/look/interact with our world is immensely interesting in my opinion. We don't have videos of what life was like in the 1500's. We do have paintings and records and thus can fill in the blanks with our imaginations, but future generations won't have to employ that technique nearly as much as we do.

The story you tell yourself creates reality.

This work has been published in GigaScience Journal under a CC-BY 4.0 license (https://doi.org/10.1093/gigascience/giac034 and has published the reviews under the same license. These reviews were as follows.

Reviewer 1. Sean Walkowiak

First review: Comment 1: The authors could more clearly and accurately present and discuss sequencing and assembly approaches, including the advantages and limitations of the ONT assembly presented here

While the standards of 'quality' for assemblies are evolving, there are standard sets of 'science-based' criteria for considering the quality of a genome, such as the 14 criteria listed in the manuscript here: https://www.nature.com/articles/s41586-021-03451-0#Tab1. Many of these criteria are ambitious, particularly for wheat due to its size and complexity, and many criteria are not met using previous assembly approaches, or the approaches used in this study. It is true that CS and 10+ Wheat Genomes do not use long reads; however, these assemblies are valuable and have been rigorously validated using 10X Genomics, Hi-C, and long read data. They also perform well for TE content, BUSCO (as outlined by Tables 1 and 2 and Fig 3 in this manuscript), and they were actually used in this MS as a reference for guiding the ONT assembly. I would also expect that they have a better base pair accuracy than the assembly presented here. I therefore suggest that the authors revise their statement "these assemblies have been produced using short-read technologies and are therefore not up to the quality standard of current genome assemblies". If the authors wish to discuss assembly quality, which I recommend they should, I suggest focusing on advantages and limitations of each technology and assembly approach in a constructive way, perhaps with a stronger focus on the value of the ONT resource developed here. In regards to base pair accuracy, ONT is at a disadvantage to short reads or to PacBio. This is particularly true in the context of HiFi reads, which have increased accuracy over ONT and Illumina and have greater lengths than Illumina, but PacBio and HiFi are not discussed. This is not to say that PacBio is superior in every way, the reads from ONT are longer and these hold a significant value. As an example of differences between PacBio and ONT that might provide useful context to describe the differences between ONT and PacBio approaches, please see: https://pubmed.ncbi.nlm.nih.gov/33319909/, for differences between short read (TriTex) and PacBio, please see https://www.nature.com/articles/s41586-020-2947-8 . All of these approaches are valuable but have both advantages and limitations, with ONT also having many clear advantages and disadvantages. But these need to be clearly communicated and supported, either through the results of this study or through the literature. For example, in the discussion, the authors state that "ONT devices HAVE a real advantage over other long-read technologies". There is only one other long read sequencing technology, so are if you saying that ONT HAS a 'real advantage' over PacBio based on read length, this is valid, but can be stated more explicitly and with examples of the read lengths from this study and the literature. It is then stated that the "error rate is drastically reduced for nanopore", again this valuable and a great advancement in regards to ONT, but it would be wise not to dismiss that this error rate is still higher than PacBio HiFi, which again can be stated explicitly with support from the literature. While both of these concepts are important, after they are stated, they are not actually discussed or framed to highlight the work from this study. The true advantage of ONT, even over PacBio HiFi, is that the long reads can resolve more complex regions that span greater distances, which are abundant in wheat (see reference from above). The authors are presenting an exciting and valuable resource with this genome assembly and this assembly has advantages due to the application of ONT, for the reasons mentioned above regarding long complex regions, but these are not fully highlighted and the authors do not take full advantage of what this assembly has to offer. I think the authors should provide additional context and support related to the value and drawbacks of their ONT assembly. The advantages are discussed superficially at the gene level through a couple of examples (Fig 5), though none of these examples are supported with any significant biological data or validation analysis. There are many interesting features of genomes that are captured by ONT that are not captured well by short reads or PacBio, and it is unfortunate that these are not explored in any significant depth in the manuscript.

Comment 2: Some of the 'highlighted features' in the manuscript could be better selected/executed

This comment relates to the previous comment on having little detail on what the ONT genome is uniquely capable of providing over other approaches. Instead, the authors focus on some anomalies in the D genome as well as differences in the nanopore software for base calling. It is unclear to me what the objective is of the report on the D genome. I suspect that this may be due to differences in repeat content between D and the other subgenomes, or an artifact of the tools and analyses used. Page 6, Figures S1 and S2, may be a consequence of poor read filtering for reads that align ambiguously - i,e perhaps reads from A and B may crossmap at a greater likelihood than those from D due to differences/similarities in repeat content between subgenomes. Once reads are aligned, the alignments should be properly filtered using standard 'best practices for NGS'- I do not see that any filtering or analysis of cross mapping was performed, but I may have missed it. Once the alignments are filtered, read coverage dips and peaks can then be assessed statistically using tools such as CNVnator and cn.mops, which are designed specifically for comparative read depth analysis since depth may not be normally distributed, rather than arbitrarily looking at 2 times the median. There may be differences between genes and intergenic regions in terms of mapping accuracy, so it may be ideal to interrogate read depth for those separately. The increased gaps is also interesting and I wonder if this could be due to the read accuracy of ONT and read mapping and assembly biases when having similar subgenomes.

Nevertheless, the results and discussion on the D genome are interesting but distracting and likely reflect that the authors should take more time to explore their data and its biases before presenting this information. In summary, I believe that additional work is needed to bring value to the read depth and D genome analysis should the authors choose to include this in the manuscript. While I agree that it would be useful to communicate that a significant gain was observed when basecalling using the more accurate basecaller, the emphasis on this is disproportionate to its value in the manuscript. The observation of a better assembly when using reads from a more advanced basecaller is not something new. As for the error rate of the ONT between organisms (yeast and wheat), with a sample size of 2, I do not think that this is worth presenting or discussing in any detail. While this may just be an artifact of the DNA quality itself from two experiments, I suspect that this may be a valid result from the manuscript and due to sequencing repeats, which are more abundant in wheat, in combination with how these basecallers self train to be more accurate. While this is certainly valid, it is not novel or interesting. This result comparing species was not tested with sufficient scientific rigor/evidence, it distracts from the central result of the manuscript, and just reaffirms something that we already known about the basecalling software and challenges of sequencing homopolymers and the importance of getting accurate reads using the more advanced basecalling methods.

Comment 3: Why Renan? This comment relates to the other two comments on the selected areas of focus. The biological story, which was on gliadins, was of some value and highlighted some of the advantages of an ONT assembly, but this was not supported by any significant biological data. Renan is a well-known cultivar with abundant genomic data, mapping populations, trait data for diseases, etc. It is unfortunate that the authors could not use the genome to dig deeper to more thoroughly demonstrate the value of this assembly specifically in the context of ONT and genomics of wheat or the biology of wheat and Renan, specifically. With abundant QTL data available specifically for Renan, these could have easily been anchored to the assembly to highlight novel transcripts from the RNAseq from this study, just as an example. Even the comparisons of the Renan assembly to other available assemblies was mostly superficial and did not highlight in significant detail the value of having an ONT assembly or the value of having data specifically for Renan. While a detailed 'biological story' may be beyond the scope of this manuscript, there was minimal effort to highlight the value of the assembly, and this comment is more of a larger reflection that more could have been done to highlight the value of the genome to support the author's vague claims that the genome "will benefit the wheat community and help breeding programs".

Minor Comments The absence of numbered lines made it difficult to provide more detailed feedback, but there are minor items throughout, so I suggest numbering the lines and also giving the manuscript a thorough review. I appreciate that the authors present and suggest methods for future assembly of complex genomes using ONT, but unlike the abstract states 'we also provide the methodological standards to generate high-quality assemblies of complex genomes'. I would argue that the standards used for ONT assembly are known and are not established here. I would also suggest caution when stating that the methods here should be considered the 'standard' for the reasons indicated in Comment 1 regarding other approaches used to assemble complex genomes, such as PacBio/HiFi, and the lack of a proper investigation/discussion/comparison of assembly quality.

Page 2: last line - what is the abbreviation ca. ? Table 1: Busco is presented twice with different values. Table 1 and 2 use different versions of RefSeq, I would stick to one version. It is unclear to me what trend or result is that the authors are trying to present in figure 1, which I would say is common for circos plots. Presenting data 'for the sake of presenting it' is not terribly valuable and I would encourage the authors to use the figures to present a trend or result that is impactful. In addition, the data that is presented is not presented clearly, and is cryptic. The roman numerals in the figure caption for Figure 1 are not actually in the figure. The caption also indicate that the dots indicate lower and higher values, but not of what - perhaps density of gaps? The color scales are not presented for each track. Two of the color scale pallets also look similar.

Page 6: 62% of exons were identical, which means 48% had SNPs, so the authors argue that SNPs are therefore rare at 48% of exons? I do not think that 48% of exons having SNPs is rare, I think it that this would mean that nearly half of exons have SNPs, so this is therefore common. Perhaps this statistic is misleading and the focus should instead be on the 0.7% divergence. How does this value compare with other within species comparisons of gene content and could this be an artifact of ONT accuracy? This question relates to a general comment that the authors could do better at bringing relevant comparisons or parallels in from the literature throughout the manuscript to bring value to any findings or insights they are presenting. Particularly in the context of other ONT assemblies.

Page 7, capitalize the T for technology, it is part of the name of the company and is a proper noun. This is repeated elsewhere.

Page 7: 'on wheat'? this statement could be written more clearly The way that the text is worded, it sounds like the basis for selecting the SmartDenovo assembly was the number of unknown bases, when I suspect it was actually a multitude of factors (BUSCO, gene or TE content, assembly stats, etc). While I do not question the selection of the assembly, I do suggest a clearer presentation of the information. I appreciate that the authors presented the data from multiple assemblers, one of the concerns with ONT is that the read accuracy is low and this may lead to issues in assembly of complex polyploids with similar subgenomes. I suspect that based on this study, it is clear that this is a valid concern for some assemblers, but may have been overcome in others. Though none of this is explored or discussed. Again, is there any information in the literature contrasting assemblers that could provide insights into what you observed?

Searches at 90% identify and coverage for genes and TEs is not strict, especially with genomes that have highly identical subgenomes. If you reduce your thresholds enough, all features will map to your genome.....

The choice of language is often objective or not representative of the results. For example, the 'extremely' similar TE content between Renan and CS. Why not say it is similar and actually report a value or a % difference. This would be more concise and informative than using vague and overzealous language. Page 8, short reads (dash or no dash?) The font sizes in Figure 2 are very small.

The RNAseq is not really presented at all, except in the Materials and Methods. I thought the genes were ab initio predicted until I saw RNAseq in the materials and methods. I suggest at least making a note of RNAseq into the results and/or discussion since this additional effort does bring added value to the annotations and the manuscript. The discussion says de novo annotations, but I suggest explicitly stating that RNAseq was performed.

Figure 3 C and D do not have horizontal axis labels, the top should be labelled as subgenome, bottom as chromosome, and the vertical axis (not the top) should be labelled as number of gaps and chromosome length. Same comment for labelling of vertical axis for panels A and B, horizontal axis should be labelled as genome assemblies, which are reflected in the pallet/legend. Note that many of the colours in this pallet are similar and difficult to differentiate, it may actually take less space to label the bars with each wheat line to make it less cryptic.

How were the dotplots in figure 4 generated? Perhaps I missed it in the materials and methods. Also one of the axis have labels or units, etc.

Much of the text in Figure 5 is too small and illegible.

Page 10: The discussion is superficial and vague and should provide an accurate and pragmatic discussion of the results in the context of the literature. For example, the manuscript boasts a 'higher resolution'... but of what? Perhaps 'complex repetitive regions'? To reiterate my previous comment on the lack of literature support throughout the manuscript - Were these 'higher resolutions' of <complex repetitive regions> comparable to what was observed in the literature when ONT was applied to other systems? Again, these advantages of ONT and the assembly could be more thoroughly

Re-review:

The revised manuscript addresses the major concerns/comments. The assembly and its report are an exciting new resource for the wheat community. I only have one very minor comment below:

When writing variety names in text and figures, it is important to be exact because there are many varieties with similar names internationally. CDC Stanley, not "Stanley"; CDC Landmark, not "Landmark"; "LongReach Lancer", not "Lancer", not "LongRead Lancer" - typo on line 308. I suggest performing a thorough check throughout.

https://readwriterespond.com/2022/11/commonplace-book-a-verb-or-a-noun/

Sometimes the root question is "what to I want to do this for?" Having an underlying reason can be hugely motivating.

Are you collecting examples of things for students? (seeing examples can be incredibly powerful, especially for defining spaces) for yourself? Are you using them for exploring a particular space? To clarify your thinking/thought process? To think more critically? To write an article, blog, or book? To make videos or other content?

Your own website is a version of many of these things in itself. You read, you collect, you write, you interlink ideas and expand on them. You're doing it much more naturally than you think.

I find that having an idea of the broader space, what various practices look like, and use cases for them provides me a lot more flexibility for what may work or not work for my particular use case. I can then pick and choose for what suits me best, knowing that I don't have to spend as much time and effort experimenting to invent a system from scratch but can evolve something pre-existing to suit my current needs best.

It's like learning to cook. There are thousands of methods (not even counting cuisine specific portions) for cooking a variety of meals. Knowing what these are and their outcomes can be incredibly helpful for creatively coming up with new meals. By analogy students are often only learning to heat water to boil an egg, but with some additional techniques they can bake complicated French pâtissier. Often if you know a handful of cooking methods you can go much further and farther using combinations of techniques and ingredients.

What I'm looking for in the reading, note taking, and creation space is a baseline version of Peter Hertzmann's 50 Ways to Cook a Carrot combined with Michael Ruhlman's Ratio: The Simple Codes Behind the Craft of Everyday Cooking. Generally cooking is seen as an overly complex and difficult topic, something that is emphasized on most aspirational cooking shows. But cooking schools break the material down into small pieces which makes the processes much easier and more broadly applicable. Once you've got these building blocks mastered, you can be much more creative with what you can create.

How can we combine these small building blocks of reading and note taking practices for students in the 4th - 8th grades so that they can begin to leverage them in high school and certainly by college? Is there a way to frame them within teaching rhetoric and critical thinking to improve not only learning outcomes, but to improve lifelong learning and thinking?

https://www.youtube.com/watch?v=zCLCIw-HSJc

I'm curious if you knew if Nelson, Engelbart or any of their contemporaries had/maintained/used commonplace books or card indexes as precursors of their computing work? That is, those along the lines of those most commonly used by academics, for example as described by Markus Krajewski in Paper Machines (MIT Press, 2011) or even Beatrice Webb's Appendix C on Note Taking in My Apprenticeship (Longmans, 1926) in which she describes a slip (or index card)-based database method of scientific note taking. I've always felt that Vannevar Bush held things back unnecessarily by not mentioning commonplace book traditions in As We May Think.

Author Response

Reviewer #1 (Public Review):

The authors define regulatory networks across 77 tissue contexts using software they have previously published (PECA2, Duren et al. 2020). Each regulatory network is a set of nodes (transcription factors (TF), target genes (TG), and regulatory elements (RE)) and edges (regulatory scores connecting the nodes). For each context, the authors define context-specific REs, as those that do not overlap REs from any of the other 76 contexts, and context-specific regulatory networks as the collection of TFs, TGs, and REs connected to at least one context-specific RE. This approach essentially creates annotations that are aggregated across genes, elements, and specific contexts. For each tissue, the authors use linkage disequilibrium score regression (LDSC) to calculate enrichment for complex trait heritability within the set of all REs from the corresponding context-specific regulatory network. Heritability enrichments in context-specific regulatory network REs are compared with heritability enrichments in regions defined using other approaches.

We thank the reviewers for the pertinent and precise summary of our paper.

Reviewer #2 (Public Review):

In this manuscript the authors develop a method, SpecVar, to perform heritability estimation from regulatory networks derived from gene expression and chromatin accessibility data. They apply this approach to public datasets available in ENCODE and Roadmap Epigenomics consortia as well as GWAS phenotype associations in UK Biobank. It promises to be a powerful method to interpret mechanisms from genetic associations. Below are some strengths and weaknesses of the paper.

Strengths

• The method performs heritability enrichment on two major genomic data types: gene expression and chromatin accessibility.

• This method leverages gene regulatory networks to perform the heritability estimation, which may better capture complex disease architecture.

• The authors perform an extensive comparison to other LDSC-based approaches using different tissue datasets.

Weaknesses

(1) This approach may represent a modest advance over existing LDSC methods when looking at other complex traits.

(2) The authors only compare with LDSC using different functional annotations as input, which may not be appropriate. A more broad comparison with other heritability methods would be helpful.

(3) The method seems to be applied to "paired" data, but this is still bulk profiles not paired single-cell RNA/ATAC data.

The authors successfully applied a regulatory network approach to improving the heritability estimation of complex traits by using both gene expression and chromatin accessibility data. While the results could be further strengthened by comparing them to other network and non-network-based methods, it provides important insight into a few traits beyond the standard LDSC model with different functional annotations.

Given that this method is based on the widely used LDSC approach it should be broadly applied in the field. However, the authors should consider adapting this to single-cell data as well as admixed human population genetic data.

We thank the reviewer for the positive comment on our work by specifically pointing out that SpecVar is a powerful method to interpret mechanisms from genetic associations. We appreciate that the reviewer’s summarized “Strength” part well captures our major contribution in building an atlas of regulatory networks by integrating paired gene expression and chromatin accessibility data, leveraging regulatory networks to perform the heritability enrichment, and identifying relevant tissues and estimate relevance correlation. We also thank the reviewer for pointing out the weakness to further enhance our results. To address the comments, we (1) performed ablation studies and added more description to clarify the novelty of our methods; (2) conducted extensive comparison to another network-based method CoCoNet and non-network-based method RolyPoly; (3) discussed the promising direction in identification of relevant contexts at cell type level by leveraging single cell multi-omics profiles and application on admixed populations.

Reviewer #3 (Public Review):

Identifying the critical tissues and cell types in which genetic variants exert their effects on complex traits is an important question that has attracted increasing attention. Feng et al propose a new method, SpecVar, to first construct context-specific regulatory networks by integrating tissue-specific chromatin states and gene expression data, and then run stratified LD score regression (LDSC) to test if the constructed regulatory network in tissue is significantly associated with the trait, measured by a statistic called trait relevance score in this study. They apply their method to 6 traits for which there exists prior evidence on the most relevant tissues in the literature, and then further apply to 206 traits in the UK Biobank. They find that compared to LDSC using other sources of information to define context-specific annotations, their method can "improve heritability enrichment", "accurately detect relevant tissues", helps to "interpret SNPs" identified from GWAS, and "better reveals shared heritability and regulations of phenotypes" between traits.

We thank the reviewer for the summary and appreciation of our efforts to address the important question: identifying the critical tissues and cell types in which genetic variants exert their effects on complex traits.

However, I think it requires more work to understand where exactly the benefits come from and the statistical properties of their proposed test statistic (e.g., how to perform hypothesis tests with their relevance score and whether the false positive rate is under control). In addition, it's not clear to me what they can conclude about the shared heritability (which means genetic correlation) by comparing their relevance score correlation across tissues to the phenotypic correlation between traits.

We thank the reviewer’s advice to do more work to enhance the statistical rigorousness of SpecVar. We have added the significant test of heritability enrichment and our proposed R score in the revision. We also clarified that SpecVar can use common relevant contexts and shared SNP-associated regulatory networks as potential explanation for the correlation between traits.

They show that SpecVar gives much higher heritability enrichment than the other methods in the trait-relevant tissues (Fig. 2). The fold enrichment from SpecVar is extremely high, e.g., more than 600x in the right lobe of the liver for LDL. First, I think a standard error should be given so that the significance of the differences can be assessed. Second, it is very rare (hence suspicious) to observe such a huge enrichment. Since SpecVar is based on LDSC, the same methodology that other methods in comparison depend on, the differences to the other methods must come from the set of SNPs annotated for each tissue. I think it is important to understand the difference between the SpecVar annotated SNPs and those from other methods. For example, is the extra heritability enrichment mainly from the SpecVar-specific annotation or from the intersection narrowed down by SpecVar?

The reviewer has pinpointed a question about one important advantage of our method to improve heritability enrichment. We addressed this question by first providing standard errors, p values, and q values of heritability enrichment. Second, we conduct the ablation analysis to study the source of extra heritability enrichment. This question greatly helps us to clarify the main contribution of our method.

They propose to use the relevance score (R score) to prioritise trait-relevant tissues. In Fig. 3, they show tissue-trait pairs with the highest R scores, and from there they prioritise several tissues for each trait (Table 1). I can see that some tissue has an outstanding R score, however, it is not clear to me where they draw the line to declare a positive result. The threshold doesn't seem to be even consistent across traits. For example, for LDL, only the right lobe of the liver is identified although other tissues have R scores greater than 100, whereas, for EA, Ammor's horn and adrenal gland are identified although their R scores are apparently smaller than 100. It seems to me they use some subjective criteria to pick the results. It leads to a serious question on how to apply their R score in a hypothesis test: how to measure the uncertainty of their R score? What significance threshold should be used? Whether the false positive rate is under control? (Without knowing these statistical properties, readers won't be able to use this method with confidence in their own research.

We thank the reviewer to raise the question about the hypothesis test of the R score. We used the block Jackknife stratagem to estimate standard errors, p values, and q values in our revision. We added the new result to the main text and they greatly enhanced the statistical rigorousness of our method.

Another related comment to the above is to investigate false positive associations, they should show the results for all tissues tested to see if SpecVar tends to give higher R scores even in tissues that are not relevant to the trait. It would also be useful to include some negative control traits, such as height for brain tissues.

We agree that negative control is important and the six phenotypes in our manuscript are negative for each other. For example, LDL is relevant to liver tissue and not relevant to brain tissue. Educational attainment is relevant to brain tissue but not relevant to liver tissue.

Fig. 3 shows that tissues prioritised by LDSC-SAP and LDSC-SEG seem to make less sense than those from SpecVar. However, some of the results are not consistent with the LDSC-SEG paper (Finucane et al 2018). For example, LDL was significantly associated with the liver in Finucane et al (Fig. 2), but not in this study. How to explain the difference? (Question 3)

We checked the results in Figure 3 and found that even though the liver was not ranked to be top 5 tissues, it has a significant P-value to LDL in our implementation. There is indeed some difference in heritability enrichment and P-value between the LDSC-SEG paper and our implementation. And the difference was from the different sets of tissues (77 tissues in our paper and 53 tissues in the LDSC-SEG paper) for the two applications.

The authors highlight an example where SpecVar facilitates the interpretation of GWAS signals near FOXC2. They find GWAS-significant SNPs located in a CNCC-specific RE downstream of FOXC2 and reason these SNPs affect brain shape by regulating the expression of FOXC2. I think more work can be done to consolidate the conclusion. For example, if the GWAS signals are colocalised with the eQTL for FOXC2 in the brain. Also, note that the top GWAS signal is actually on the left of the CNCC-specific RE (Fig. 4b). A deeper investigation should be warranted.

We agree that more work should be done to consolidate the regulation of FOXC2. In our revision, we used the HiChIP loop in the brain to support the SNP-associated regulation of FOXC2. We also thank the reviewer’s suggestion for the idea of eQTL colocalization and we conduct eQTL colocalization analysis on our method-revealed SNP-associated regulation to show our method can facilitate the fine mapping of GWAS signals. Lastly, brain shape is a complex trait and may be relevant to multiple tissues. Hence it is reasonable to suspect that the top GWAS signal may be active in other relevant tissues’ regulatory elements.

They show that SpecVar's relevance score correlation across tissues can better approximate phenotypic correlation between traits. However, the estimation of the phenotypic correlation between traits is neither very interesting nor a thing difficult to do (it can be directly estimated from GWAS summary statistics). A more interesting question is to which extent the observed phenotypic correlation is due to common genetic factors acting in the shared tissues/cell types/pathways/regulatory networks between traits. Note that in their Abstract, they use words "depict shared heritability and regulations" but I don't seem to see results supporting that.

We are sorry that we didn’t make it clear how SpecVar “depict shared heritability and regulations”. We added more results and one example in the UKBB application to show SpecVar can use common relevant contexts and shared SNP-associated regulatory networks as potential explanation for the correlation between traits.

Line 396-402: "For example, ... heritability could select most relevant tissues ... but failed to get correct tissues for other phenotypes ... P-value could obtain correct tissues for CP ... but failed to get correct tissues for ... SpecVar could prioritize correct relevant tissues for all the six phenotypes." Honestly, I find hard to judge which tissues are "correct" or "incorrect" for a trait in real life. It would be more straightforward to compare methods using simulation where we know which tissues are causal.

We thank the reviewers to pinpoint the improper statement of “correct”. It is difficult to find phenotypes with gold-standard relevant tissues and we used six relatively well-studied phenotypes with prior knowledge of possible relevant tissues in our paper. We revised the “correct” statement in our revision.

Author Response

Reviewer #1 (Public Review):

Trudel and colleagues aimed to uncover the neural mechanisms of estimating the reliability of the information from social agents and non-social objects. By combining functional MRI with a behavioural experiment and computational modelling, they demonstrated that learning from social sources is more accurate and robust compared with that from non-social sources. Furthermore, dmPFC and pTPJ were found to track the estimated reliability of the social agents (as opposed to the non-social objects). The strength of this study is to devise a task consisting of the two experimental conditions that were matched in their statistical properties and only differed in their framing (social vs. non-social). The novel experimental task allows researchers to directly compare the learning from social and non-social sources, which is a prominent contribution of the present study to social decision neuroscience.

Thank you so much for your positive feedback about our work. We are delighted that you found that our manuscript provided a prominent contribution to social decision neuroscience. We really appreciate your time to review our work and your valuable comments that have significantly helped us to improve our manuscript further.

One of the major weaknesses is the lack of a clear description about the conceptual novelty. Learning about the reliability/expertise of social and non-social agents has been of considerable concern in social neuroscience (e.g., Boorman et al., Neuron 2013; and Wittmann et al., Neuron 2016). The authors could do a better job in clarifying the novelty of the study beyond the previous literature.

We understand the reviewer’s comment and have made changes to the manuscript that, first, highlight more strongly the novelty of the current study. Crucially, second, we have also supplemented the data analyses with a new model-based analysis of the differences in behaviour in the social and non-social conditions which we hope makes clearer, at a theoretical level, why participants behave differently in the two conditions.

There has long been interest in investigating whether ‘social’ cognitive processes are special or unique compared to ‘non-social’ cognitive processes and, if they are, what makes them so. Differences between conditions could arise during the input stage (e.g. the type of visual input that is processed by social and non-social system), at the algorithm stage (e.g. the type of computational principles that underpin social versus non-social processes) or, even if identical algorithms are used, social and non-social processes might depend on distinct anatomical brain areas or neurons within brain areas. Here, we conducted multiple analyses (in figures 2, 3, and 4 in the revised manuscript and in Figure 2 – figure supplement 1, Figure 3 – figure supplement 1, Figure 4 – figure supplement 3, Figure 4 – figure supplement 4) that not only demonstrated basic similarities in mechanism generalised across social and non-social contexts, but also demonstrated important quantitative differences that were linked to activity in specific brain regions associated with the social condition. The additional analyses (Figure 4 – figure supplement 3, Figure 4 – figure supplement 4) show that differences are not simply a consequence of differences in the visual stimuli that are inputs to the two systems1, nor does the type of algorithm differ between conditions. Instead, our results suggest that the precise manner in which an algorithm is implemented differs when learning about social or non-social information and that this is linked to differences in neuroanatomical substrates.

The previous studies mentioned by the reviewer are, indeed, relevant ones and were, of course, part of the inspiration for the current study. However, there are crucial differences between them and the current study. In the case of the previous studies by Wittmann, the aim was a very different one: to understand how one’s own beliefs, for example about one’s performance, and beliefs about others, for example about their performance levels, are combined. Here, however, instead we were interested in the similarities and differences between social and non-social learning. It is true that the question resembles the one addressed by Boorman and colleagues in 2013 who looked at how people learned about the advice offered by people or computer algorithms but the difference in the framing of that study perhaps contributed to authors’ finding of little difference in learning. By contrast, in the present study we found evidence that people were predisposed to perceive stability in social performance and to be uncertain about non-social performance. By accumulating evidence across multiple analyses, we show that there are quantitative differences in how we learn about social versus non-social information, and that these differences can be linked to the way in which learning algorithms are implemented neurally. We therefore contend that our findings extend our previous understanding of how, in relation to other learning processes, ‘social’ learning has both shared and special features.

We would like to emphasize the way in which we have extended several of the analyses throughout the revision. The theoretical Bayesian framework has made it possible to simulate key differences in behaviour between the social and non-social conditions. We explain in our point-by-point reply below how we have integrated a substantial number of new analyses. We have also more carefully related our findings to previous studies in the Introduction and Discussion.

Introduction, page 4:

[...] Therefore, by comparing information sampling from social versus non-social sources, we address a long-standing question in cognitive neuroscience, the degree to which any neural process is specialized for, or particularly linked to, social as opposed to non-social cognition 2–9. Given their similarities, it is expected that both types of learning will depend on common neural mechanisms. However, given the importance and ubiquity of social learning, it may also be that the neural mechanisms that support learning from social advice are at least partially specialized and distinct from those concerned with learning that is guided by nonsocial sources. However, it is less clear on which level information is processed differently when it has a social or non-social origin. It has recently been argued that differences between social and non-social learning can be investigated on different levels of Marr’s information processing theory: differences could emerge at an input level (in terms of the stimuli that might drive social and non-social learning), at an algorithmic level or at a neural implementation level 7. It might be that, at the algorithmic level, associative learning mechanisms are similar across social and non-social learning 1. Other theories have argued that differences might emerge because goal-directed actions are attributed to social agents which allows for very different inferences to be made about hidden traits or beliefs 10. Such inferences might fundamentally alter learning about social agents compared to non-social cues.

Discussion, page 15:

[…] One potential explanation for the assumption of stable performance for social but not non-social predictors might be that participants attribute intentions and motivations to social agents. Even if the social and non-social evidence are the same, the belief that a social actor might have a goal may affect the inferences made from the same piece of information 10. Social advisors first learnt about the target’s distribution and accordingly gave advice on where to find the target. If the social agents are credited with goal-directed behaviour then it might be assumed that the goals remain relatively constant; this might lead participants to assume stability in the performances of social advisors. However, such goal-directed intentions might not be attributed to non-social cues, thereby making judgments inherently more uncertain and changeable across time. Such an account, focussing on differences in attribution in social settings aligns with a recent suggestion that any attempt to identify similarities or differences between social and non-social processes can occur at any one of a number of the levels in Marr’s information theory 7. Here we found that the same algorithm was able to explain social and non-social learning (a qualitatively similar computational model could explain both). However, the extent to which the algorithm was recruited when learning about social compared to non-social information differed. We observed a greater impact of uncertainty on judgments about social compared to non-social information. We have shown evidence for a degree of specialization when assessing social advisors as opposed to non-social cues. At the neural level we focused on two brain areas, dmPFC and pTPJ, that have not only been shown to carry signals associated with belief inferences about others but, in addition, recent combined fMRI-TMS studies have demonstrated the causal importance of these activity patterns for the inference process […]

Another weakness is the lack of justifications of the behavioural data analyses. It is difficult for me to understand why 'performance matching' is suitable for an index of learning accuracy. I understand the optimal participant would adjust the interval size with respect to the estimated reliability of the advisor (i.e., angular error); however, I am wondering if the optimal strategy for participants is to exactly match the interval size with the angular error. Furthermore, the definitions of 'confidence adjustment across trials' and 'learning index' look arbitrary.

First, having read the reviewer’s comments, we realise that our choice of the term ‘performance matching’ may not have been ideal as it indeed might not be the case that the participant intended to directly match their interval sizes with their estimates of advisor/predictor error. Like the reviewer, our assumption is simply that the interval sizes should change as the estimated reliability of the advisor changes and, therefore, that the intervals that the participants set should provide information about the estimates that they hold and the manner in which they evolve. On re-reading the manuscript we realised that we had not used the term ‘performance matching’ consistently or in many places in the manuscript. In the revised manuscript we have simply removed it altogether and referred to the participants’ ‘interval setting’.

Most of the initial analyses in Figure 2a-c aim to better understand the raw behaviour before applying any computational model to the data. We were interested in how participants make confidence judgments (decision-making per se), but also how they adapt their decisions with additional information (changes or learning in decision making). In the revised manuscript we have made clear that these are used as simple behavioural measures and that they will be complemented later by more analyses derived from more formal computational models.

In what we now refer to as the ‘interval setting’ analysis (Figure 2a), we tested whether participants select their interval settings differently in the social compared to non-social condition. We observe that participants set their intervals closer to the true angular error of the advisor/predictor in the social compared to the non-social condition. This observation could arise in two ways. First, it could be due to quantitative differences in learning despite general, qualitative similarity: mechanisms are similar but participants differ quantitatively in the way that they learn about non-social information and social information. Second, it could, however, reflect fundamentally different strategies. We tested basic performance differences by comparing the mean reward between conditions. There was no difference in reward between conditions (mean reward: paired t-test social vs. non-social, t(23)= 0.8, p=0.4, 95% CI= [-0.007 0.016]), suggesting that interval setting differences might not simply reflect better or worse performance in social or non-social contexts but instead might reflect quantitative differences in the processes guiding interval setting in the two cases.

In the next set of analyses, in which we compared raw data, applied a computational model, and provided a theoretical account for the differences between conditions, we suggest that there are simple quantitative differences in how information is processed in social and nonsocial conditions but that these have the important impact of making long-term representations – representations built up over a longer series of trials – more important in the social condition. This, in turn, has implications for the neural activity patterns associated with social and non-social learning. We, therefore, agree with the reviewer, that one manner of interval setting is indeed not more optimal than another. However, the differences that do exist in behaviour are important because they reveal something about the social and non-social learning and its neural substrates. We have adjusted the wording and interpretation in the revised manuscript.

Next, we analysed interval setting with two additional, related analyses: interval setting adjustment across trials and derivation of a learning index. We tested the degree to which participants adjusted their interval setting across trials and according to the prediction error (learning index, Figure f); the latter analysis is very similar to a trial-wise learning rate calculated in previous studies11. In contrast to many other studies, the intervals set by participants provide information about the estimates that they hold in a simple and direct way and enable calculation of a trial-wise learning index; therefore, we decided to call it ‘learning index’ instead of ‘learning rate’ as it is not estimated via a model applied to the data, but instead directly calculated from the data. Arguably the directness of the approach, and its lack of dependence on a specific computational model, is a strength of the analysis.

Subsequently in the manuscript, a new analysis (illustrated in new Figure 3) employs Bayesian models that can simulate the differences in the social and non-social conditions and demonstrate that a number of behavioural observations can arise simply as a result of differences in noise in each trial-wise Bayesian update (Figure 3 and specifically 3d; Figure 3 – figure supplement 1b-c). In summary, the descriptive analyses in Figure 2a-c aid an intuitive understanding of the differences in behaviour in the social and non-social conditions. We have then repeated these analyses with Bayesian models incorporating different noise levels and showed that in such a way, the differences in behaviour between social and non-social conditions can be mimicked (please see next section and manuscript for details).

We adjusted the wording in a number of sections in the revised manuscript such as in the legend of Figure 2 (figures and legend), Figure 4 (figures and legend).

Main text, page 5:

The confidence interval could be changed continuously to make it wider or narrower, by pressing buttons repeatedly (one button press resulted in a change of one step in the confidence interval). In this way participants provided what we refer to as an ’interval setting’.

We also adjusted the following section in Main text, page 6:

Confidence in the performance of social and non-social advisors

We compared trial-by-trial interval setting in relation to the social and non-social advisors/predictors. When setting the interval, the participant’s aim was to minimize it while ensuring it still encompassed the final target position; points were won when it encompassed the target position but were greater when it was narrower. A given participant’s interval setting should, therefore, change in proportion to the participant’s expectations about the predictor’s angular error and their uncertainty about those expectations. Even though, on average, social and non-social sources did not differ in the precision with which they predicted the target (Figure 2 – figure supplement 1), participants gave interval settings that differed in their relationships to the true performances of the social advisors compared to the non-social predictors. The interval setting was closer to the angular error in the social compared to the non-social sessions (Figure 2a, paired t-test: social vs. non-social, t(23)= -2.57, p= 0.017, 95% confidence interval (CI)= [-0.36 -0.4]). Differences in interval setting might be due to generally lower performance in the nonsocial compared to social condition, or potentially due to fundamentally different learning processes utilised in either condition. We compared the mean reward amounts obtained by participants in the social and non-social conditions to determine whether there were overall performance differences. There was, however, no difference in the reward received by participants in the two conditions (mean reward: paired t-test social vs. non-social, t(23)= 0.8, p=0.4, 95% CI= [-0.007 0.016]), suggesting that interval setting differences might not simply reflect better or worse performance

Discussion, page 14:

Here, participants did not match their confidence to the likely accuracy of their own performance, but instead to the performance of another social or non-social advisor. Participants used different strategies when setting intervals to express their confidence in the performances of social advisors as opposed to non-social advisors. A possible explanation might be that participants have a better insight into the abilities of social cues – typically other agents – than non-social cues – typically inanimate objects.

As the authors assumed simple Bayesian learning for the estimation of reliability in this study, the degree/speed of the learning should be examined with reference to the distance between the posterior and prior belief in the optimal Bayesian inference.

We thank the reviewer for this suggestion. We agree with the reviewer that further analyses that aim to disentangle the underlying mechanisms that might differ between both social and non-social conditions might provide additional theoretical contributions. We show additional model simulations and analyses that aim to disentangle the differences in more detail. These new results allowed clearer interpretations to be made.

In the current study, we showed that judgments made about non-social predictors were changed more strongly as a function of the subjective uncertainty: participants set a larger interval, indicating lower confidence, when they were more uncertain about the non-social cue’s accuracy to predict the target. In response to the reviewer’s comments, the new analyses were aimed at understanding under which conditions such a negative uncertainty effect might emerge.

Prior expectations of performance First, we compared whether participants had different prior expectations in the social condition compared to the non-social condition. One way to compare prior expectations is by comparing the first interval set for each advisor/predictor. This is a direct readout of the initial prior expectation with which participants approach our two conditions. In such a way, we test whether the prior beliefs before observing any social or non-social information differ between conditions. Even though this does not test the impact of prior expectations on subsequent belief updates, it does test whether participants have generally different expectations about the performance of social advisors or non-social predictors. There was no difference in this measure between social or non-social cues (Figure below; paired t-test social vs. non-social, t(23)= 0.01, p=0.98, 95% CI= [-0.067 0.68]).

Figure. Confidence interval for the first encounter of each predictor in social and non-social conditions. There was no initial bias in predicting the performance of social or non-social predictors.

Learning across time We have now seen that participants do not have an initial bias when predicting performances in social or non-social conditions. This suggests that differences between conditions might emerge across time when encountering predictors multiple times. We tested whether inherent differences in how beliefs are updated according to new observations might result in different impacts of uncertainty on interval setting between social and non-social conditions. More specifically, we tested whether the integration of new evidence differed between social and non-social conditions; for example, recent observations might be weighted more strongly for non-social cues while past observations might be weighted more strongly for social cues. This approach was inspired by the reviewer’s comments about potential differences in the speed of learning as well as the reduction of uncertainty with increasing predictor encounters. Similar ideas were tested in previous studies, when comparing the learning rate (i.e. the speed of learning) in environments of different volatilities 12,13. In these studies, a smaller learning rate was prevalent in stable environments during which reward rates change slower over time, while higher learning rates often reflect learning in volatile environments so that recent observations have a stronger impact on behaviour. Even though most studies derived these learning rates with reinforcement learning models, similar ideas can be translated into a Bayesian model. For example, an established way of changing the speed of learning in a Bayesian model is to introduce noise during the update process14. This noise is equivalent to adding in some of the initial prior distribution and this will make the Bayesian updates more flexible to adapt to changing environments. It will widen the belief distribution and thereby make it more uncertain. Recent information has more weight on the belief update within a Bayesian model when beliefs are uncertain. This increases the speed of learning. In other words, a wide distribution (after adding noise) allows for quick integration of new information. On the contrary, a narrow distribution does not integrate new observations as strongly and instead relies more heavily on previous information; this corresponds to a small learning rate. So, we would expect a steep decline of uncertainty to be related to a smaller learning index while a slower decline of uncertainty is related to a larger learning index. We hypothesized that participants reduce their uncertainty quicker when observing social information, thereby anchoring more strongly on previous beliefs instead of integrating new observations flexibly. Vice versa, we hypothesized a less steep decline of uncertainty when observing non-social information, indicating that new information can be flexibly integrated during the belief update (new Figure 3a).

We modified the original Bayesian model (Figure 2d, Figure 2 – figure supplement 2) by adding a uniform distribution (equivalent to our prior distribution) to each belief update – we refer to this as noise addition to the Bayesian model14,21 . We varied the amount of noise between δ = [0,1], while δ= 0 equals the original Bayesian model and δ= 1 represents a very noisy Bayesian model. The uniform distribution was selected to match the first prior belief before any observation was made (equation 2). This δ range resulted in a continuous increase of subjective uncertainty around the belief about the angular error (Figure 3b-c). The modified posterior distribution denoted as 𝑝′(σ x) was derived at each trial as follows:

We applied each noisy Bayesian model to participants’ choices within the social and nonsocial condition.

The addition of a uniform distribution changed two key features of the belief distribution: first, the width of the distribution remains larger with additional observations, thereby making it possible to integrate new observations more flexibly. To show this more clearly, we extracted the model-derived uncertainty estimate across multiple encounters of the same predictor for the original model and the fully noisy Bayesian model (Figure 3 – figure supplement 1). The model-derived ‘uncertainty estimate’ of a noisy Bayesian model decays more slowly compared to the ‘uncertainty estimate’ of the original Bayesian model (upper panel). Second, the model-derived ‘accuracy estimate’ reflects more recent observations in a noisy Bayesian model compared to the ‘accuracy estimate’ derived from the original Bayesian model, which integrates past observations more strongly (lower panel). Hence, as mentioned beforehand, a rapid decay of uncertainty implies a small learning index; or in other words, stronger integration of past compared to recent observations.

In the following analyses, we tested whether an increasingly noisy Bayesian model mimics behaviour that is observed in the non-social compared to social condition. For example, we tested whether an increasingly noisy Bayesian model also exhibits a strongly negative ‘predictor uncertainty’ effect on interval setting (Figure 2e). In such a way, we can test whether differences in noise in the updating process of a Bayesian model might reproduce important qualitative differences in learning-related behaviour seen in the social and nonsocial conditions.

We used these modified Bayesian models to simulate trial-wise interval setting for each participant according to the observations they made when selecting a particular advisor or non-social cue. We simulated interval setting at each trial and examined whether an increase in noise produced model behaviours that resembled participant behaviour patterns observed in the non-social condition as opposed to social condition. At each trial, we used the accuracy estimate (Methods, equation 6) – which represents a subjective belief about a single angular error -- to derive an interval setting for the selected predictor. To do so, we first derived the point-estimate of the belief distribution at each trial (Methods, equation 6) and multiplied it with the size of one interval step on the circle. The step size was derived by dividing the circle size by the maximum number of possible steps. Here is an example of transforming an accuracy estimate into an interval: let’s assume the belief about the angular error at the current trial is 50 (Methods, equation 6). Now, we are trying to transform this number into an interval for the current predictor on a given trial. To obtain the size of one interval step, the circle size (360 degrees) is divided by the maximum number of interval steps (40 steps; note, 20 steps on each side), which results in nine degrees that represents the size of one interval step. Next, the accuracy estimate in radians (0,87) is multiplied by the step size in radians (0,1571) resulting in an interval of 0,137 radians or 7,85 degrees. The final interval size would be 7,85.

Simulating Bayesian choices in that way, we repeated the behavioural analyses (Figure 2b,e,f) to test whether intervals derived from more noisy Bayesian models mimic intervals set by participants in the non-social condition: greater changes in interval setting across trials (Figure 3 – figure supplement 1b), a negative ‘predictor uncertainty' effect on interval setting (Figure 3 – figure supplement 1c), and a higher learning index (Figure 3d).

First, we repeated the most crucial analysis -- the linear regression analysis (Figure 2e) and hypothesized that intervals that were simulated from noisy Bayesian models would also show a greater negative ‘predictor uncertainty’ effect on interval setting. This was indeed the case: irrespective of social or non-social conditions, the addition of noise (increased weighting of the uniform distribution in each belief update) led to an increasingly negative ‘predictor uncertainty’ effect on confidence judgment (new Figure 3d). In Figure 3d, we show the regression weights (y-axis) for the ‘predictor uncertainty’ on confidence judgment with increasing noise (x-axis). This result is highly consistent with the idea that that in the non-social condition the manner in which task estimates are updated is more uncertain and more noisy. By contrast, social estimates appear relatively more stable, also according to this new Bayesian simulation analysis.

This new finding extends the results and suggests a formal computational account of the behavioural differences between social and non-social conditions. Increasing the noise of the belief update mimics behaviour that is observed in the non-social condition: an increasingly negative effect of ‘predictor uncertainty’ on confidence judgment. Noteworthily, there was no difference in the impact that the noise had in the social and non-social conditions. This was expected because the Bayesian simulations are blind to the framing of the conditions. However, it means that the observed effects do not depend on the precise sequence of choices that participants made in these conditions. It therefore suggests that an increase in the Bayesian noise leads to an increasingly negative impact of ‘predictor uncertainty’ on confidence judgments irrespective of the condition. Hence, we can conclude that different degrees of uncertainty within the belief update is a reasonable explanation that can underlie the differences observed between social and non-social conditions.

Next, we used these simulated confidence intervals and repeated the descriptive behavioural analyses to test whether interval settings that were derived from more noisy Bayesian models mimic behavioural patterns observed in non-social compared to social conditions. For example, more noise in the belief update should lead to more flexible integration of new information and hence should potentially lead to a greater change of confidence judgments across predictor encounters (Figure 2b). Further, a greater reliance on recent information should lead to prediction errors more strongly in the next confidence judgment; hence, it should result in a higher learning index in the non-social condition that we hypothesize to be perceived as more uncertain (Figure 2f). We used the simulated confidence interval from Bayesian models on a continuum of noise integration (i.e. different weighting of the uniform distribution into the belief update) and derived again both absolute confidence change and learning indices (Figure 3 – figure supplement 1b-c).

‘Absolute confidence change’ and ‘learning index’ increase with increasing noise weight, thereby mimicking the difference between social and non-social conditions. Further, these analyses demonstrate the tight relationship between descriptive analyses and model-based analyses. They show that a noise in the Bayesian updating process is a conceptual explanation that can account for both the differences in learning and the difference in uncertainty processing that exist between social and non-social conditions. The key insight conveyed by the Bayesian simulations is that a wider, more uncertain belief distribution changes more quickly. Correspondingly, in the non-social condition, participants express more uncertainty in their confidence estimate when they set the interval, and they also change their beliefs more quickly as expressed in a higher learning index. Therefore, noisy Bayesian updating can account for key differences between social and non-social condition.

We thank the reviewer for making this point, as we believe that these additional analyses allow theoretical inferences to be made in a more direct manner; we think that it has significantly contributed towards a deeper understanding of the mechanisms involved in the social and non-social conditions. Further, it provides a novel account of how we make judgments when being presented with social and non-social information.

We made substantial changes to the main text, figures and supplementary material to include these changes:

Main text, page 10-11 new section:

The impact of noise in belief updating in social and non-social conditions

So far, we have shown that, in comparison to non-social predictors, participants changed their interval settings about social advisors less drastically across time, relied on observations made further in the past, and were less impacted by their subjective uncertainty when they did so (Figure 2). Using Bayesian simulation analyses, we investigated whether a common mechanism might underlie these behavioural differences. We tested whether the integration of new evidence differed between social and non-social conditions; for example, recent observations might be weighted more strongly for non-social cues while past observations might be weighted more strongly for social cues. Similar ideas were tested in previous studies, when comparing the learning rate (i.e. the speed of learning) in environments of different volatilities12,13. We tested these ideas using established ways of changing the speed of learning during Bayesian updates14,21. We hypothesized that participants reduce their uncertainty quicker when observing social information. Vice versa, we hypothesized a less steep decline of uncertainty when observing non-social information, indicating that new information can be flexibly integrated during the belief update (Figure 5a).

We manipulated the amount of uncertainty in the Bayesian model by adding a uniform distribution to each belief update (Figure 3b-c) (equation 10,11). Consequently, the distribution’s width increases and is more strongly impacted by recent observations (see example in Figure 3 – figure supplement 1). We used these modified Bayesian models to simulate trial-wise interval setting for each participant according to the observations they made by selecting a particular advisor in the social condition or other predictor in the nonsocial condition. We simulated confidence intervals at each trial. We then used these to examine whether an increase in noise led to simulation behaviour that resembled behavioural patterns observed in non-social conditions that were different to behavioural patterns observed in the social condition.

First, we repeated the linear regression analysis and hypothesized that interval settings that were simulated from noisy Bayesian models would also show a greater negative ‘predictor uncertainty’ effect on interval setting resembling the effect we had observed in the nonsocial condition (Figure 2e). This was indeed the case when using the noisy Bayesian model: irrespective of social or non-social condition, the addition of noise (increasing weight of the uniform distribution to each belief update) led to an increasingly negative ‘predictor uncertainty’ effect on confidence judgment (new Figure 3d). The absence of difference between the social and non-social conditions in the simulations, suggests that an increase in the Bayesian noise is sufficient to induce a negative impact of ‘predictor uncertainty’ on interval setting. Hence, we can conclude that different degrees of noise in the updating process are sufficient to cause differences observed between social and non-social conditions. Next, we used these simulated interval settings and repeated the descriptive behavioural analyses (Figure 2b,f). An increase in noise led to greater changes of confidence across time and a higher learning index (Figure 3 – figure supplement 1b-c). In summary, the Bayesian simulations offer a conceptual explanation that can account for both the differences in learning and the difference in uncertainty processing that exist between social and non-social conditions. The key insight conveyed by the Bayesian simulations is that a wider, more uncertain belief distribution changes more quickly. Correspondingly, in the non-social condition, participants express more uncertainty in their confidence estimate when they set the interval, and they also change their beliefs more quickly. Therefore, noisy Bayesian updating can account for key differences between social and non-social condition.

Methods, page 23 new section:

Extension of Bayesian model with varying amounts of noise

We modified the original Bayesian model (Figure 2d, Figure 2 – figure supplement 2) to test whether the integration of new evidence differed between social and non-social conditions; for example, recent observations might be weighted more strongly for non-social cues while past observations might be weighted more strongly for social cues. [...] To obtain the size of one interval step, the circle size (360 degrees) is divided by the maximum number of interval steps (40 steps; note, 20 steps on each side), which results in nine degrees that represents the size of one interval step. Next, the accuracy estimate in radians (0,87) is multiplied by the step size in radians (0,1571) resulting in an interval of 0,137 radians or 7,85 degrees. The final interval size would be 7,85.

We repeated behavioural analyses (Figure 2b,e,f) to test whether confidence intervals derived from more noisy Bayesian models mimic behavioural patterns observed in the nonsocial condition: greater changes of confidence across trials (Figure 3 – figure supplement 1b), a greater negative ‘predictor uncertainty' on confidence judgment (Figure 3 – figure supplement 1c) and a greater learning index (Figure 3d).

Discussion, page 14: […] It may be because we make just such assumptions that past observations are used to predict performance levels that people are likely to exhibit next 15,16. An alternative explanation might be that participants experience a steeper decline of subjective uncertainty in their beliefs about the accuracy of social advice, resulting in a narrower prior distribution, during the next encounter with the same advisor. We used a series of simulations to investigate how uncertainty about beliefs changed from trial to trial and showed that belief updates about non-social cues were consistent with a noisier update process that diminished the impact of experiences over the longer term. From a Bayesian perspective, greater certainty about the value of advice means that contradictory evidence will need to be stronger to alter one’s beliefs. In the absence of such evidence, a Bayesian agent is more likely to repeat previous judgments. Just as in a confirmation bias 17, such a perspective suggests that once we are more certain about others’ features, for example, their character traits, we are less likely to change our opinions about them.

Reviewer #2 (Public Review):

Humans learn about the world both directly, by interacting with it, and indirectly, by gathering information from others. There has been a longstanding debate about the extent to which social learning relies on specialized mechanisms that are distinct from those that support learning through direct interaction with the environment. In this work, the authors approach this question using an elegant within-subjects design that enables direct comparisons between how participants use information from social and non-social sources. Although the information presented in both conditions had the same underlying structure, participants tracked the performance of the social cue more accurately and changed their estimates less as a function of prediction error. Further, univariate activity in two regions-dmPFC and pTPJ-tracked participants' confidence judgments more closely in the social than in the non-social condition, and multivariate patterns of activation in these regions contained information about the identity of the social cues.

Overall, the experimental approach and model used in this paper are very promising. However, after reading the paper, I found myself wanting additional insight into what these condition differences mean, and how to place this work in the context of prior literature on this debate. In addition, some additional analyses would be useful to support the key claims of the paper.

We thank the reviewer for their very supportive comments. We have addressed their points below and have highlighted changes in our manuscript that we made in response to the reviewer’s comments.

(1) The framing should be reworked to place this work in the context of prior computational work on social learning. Some potentially relevant examples:

• Shafto, Goodman & Frank (2012) provide a computational account of the domainspecific inductive biases that support social learning. In brief, what makes social learning special is that we have an intuitive theory of how other people's unobservable mental states lead to their observable actions, and we use this intuitive theory to actively interpret social information. (There is also a wealth of behavioral evidence in children to support this account; for a review, see Gweon, 2021).

• Heyes (2012) provides a leaner account, arguing that social and non-social learning are supported by a common associative learning mechanism, and what distinguishes social from non-social learning is the input mechanism. Social learning becomes distinctively "social" to the extent that organisms are biased or attuned to social information.

I highlight these papers because they go a step beyond asking whether there is any difference between mechanisms that support social and nonsocial learning-they also provide concrete proposals about what that difference might be, and what might be shared. I would like to see this work move in a similar direction.

References<br /> (In the interest of transparency: I am not an author on these papers.)

Gweon, H. (2021). Inferential social learning: how humans learn from others and help others learn. PsyArXiv. https://doi.org/10.31234/osf.io/8n34t

Heyes, C. (2012). What's social about social learning?. Journal of Comparative Psychology, 126(2), 193.

Shafto, P., Goodman, N. D., & Frank, M. C. (2012). Learning from others: The consequences of psychological reasoning for human learning. Perspectives on Psychological Science, 7(4), 341-351.

Thank you for this suggestion to expand our framing. We have now made substantial changes to the Discussion and Introduction to include additional background literature, the relevant references suggested by the reviewer, addressing the differences between social and non-social learning. We further related our findings to other discussions in the literature that argue that differences between social and non-social learning might occur at the level of algorithms (the computations involved in social and non-social learning) and/or implementation (the neural mechanisms). Here, we describe behaviour with the same algorithm (Bayesian model), but the weighing of uncertainty on decision-making differs between social and non-social contexts. This might be explained by similar ideas put forward by Shafto and colleagues (2012), who suggest that differences between social and non-social learning might be due to the attribution of goal-directed intention to social agents, but not non-social cues. Such an attribution might lead participants to assume that advisor performances will be relatively stable under the assumption that they should have relatively stable goal-directed intentions. We also show differences at the implementational level in social and non-social learning in TPJ and dmPFC.

Below we list the changes we have made to the Introduction and Discussion. Further, we would also like to emphasize the substantial extension of the Bayesian modelling which we think clarifies the theoretical framework used to explain the mechanisms involved in social and non-social learning (see our answer to the next comments below).

Introduction, page 4:

[...]<br /> Therefore, by comparing information sampling from social versus non-social sources, we address a long-standing question in cognitive neuroscience, the degree to which any neural process is specialized for, or particularly linked to, social as opposed to non-social cognition 2–9. Given their similarities, it is expected that both types of learning will depend on common neural mechanisms. However, given the importance and ubiquity of social learning, it may also be that the neural mechanisms that support learning from social advice are at least partially specialized and distinct from those concerned with learning that is guided by nonsocial sources.

However, it is less clear on which level information is processed differently when it has a social or non-social origin. It has recently been argued that differences between social and non-social learning can be investigated on different levels of Marr’s information processing theory: differences could emerge at an input level (in terms of the stimuli that might drive social and non-social learning), at an algorithmic level or at a neural implementation level 7. It might be that, at the algorithmic level, associative learning mechanisms are similar across social and non-social learning 1. Other theories have argued that differences might emerge because goal-directed actions are attributed to social agents which allows for very different inferences to be made about hidden traits or beliefs 10. Such inferences might fundamentally alter learning about social agents compared to non-social cues.

Discussion, page 15:

[…] One potential explanation for the assumption of stable performance for social but not non-social predictors might be that participants attribute intentions and motivations to social agents. Even if the social and non-social evidence are the same, the belief that a social actor might have a goal may affect the inferences made from the same piece of information 10. Social advisors first learnt about the target’s distribution and accordingly gave advice on where to find the target. If the social agents are credited with goal-directed behaviour then it might be assumed that the goals remain relatively constant; this might lead participants to assume stability in the performances of social advisors. However, such goal-directed intentions might not be attributed to non-social cues, thereby making judgments inherently more uncertain and changeable across time. Such an account, focussing on differences in attribution in social settings aligns with a recent suggestion that any attempt to identify similarities or differences between social and non-social processes can occur at any one of a number of the levels in Marr’s information theory 7. Here we found that the same algorithm was able to explain social and non-social learning (a qualitatively similar computational model could explain both). However, the extent to which the algorithm was recruited when learning about social compared to non-social information differed. We observed a greater impact of uncertainty on judgments about social compared to non-social information. We have shown evidence for a degree of specialization when assessing social advisors as opposed to non-social cues. At the neural level we focused on two brain areas, dmPFC and pTPJ, that have not only been shown to carry signals associated with belief inferences about others but, in addition, recent combined fMRI-TMS studies have demonstrated the causal importance of these activity patterns for the inference process […]

(2) The results imply that dmPFC and pTPJ differentiate between learning from social and non-social sources. However, more work needs to be done to rule out simpler, deflationary accounts. In particular, the condition differences observed in dmPFC and pTPJ might reflect low-level differences between the two conditions. For example, the social task could simply have been more engaging to participants, or the social predictors may have been more visually distinct from one another than the fruits.

We understand the reviewer’s concern regarding low-level distinctions between the social and non-social condition that could confound for the differences in neural activation that are observed between conditions in areas pTPJ and dmPFC. From the reviewer’s comments, we understand that there might be two potential confounders: first, low-level differences such that stimuli within one condition might be more distinct to each other compared to the relative distinctiveness between stimuli within the other condition. Therefore, simply the greater visual distinctiveness of stimuli in one condition than another might lead to learning differences between conditions. Second, stimuli in one condition might be more engaging and potentially lead to attentional differences between conditions. We used a combination of univariate analyses and multivariate analyses to address both concerns.

Analysis 1: Univariate analysis to inspect potential unaccounted variance between social and non-social condition

First, we used the existing univariate analysis (exploratory MRI whole-brain analysis, see Methods) to test for neural activation that covaried with attentional differences – or any other unaccounted neural difference -- between conditions. If there were neural differences between conditions that we are currently not accounting for with the parametric regressors that are included in the fMRI-GLM, then these differences should be captured in the constant of the GLM model. For example, if there are attentional differences between conditions, then we could expect to see neural differences between conditions in areas such as inferior parietal lobe (or other related areas that are commonly engaged during attentional processes).

Importantly, inspection of the constant of the GLM model should capture any unaccounted differences, whether they are due to attention or alternative processes that might differ between conditions. When inspecting cluster-corrected differences in the constant of the fMRI-GLM model during the setting of the confidence judgment, there were no clustersignificant activation that was different between social and non-social conditions (Figure 4 – figure supplement 4a; results were familywise-error cluster-corrected at p<0.05 using a cluster-defining threshold of z>2.3). For transparency, we show the sub-threshold activation map across the whole brain (z > 2) for the ‘constant’ contrasted between social and nonsocial condition (i.e. constant, contrast: social – non-social).

For transparency we additionally used an ROI-approach to test differences in activation patterns that correlated with the constant during the confidence phase – this means, we used the same ROI-approach as we did in the paper to avoid any biased test selection. We compared activation patterns between social and non-social conditions in the same ROI as used before; dmPFC (MNI-coordinate [x/y/z: 2,44,36] 16), bilateral pTPJ (70% probability anatomical mask; for reference see manuscript, page 23) and additionally compared activation patterns between conditions in bilateral IPLD (50% probability anatomical mask, 20). We did not find significantly different activation patterns between social and non-social conditions in any of these areas: dmPFC (confidence constant; paired t-test social vs nonsocial: t(23) = 0.06, p=0.96, [-36.7, 38.75]), bilateral TPJ (confidence constant; paired t-test social vs non-social: t(23) = -0.06, p=0.95, [-31, 29]), bilateral IPLD (confidence constant; paired t-test social vs non-social: t(23) = -0.58, p=0.57, [-30.3 17.1]).

There were no meaningful activation patterns that differed between conditions in either areas commonly linked to attention (eg IPL) or in brain areas that were the focus of the study (dmPFC and pTPJ). Activation in dmPFC and pTPJ covaried with parametric effects such as the confidence that was set at the current and previous trial, and did not correlate with low-level differences such as attention. Hence, these results suggest that activation between conditions was captured better by parametric regressors such as the trial-wise interval setting, i.e. confidence, and are unlikely to be confounded by low-level processes that can be captured with univariate neural analyses.

Analysis 2: RSA to test visual distinctiveness between social and non-social conditions

We addressed the reviewer’s other comment further directly by testing whether potential differences between conditions might arise due to a varying degree of visual distinctiveness in one stimulus set compared to the other stimulus set. We used RSA analysis to inspect potential differences in early visual processes that should be impacted by greater stimulus similarity within one condition. In other words, we tested whether the visual distinctiveness of one stimuli set was different to the visual distinctiveness of the other stimuli set. We used RSA analysis to compare the Exemplar Discriminability Index (EDI) between conditions in early visual areas. We compared the dissimilarity of neural activation related to the presentation of an identical stimulus across trials (diagonal in RSA matrix) with the dissimilarity in neural activation between different stimuli across trials (off-diagonal in RSA matrix). If stimuli within one stimulus set are very similar, then the difference between the diagonal and off-diagonal should be very small and less likely to be significant (i.e. similar diagonal and off-diagonal values). In contrast, if stimuli within one set are very distinct from each other, then the difference between the diagonal and off-diagonal should be large and likely to result in a significant EDI (i.e. different diagonal and off-diagonal values) (see Figure 4g for schematic illustration). Hence, if there is a difference in the visual distinctiveness between social and non-social conditions, then this difference should result in different EDI values for both conditions – hence, visual distinctiveness between the stimuli set can be tested by comparing the EDI values between conditions within the early visual processing. We used a Harvard-cortical ROI mask based on bilateral V1. Negative EDI values indicate that the same exemplars are represented more similarly in the neural V1 pattern than different exemplars. This analysis showed that there was no significant difference in EDI between conditions (Figure 4 – figure supplement 4b; EDI paired sample t-test: t(23) = -0.16, p=0.87, 95% CI [-6.7 5.7]).

We have further replicated results in V1 with a whole-brain searchlight analysis, averaging across both social and non-social conditions.

In summary, by using a combination of univariate and multivariate analyses, we could test whether neural activation might be different when participants were presented with a facial or fruit stimuli and whether these differences might confound observed learning differences between conditions. We did not find meaningful neural differences that were not accounted for with the regressors included in the GLM. Further, we did not find differences in the visual distinctiveness between the stimuli sets. Hence, these control analyses suggest that differences between social and non-social conditions might not arise because of differences in low-level processes but are instead more likely to develop when learning about social or non-social information.

Moreover, we also examined behaviourally whether participants differed in the way they approached social and non-social condition. We tested whether there were initial biases prior to learning, i.e. before actually receiving information from either social or non-social information sources. Therefore, we tested whether participants have different prior expecations about the performance of social compared to non-social predictors. We compared the confidence judgments at the first trial of each predictor. We found that participants set confidence intervals very similarly in social and non-social conditions (Figure below). Hence, it did not seem to be the case that differences between conditions arose due to low level differences in stimulus sets or prior differences in expectations about performances of social compared to non-social predictors. However, we can show that differences between conditions are apparent when updating one’s belief about social advisors or non-social cues and as a consequence, in the way that confidence judgments are set across time.

Figure. Confidence interval for the first encounter of each predictor in social and non-social conditions. There was no initial bias in predicting the performance of social or non-social predictors.

Main text page 13:

[… ]<br /> Additional control analyses show that neural differences between social and non-social conditions were not due to the visually different set of stimuli used in the experiment but instead represent fundamental differences in processing social compared to non-social information (Figure 4 – figure supplement 4). These results are shown in ROI-based RSA analysis and in whole-brain searchlight analysis. In summary, in conjunction, the univariate and multivariate analyses demonstrate that dmPFC and pTPJ represent beliefs about social advisors that develop over a longer timescale and encode the identities of the social advisors.

References

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6. Grabenhorst, F., and Schultz, W. (2021). Functions of primate amygdala neurons in economic decisions and social decision simulation. Behavioural Brain Research 409, 113318. 10.1016/j.bbr.2021.113318.
7. Lockwood, P.L., Apps, M.A.J., and Chang, S.W.C. (2020). Is There a ‘Social’ Brain? Implementations and Algorithms. Trends in Cognitive Sciences, S1364661320301686. 10.1016/j.tics.2020.06.011.
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Author Response

Reviewer #2 (Public Review):

Reinforcement learning (RL) theory is important because it provides a broad, mathematically proven framework for linking behavioral states to behavioral actions, and has the potential for linking realistic biological network dynamics to behavior. The most detailed neurophysiological modeling uses biophysical compartmental models with the theoretical framework of HodgkinHuxley and Rall to describe the dynamics of real neurons, but those models are extremely difficult to link to behavioral output. RL provides a theoretical framework that could help bridge across the still-underexplored chasm between behavioral modeling and neurophysiological detail.

On the positive side, this paper uses a network of interacting neurons in region CA3 and CA1 (as used in previous models by McNaughton and Morris, 1987; Hasselmo and Schnell, 1994; Treves and Rolls, 1994; Mehta, Quirk and Wilson. 2000; Hasselmo, Bodelon and Wyble, 2002) to address how a simple representation of biological network dynamics could generate the successor representation used in RL. The successor representation is an interesting theory of hippocampal function, as it contrasts with a previous idea of model-based planning. Previous neuroscience data supports the idea that animals use a model-based representation (a cognitive map made up of place cells or grid cells) to read out potential future paths to plan their behavior in the environment. For example, Johnson and Redish, 2007 showed activity spreading into alternating arms of a T-maze before a decision is made (i.e. a model-based exploration of possible actions, NOT a successor representation), and Pfeiffer and Foster, 2013 showed that replay in 2-dimensions corresponds to future goal directed activity. Models such as Erdem and Hasselmo, 2012 and Fenton and Kubie, 2012 showed how forward planning of possible trajectories could guide performance of behavioral tasks. In contrast, the successor representation proposes that model-based activity is too computationally expensive and proposes that instead of reading out various possible model-based future paths when making a decision, that a simulated agent could instead learn a look-up table indicating the probability of future behavioral states accessible from a given state. In previous work, the successor representations accounted for certain aspects of experimental neuroscience data such as place cells responding to the insertion of barriers as seen by Alvernhe et al. and the backward expansion of place field seen by Mehta et al. The current paper is admirable for addressing the potential role of neural replay in training of successor representations and its relationship to other neural and behavioral data such as the papers by Cheng and Frank 2008 and by Wu et al. 2017.

However, a lot of this same data could still be interpreted as indicating that animals use a model-based representation as described above. There's nothing in this paper that rules out a model-based interpretation of the results discussed above. In fact, the cited paper by Momennejad et al. 2017 shows that humans extensively use model-based mechanisms along with some use of a successor representation in addition to the model-based mechanism. The description in the article under review needs to avoid treating successor representations as if they are already the ground truth.

To do this, throughout the paper, the authors need to repeatedly address the fact that the Successor Representation is just a theory and not proven experimental fact. And they need to repeatedly in all sections point out that the successor representations hypothesis can be contrasted with the theory that model-based neural activity could instead guide behavior and could be the correct account for all of the data that they address (i.e. such as the darkavoidance behavior). They should cite the previous examples of neural data that looks like model-based planning such as Johnson and Redish, 2007 in the T-maze and Pfeiffer and Foster, 2013 in open fields, and cite models such as Hasselmo and Eichenbaum, 2005; Erdem and Hasselmo, 2012 and Fenton and Kubie, 2012 that showed how forward replay or planning of possible trajectories could guide performance of behavioral tasks

We thank the reviewer for the valuable feedback. We have adapted the manuscript throughout to discuss the important point that the SR is not the ground truth (e.g. the final paragraphs in the sections “Bias-variance trade-off” and “Leveraging replays to learn novel trajectories”). We also discussed more extensively the model-based literature and the suggested citations in the manuscript.

The title and text repeatedly refers to a "spiking" model. They show spikes in Figure 2 and extensively discuss the influence of spiking on STDP, but they ought to more explicitly discuss the interaction of their spike generation mechanisms (using a Poisson process) and the authors should compare their model to the model of George, DeCothi, Stachenfeld and Barry which addresses many of the same questions but using theta phase precession to obtain the correct spike timing in STDP.

Yes, that's a great suggestion. We have extended our discussion section. In particular, we added:

In our work, we did not include theta modulation, but phase precession and theta sequences could be yet another type of activity within the TD lambda framework. Interestingly, more groups have recently investigated related ideas. A recent work \citep{George2022} incorporated the theta sweeps into behavioural activity, showing it approximately learns the SR. Moreover, theta sequences allow for fast learning, playing a similar role as replays (or any other fast temporalcode sequences) in our work. By simulating the temporally compressed and precise theta sequences, their model also reconciles the learning over behavioral timescales with STDP. In contrast, our framework reconciles both timescales relying purely on rate-coding during behaviour. Finally, their method allows to learn the SR within continuous space. It would be interesting to investigate whether these methods co-exist in the hippocampus and other brain areas. Furthermore, \citep{Fang2022} et al. recently showed how the SR can be learned using recurrent neural networks with biologically plausible plasticity.

The introduction and start of the Results section are should have more citations to neuroscience data. The introduction currently cites only three experimental citations (O'Keefe and Dostrovsky, 1971; O'Keefe and Nadel, 1978 and Mehta et al. 2000) and then gives repeated citations of previous theory papers as if those papers define the experimental data that is relevant to this study. The article should review actual neuroscience literature, instead of acting as if a few theory papers in the last five years are more important sources of data than decades worth of experimental work. The start of the results section makes a statement about the role of hippocampus and only cites Stachenfeld et al. 2017 as if it were an experimental paper. The introduction, start of results and discussion need to be modified to address actual experimental data instead of just prior modeling papers. They need to add at least a paragraph to the introduction discussing real experimental data. There are numerous original research papers that should be cited for the role of hippocampus in behavior so that the reader doesn't get the impression all of this work started with the paper by Stachenfeld et al. 2017. For example, the introduction should supplement the citations to O'Keefe and Mehta with other experimental papers including those that they cite later in the paper. They should also cite other seminal work of Morris et al. 1982 in Morris water maze and Olton, 1979 in 8-arm radial maze and work by Wood, Dudchenko, Robitsek and Eichenbaum on neural activity during spatial alternation. At the start of the Results, instead of only citing Stachenfeld (which should have reduced emphasis when speaking about experiments), they should again cite O'Keefe and Nadel, 1978 for the very comprehensive review of the literature up to that time, plus the work of Morris and Eichenbaum and Aggleton and other experimental work.

We thank the reviewer for the suggested citations. We have added many citations in order to discuss the experimental literature more thoroughly.

This article is admirable for addressing how to utilize a continuous representation of space and time, which Kenji Doya also addressed in his NeurIPS article in 1995 and Neural Computation 2000 (which should be cited). To emphasize the significance of this continuous representation, they could note that reinforcement learning (RL) theory models still tend to use a discretized grid-like map of the world and discrete representation of time that does not correspond to the probabilistic nature of place cell response properties (Fenton and Muller) and the continuous nature of the response of time cells (Kraus et al. 2013).

We thank the reviewer for this important comment and this is indeed one of the main strengths of the proposed framework. We have now emphasised this point, by adding the following paragraph to the Discussion:

“Importantly, the discount parameter also depends on the time spent in each state. This eliminates the need for time discretization, which does not reflect the continuous nature of the response of time cells (Kraus et al. 2013).”

I think the authors of this article need to be clear about the shortcomings of RL. They should devote some space in the discussion to noting neuroscience data that has not been addressed yet. They could note that most components of their RL framework are still implemented as algorithms rather than neural models. They could note that most RL models usually don't have neurons of any kind in them and that their own model only uses neurons to represent state and successor representations, without representing actions or action selection processes. They could note that the agents in most RL models commonly learn about barriers by needing to bang into the barrier in every location, rather than learning to look at it from a distance. The ultimate goal of research such as this should to link cellular level neurophysiological data to experimental data on behavior. To the extent possible, they should focus on how they link neurophysiological data at the cellular level to spatial behavior and the unit responses of place cells in behaving animals, rather than basing the validity of their work on the assumption that the successor representation is correct.

We thank the reviewer for this suggestion, we have now extended the Discussion to include a paragraph on the “Limitations of the Reinforcement Learning framework” which we reproduce here:

We have already outlined some of the perks of using reinforcement learning for modelling behaviour, including providing clear computational and algorithmic frameworks. However, there are several intrinsic limitations to this framework. For example, it needs to be noted that RL agents that only use spatial data do not provide complete descriptions of behavior, which likely arises from integrating information across multiple sensory inputs. Whereas an animal would be able to smell and see a reward from a certain distance, an agent exploring the environment would only be able to discover it when randomly visiting the exact reward location. Furthermore, the framework rests on fairly strict mathematical assumptions: typically the state space needs to be markovian, time and space need to be discretized (which we manage to evade in this particular framework) and the discounting needs to follow an exponential decay. These assumptions are overly simplistic and it is not clear how often they are actually met. Reinforcement Learning is also a sample-intensive technique, whereas we know that some animals, including humans, are capable of much faster or even one-shot learning. \ Regarding the specific limitations of our model, we can note that even though we have provided a neural implementation of the SR, and of the value function as its read-out (see Figure 5-figure supplement S2, the whole action selection process is still computed only at the algorithmic level. It may be interesting to extend the neural implementation to the policy selection mechanism in the future.

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

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Reply to the reviewers

_Reply to the reviewers _

Note: the three reviewers who provided comments were identified as Reviewers 2-4

Reviewer #2

1) I could not open any of the movies (while those associated with the BioRXiv preprint were fine). Some of the movies could be combined to minimize download/open clicking sequences.

• The movies were uploaded as .avi files, as per Review Commons instructions, and we tested our ability to view them on several computers at our institution before submission. We are relieved the reviewer was able to access the .mp4 formatted movies via BioRXiv. We will ask the Review Commons Managing Editor to make sure there are no problems with the videos uploaded with the revised manuscript.*

2) I really dislike reviewing papers without line numbers

• Line numbers have been added to the revised version.*

3) The manuscript could be made more relevant to malaria researchers by briefly discussing red cell invasion by merozoites (a single constriction and force against the cell cortex), migration of ookinetes (multiple constrictions during mosquito gut penetration) and sporozoites (long distance migration), but this is not a must.

• Constrictions during ookinete migration are now mentioned on lines 265-269, and the discussion of the constriction at the moving junction has been broadened to include other apicomplexan parasites lines 270-278.*

4) I would limit reporting of numbers to two digits, e.g. instead of 46.3% make it 46%; 2.56 +/- 0.38 to 2,6 +/- 0,4 etc

> We have adjusted all numbers in the text and figures to the appropriate number of significant figures based on measurement precision.

5) Millions of deaths, please rewrite, more like around 1 million from malaria and cryptosporidium; use citation (WHO)

> Done (line 40)

6) Motility: please don't mention flagella, which are used for swimming, in the same sentence / phrase / logic connection as lamellipodia, which are used for substrate based migration

> The sentence has been rewritten to make clear that cilia and flagella are not organelles involved in the substrate-dependent motility of other eukaryotic cells (lines 47-49).

7) In Figure 1B, I can see one microsphere and it's not clear if it moves completely back to the original position. In the movie it looks like it goes completely back, maybe exchange the last panel of the figure with a last frame from the movie? Or maybe better: replace with frames from movie 2, which is more striking and shows many beads being displaced?

> As suggested, Figure 1B now shows frames from the other movie (former Video 2), where bead movement is more obvious.

8) Please add the entire figure S1 to Figure 1. This is important for readers to understand and 'deserves' full figure status. Same for Figure S2.

*> We have moved most of former Figure S1 into a new main Figure 2, as suggested. We left the two graphs as Supplemental data (new Figure S1), since these graphs simply show that parasite motility in fibrin is similar to the previously described motility of parasites in Matrigel. *

*> Figure S2 has been moved to the main text, as suggested (in new Figures 3 and 6). *

9) I would encourage the authors to elaborate more on the data on Figure S2. It appears that motile parasites did mostly not exert forces above the level for non-motile parasites; for how much motility did they observe forces? The meaning of the x-axis does not become clear. Are those individual parasites per time point or time points of one parasite or of the analyzed matrix volumes over several parasites? How many parasites where observed? This is stated more clearly later but needs to be done already here.

> We have moved the data in former Suppl. Figure S2 into the main figures, broken it into two parts (Figures 3 and 6B-E) and included a new 3D volume view and additional explanatory detail in the figure legends and text to clarify these points of confusion (lines 100-116, 500-507, 564-570).

10) Please change 0.042 um into 42 nm etc

*> Done, lines 113-116. *

11) Please move some of the data in Figure S8 to the main figures e.g. Figure 4, where it would make a nice contrast / comparison to the mic2 mutant. Please also put a WT for comparison.

> Done; see revised Figure 6.

12) I wonder if the defect in directional migration of the mic2 mutant is also partly due to the parasite not being able to squeeze through narrow matrix pores and hence is deflected more often. While I understand (and agree) with the authors observation (interpretation) of the wt parasites not squeezing but pulling, it's hard to think that such squeezing would not still play a part.

*> The idea that the parasite needs to squeeze its way through pores in the matrix is intuitively appealing (and, in fact, what we had expected to see) but there is currently no data to support it. If squeezing were occurring, we should see an outward deformation of the matrix as the parasite pushes on the matrix fibers, but this is something we have never observed. We therefore think it is unlikely that the loss of directional migration is due to an inability to squeeze through pores in order to “stay on track”. *

13) Hueschen et al is now on BioRXiv

> The BioRXiv citation has been added (lines 293, 320).

14) The shaving off of antibodies could be brought into context to the work on sporozoites by Aliprandini Nat Micro 2018 and on trypanosomes by Enstler Cell 2007 (but not a must)

*> The two studies mentioned are intriguing and may be related to the well-documented anterior to posterior flux and shedding of GPI-anchored proteins from the surface of gliding Toxoplasma tachyzoites. What we are showing here is slightly different: the fluorescent antibodies on the cell surface seem to be “shaved” backwards at the constriction, much like surface bound antibodies are shaved backwards at the moving junction during invasion (Dubremetz 1985). In other words, there is a discontinuity in the density of surface staining at the constriction/junction. All of these processes may be related, but this is only speculation at this point and since the shaving of antibody at the constriction is a minor point of the paper (meant only to illustrate another similarity between 3D motility and invasion), we would prefer not to try to tie it to these other observations which may or may not be related. *

15) Anterior-posterior flux: best experimental evidence for this is Quadt et al. ACS Nano 2016 for Plasmodium and Stadler MBoC 2017 for Toxoplasma. The common observations and differences could be discussed as they pertain to the current study

> These two papers are now cited in our discussion of the linear motor model along with our speculation that the constriction reflects the motility-relevant zone of engagement of this rearward flux with ligands in the matrix (lines 319-322).

16) The loss of mic2 could lead to the loss of the capability to form discrete adhesion sites that reveal themselves as the observed rings in 3D. I suggest to be careful to hypothesize that the absence of this and MyoA reveals a completely different motility mechanism. To me it seems more likely that the absence of the proteins means that the existing mechanism doesn't work perfectly any more, ie the highly tuned migration machinery misses a key part and malfunctions.

*> The paragraph in question offered possible explanations for how parasites lacking the constriction could in fact move at normal speeds, not that motility was negatively affected. We have tried to make this more clear in the revision (lines 352-354), before describing the 3 possible explanations. *

17) Maybe reflect on whether 'search strategy' might be a better word than 'guidance system'

*> We have replaced the term “guidance system” in the title (lines 1-2), abstract (lines 33-36) and introduction (line 75) with more conservative references to the ability of the parasite to move directionally. The only place the term “guidance system” remains is in the final paragraph of the discussion, which is more speculative in nature, and where we now suggest it to be “part of” a guidance system. *

Reviewer #3

1) Extracellular matrix choice. The authors track the parasite movement first on Matrigel and next on fibrin. The authors exemplify the fibrin matrix on an image on Suppl. Fig 1 that shows a relatively quite large pore size, similar or greater than parasite size. Was the analysis done on parasites touching the fibers?

*> Previous Suppl Figure 1A showed a confocal image at only one z-plane which did indeed give the impression that the pores are relatively large. We have changed this image to a more informative maximum intensity projection (New Figure 2A) and included a video showing the entire imaging volume (new Video 4), which makes clear that the matrix contains many small fibers and that the pores are smaller than the previous single z-plane suggested, so the parasite is likely to be near to or in contact with fibers of the matrix at all times. In Suppl Figure 1D we purposely used a less dense matrix in order to make the matrix deformation more obvious to the eye. The density of the matrix in Fig. 1D has been added to the legend. *

2) Lack of movement of parasites. In many figures of the articles it is revealed that the majority of parasites in fibrin remain immobile (Suppl Fig 1, Fig 2, Video 5, Suppl Fig 2, Suppl Fig 8). The number of immobile parasites in Matrigel seem to be lower than in fibrin (Suppl Fig 1B) although no quantification is shown. How does the movement in fibrin and Matrigel compare? How does this compares with movement in stiff substrates in 2D? Could the lack of movement be caused by the large pore site in fibrin?.

> We have added a panel to Suppl. Figure S1 showing that the proportions of parasites moving in fibrin vs Matrigel are not significantly different. In fact, none of our measured motility parameters are different between fibrin and Matrigel. Not all parasites move during the 80s of capture used for these matrix comparisons; some of the parasites are likely dead, but others may have simply not initiated motility during this time window. We typically see between 30-50% movement in 3D motility assays of this duration and similar numbers in 2D trail assays although we have not explored the effect of 2D substrate stiffness.

3) Considering parasite movement: The authors consider that 3SD is a cutoff for considering parasite displacement. However, several timepoints fall behind this cutoff in the control without parasites and the knockouts with restricted movement.

> We chose three standard deviations from the mean as our cutoff, in order to eliminate 99.7% of the noise. Since we calculate 16807 vectors per comparison, this leaves us with ~50 vectors above the cutoff even in samples with no moving parasites. Not surprisingly, these vectors are found at random locations in the volume. New Figures 3 and 6B-E and the associated text (lines 100-116, 500-507, 564-570) hopefully clarify this point adequately; it is quite obvious in Figure 3C which vectors correspond to parasite-induced displacements and which correspond to random noise.

4) Imaging: Although the authors show a very detailed an illustrative table of the imaging acquisition conditions in table 1, it is unclear which microscope the authors used, as two microscopes are described in the methods section, a Nikon Eclipse TE300 widefield microscope and a Nikon AIR-ER confocal microscope. Which images were taken in each system? For the location of Table1 in the manuscript it seems that most images were taken with the Nikon Eclipse. Although this microscope has control over z, the images are quite noisy. How does the lack of confocallity might interfere with the analysis?

> The high temporal resolution needed for 3D force mapping of cells that move several microns per second meant that all these experiments were done using a widefield microscope equipped with a piezo-driven z-stage. The fastest confocal we tested was not as fast as the widefield. However, spatial resolution suffered as a result of having to use widefield, particularly in z,* and this did indeed make our data more noisy as suggested by the reviewer. This may be why we were unable to detect fibrin deformation in the knockout parasites. The only data collected on the confocal microscope were those shown in new Figure 2A; we have clarified this on lines 421-427. Future studies will explore other imaging modalities such as light sheet microscopy in an attempt to achieve better spatial resolution while maintaining the high frame rates required for force mapping. *

5) Nuclear constriction. The authors did not show any image or video exemplifying this.

The images in Suppl. Figure 6 have been replaced with data that show the nuclear shape more clearly.

6) Knockouts: The authors did not explain how did they generated the knockouts in the methods or did now show the efficacy of the knockout in any figure. If these knockout strains were a gift (I did not find it on the manuscript), the authors should indicate this more explicitly and reference the manuscript where they were described for the first time.

> Both of the stable knockout lines used were generous gifts from Dr. Markus Meissner. We cited the original papers describing these lines in the text and thanked Dr. Meissner for providing them in the Acknowledgements section. We have now included an additional citation at the first mention of each of the knockouts (lines 174, 188) to make it even clearer where they came from.

7) Discussion: Although the experimental methodology is sound the authors seem to make many assumptions and speculations on the discussion as how the appearance of this ring/constriction on the parasite translates into the helical movement of the parasite or the coupling of the ring with the cytoskeleton. Live imaging of actin dynamics or mathematical modelling could be used to support their claims.

> We imaged parasites expressing the actin chromobody but were unable to visualize a ring of actin at the constriction. However, due to the speed of the parasites and the need for a fast frame rate (~15 ms per image) to reconstruct the 3D image volumes, the actin chromobody signal could be under our threshold of detection. We need to develop new, more sensitive ways to visualize proteins at the constriction, and this will be a major focus of our work going forward.

*> We fully concur that mathematical modeling such as the work recently done by Hueschen et al on actin flow during motility and by Pavlou et al on the role of parasite twist during invasion has much to offer our understanding of these processes. Similar approaches may provide support to the speculations (not claims!) we offer in the discussion and, although beyond the scope of the current study, are a direction we intend to take this work in the future – particularly if we are able to improve the signal-to-noise in our force mapping. *

8) Quantification of experiments missing: Overall, the main figures lack quantification that sometimes can be found in the supplemental information and sometimes is missing. I would suggest including quantifications next to the events described in the main figures). Likewise, some of the supplemental figures lack quantification (Suppl Fig 7, how many parasites showed this protein trail?)… Overall, the authors should indicate how many parasites were quantified in each figure. As they usually refer to number of constrictions. This is overall a problem in main figures 3 and 5. Or for example in Suppl Fig 5: How many parasites were quantified in this figure? The authors only show number of constrictions, and as the authors described, a parasite might have more than one constriction.

> We have added further detail on the number of events/parasites quantified to both the figure legends and text throughout the manuscript, including the specific examples noted by the reviewer.

9) Videos: The videos lack scale of time. Although this that can be found in main figures, it would be helpful to have the annotation in the videos. Likewise, some references for positions in videos, such as the cross found on Fig1 would be helpful for parasites that present little movement.

> Time stamps have been added to all videos as suggested, and crosshairs have been applied to new Figure 1B and Suppl. Figures 7 and 8 to make the movement of the parasites more obvious. *

*

Reviewer #4

1) I am not sure about the premise that the "linear model" of gliding motility predicts uniformly forward direction. Previous videos of 2D gliding show sporadic motility, changes in direction, or even reversal of direction are not infrequent. However, the current model could explain these behaviors if one or more of the following conditions occur: 1) myosin motors might be coordinating activated to initiate motility, followed by relaxation, 2) actin fibers might be transiently arrayed in clusters that change density and polarity over time, or 3) adhesins, necessary to generate traction, might vary in density and spatial orientation across the surface of the parasite. Changes in these properties would be expected result in zones that promote or disfavor local forces needed for motility - and reversal of direction could occur when forward forces relax and external elastic forces predominate.

> The potential explanations offered by the reviewer for the frequent changes in direction of zoite motility are intriguing and worth exploring experimentally. The ability of actin fibers to periodically reverse polarity, or the presence of counteracting elastic forces are not components of the “standard” linear motor model of motility but, if they occur, could explain the patch gliding phenomenon and help refine our understanding of motility. Since the data in this manuscript do not in the end either strongly support or disprove the linear motor model – this may ultimately require higher resolution force mapping methods that can detect the forces responsible for forward motion – we have de-emphasized potential problems with the model in the introduction and deleted specific discussion of patch gliding as one of these problems (lines 61-64).

2) The model favored here: "we propose that force is generated, at least in part, by the rearward translocation of the subset of actin filaments that are coupled to adhesins at the circular ring of attachment" does not seem fundamentally different from the current model - other than it focuses the forces at a critical junction that the parasite migrates through. It seems to me that this is a refinement of the current model and not a replacement. As such, the authors might focus on how their data improve the model rather than pointing out prior deficiencies (although I get that editors like this style).

> We agree with the reviewer and have modified the text to be more circumspect on this issue* (lines 319-331). *

3) The finding that the absence of MIC2 affects the constriction formed by inward pull on the matrix is quite convincing and interesting. However, mutants that cannot form the constriction, still move at similar speeds. This suggest that the inward force is different from the motor itself and affects its ability to impart direction, rather than the ability to move per see. The interpretation of the MyoA defect is complicated since motility is certain to be disrupted, the potential role of an independent inward force may no longer be detectable.

> We agree with the reviewer on this point as well: the forces we have observed to date cannot explain forward motion. We stated this previously and have now emphasized the point further *(lines 322-324, 352-357). Because the parasite is moving forward, the forces responsible must be there but are likely below our threshold of detection. In order to visualize these forces, we are going to need new imaging modalities that can achieve better signal-to-noise than our current setup at the high frame rates required for force mapping. That said, we new data we have added to the manuscript are at least consistent with the narrow diameter ring of the constriction making a contribution to the parasite’s forward motion (new Suppl. Figure 10 and lines 347-351) *

4) Although I agree with the authors that there are striking parallels between motility in 3D and cell invasion, I am not certain about their conclusion that the construction seen during cell entry is due to the parasite pulling inwardly. When entering the host cell, the parasite must also navigate the dense subcortical actin network, which likely also aids in forming the constriction that is observed. It would be interesting to record this pattern under conditions where host cell actin is destabilized while parasite motility is intact- for example using cytochalasin D to treat wild type host cells during invasion by resistant parasites.

*> We do not conclude that the constriction during invasion is due to the parasites pulling inwardly, but we do propose that this possibility needs to be considered based on the noted similarities between invasion and motility and our clear (and somewhat surprising) demonstration that the moving parasite pulls on the matrix at the constriction during motility. During invasion, the parasite may indeed have to squeeze through the dense subcortical network – or it may use secreted proteins to loosen up the network so that no squeezing is required. We just don’t know, and our purpose here was simply to put this alternative possibility on the table because we believe it is a viable possibility that follows from the data presented. *

> We thank the reviewer for the suggestion of testing what happens when cytoD resistant parasites invade in the presence of cytoD; this is a clever idea that we will likely pursue in future work.

5) Not all of the color patterns shown in Figure 1A are consistent with the model. For example, GAP40 (yellow) does not appear in the model, there are two MLC boxes, but they are different shades, and ELC1/2 does not appear in the model.

> We thank the reviewer for catching this error; it has now been fixed.

Discussion, revision and decision

Decision

Verified with reservations: The content is scientifically sound, but has shortcomings that could be improved by further studies and/or minor revisions.

Dr. Bañuelos: Verified manuscript

Dr. Morris: Verified with reservations

Revision

Response to Reviewer 1 (Dr. Bañuelos)

1. Most importantly, I would like to see an introduction that explains the authors’ general arguments about grading changes – including the trajectory of these changes at Dalhousie and why this arc contributes to our knowledge of the history of higher education more broadly. Then, the authors might continually remind us of the arc they present at the outset of their paper – especially when they are highlighting a piece of evidence that illustrates their central argument. To me, the quotes from students and faculty responding to grading changes are among the most interesting parts of the paper and placing these in additional context should make them shine even more brightly!

Our Response: Thank you so much for your thoughtful review. We have added a larger new introduction section of the paper (paragraphs 1-5 in the latest draft are new) that outlines the general importance of the topic, the Canadian context, details on Dalhousie University, and our overall thesis statement (i.e., most decisions were to improve the external communication value of grades). Moreover, we have added three new student quotes form the Dalhousie Gazette to build a stronger picture for student reactions, and to build a better case for our overall thesis statement (i.e., that changes in grading were often to increase the external communication value of grades). Moreover, throughout we have added some details on the overall funding trajectory for institutions in Canada that created some pressure to standardize grading. We think that these changes have improved the manuscript.

1. I’d like to read a little more about Dalhousie itself – why it is either a remarkable or unremarkable place to study changes in grading policies. Is it representative of most Canadian universities and thus, a good example of how grading changes work in this national context? Is it unlike any other institution of higher education and thus, tells us something important about grades that we could not learn from other case studies? I don’t think this kind of description needs to be particularly long, but it should be a little more involved than the brief sentences the authors currently include (p.3, paragraph 1) and should explain the choice of this case.

Our Response: This comment revealed that two additional pieces of context were needed for the introduction: (a) some national context for higher education policy in Canada and (b) some extended description of Dalhousie University when compared to other universities in Canada. To this end, two new paragraphs have been added to the paper (paragraphs 2 & 3 in the current draft).

Notably, Jones (2014) notes that “Canada may have the most decentralized approach to higher education than any other developed country on the planet” (pg 20). With this in mind, any historical review of education policy is by necessity specific to province and institution – that is, the information can be placed in its context, but resists wide generalization to the country as a whole. In the newest draft, we tried to describe the national, provincial, and institutional context in some more detail in paragraphs 2 & 3.

1. I’d also like to know more about the archival materials the authors used. The authors mention that they drew from “Senate minutes, university calendars, and student newspapers” (p. 3), but what kinds of conversations about grades did these materials include? At various points, the authors engage in “speculation” (e.g. p.4) about why a particular change occurred. This is just fine and, in fact, it’s good of the authors to remind us that they are not really sure why some of these shifts happened. But, they might go one step further and tell us why they have to speculate. Were explicit discussions of grading changes – including in inter- and intradepartmental letters and memo, reports, and other documents – not available in these archives? Why are these important discussions absent from the historical record?

Our Response: We have added a new paragraph (paragraph 4) to the paper discussing the sources in some more detail. It is true that the verbatim discussions are frequently absent from the record, especially earlier in history – or if they exist, we have not found them! Instead, we frequently are reviewing meeting minutes or committee reports, which are summaries of discussions. As we now note in the paper, “Thus, the sources used showed what policy changes were implemented, when they were implemented, and a general sense of whether there was opposition to changes; however, there were notable gaps in faculty and student reactions to grade policy changes, as these reactions were frequently not written down and archived.”

This gap was most apparent in the Senate minutes around the 1940s, where I (the first author) could not find any direct discussions of why changes were implemented. Under the 1937-1947 heading, we more clearly indicate that the rationale for the changes was absent from the Senate minutes during this period. I add some further speculation on why these records might be absent, based on summaries from Waite (1998b); specifically, the university president of the time often made unilateral decisions, circumventing Senate, which might account for why the changes are absent from the records.

This will hopefully make the limitations of what can be learned from this approach more apparent.

1. At various points, the authors make references to the outside world – for example, WWII (p. 5), the Veteran’s Rehabilitation Act (pp. 6-7), and British versus American grading schemas (p. 6). But, these references are brief and seem almost off-handed. I know space is limited, but putting these grading changes in their broader context might help make the case for why this study is interesting and important. Are the changes in the 1940s, for example, related to the ascendance of one national graduate education model over another (e.g. American versus British)? Are there any data on how many Canadian undergraduates enrolled in British versus American graduate programs over time? If so, I would share any information you might have on these broader trends.

Our Response: To our knowledge, there isn’t any comparable report to what we’ve written here documenting the transition from British “divisions” to American “letter grades” in Canadian Universities, making our report novel in this regard. It might well be that a similar historical arc exists in many of the 223 public and private universities in Canada, but we don’t believe such data exists in any readily accessible way – excepting perhaps undergoing a similar deep dive into historical documents at each respective institution! So, we do not have the answer to your question: “Are there any data on how many Canadian undergraduates enrolled in British versus American graduate programs over time?” However, we did add one reference which provided a snapshot point of comparison in 1960, noting in the paper “Baldwin (1960) notes that the criteria for “High First Class” grades in the humanities was around 75-80% at Universities of Toronto, Alberta, and British Columbia in 1960, suggesting that Dalhousie’s system was similar to other research-intensive universities around this time.” That said, there are a few major national events related to the funding of universities in Canada that we have elaborated on in the text to address the spirit of your recommendation for describing the national context:

a) In the “Late 1940s” section of the paper, we added: “Though Dalhousie had an unusually high proportion of veterans enrolled relative to other maritime universities during this period (Turner, 2011), the Veteran’s Rehabilitation Act was a turning point for large increases in enrollment and government funding Canada-wide, at least until the economic recession of the 1970s (Jones, 2014).”

b) In the 1990s, there were major government cuts to funding, creating challenging financial times for the university. We discuss the funding pressures that likely contributed to standardization of grading during this time by saying the following in the 1980s-2000s section: “Starting in in the 1980s-1990s there were major government cuts to university funding nation-wide, with the cuts becoming more severe in the 1990s (Jones, 2014; Higher Education Strategy Associates, 2021). Because of the nature of the funding formulas, cuts in Nova Scotia were especially deep. Beyond tuition increases, university administrators knew that obtaining external research grants, Canada Research Chairs, and scholarship funding was one of the few other ways for a university to balance budgets, so there was extra pressure to be competitive in these pools. […] The increased standardization was likely related to increased financial pressures at this time – standardization is an oft-employed tool to deal with ever-increasing class sizes with no additional resources.”

c) In the 2010s section of the paper, we added context to how universities in country-wide have become increasingly dependent on tuition fees for funding: “Following the 2008 recession, federal funding decreased again (Jones, 2014; Higher Education Strategy Associates, 2021); however, this time universities tended to balance budgets by increasing tuition and international student fees. This trend towards increased reliance on tuition for income is especially pronounced in Nova Scotia, which has the highest tuition rates in the country (Higher Education Strategy Associates, 2021). Thus, the university moved closer to a “consumer” model of education, so it makes sense that a driving force for standardization was student complaints.”

1. This is a very nitpicky concern that doesn’t fit well elsewhere, so please take it with a grain of salt. I was surprised at the length of the reference list – it seemed quite short for a historical piece! I wonder, again, if more description of the archival material - including why you looked at these sources, in particular, and what was missing from the record – would help explain this and further convince the reader that you have all your bases covered.

Our Response: In the introduction section, paragraph 4, we describe our sources in more detail including what is likely missing from the record and why we used them. Regarding the length of the reference list, we did add ~12 new references to the list in the course of making various revisions, which partially addresses your concern. Beyond this though, it’s worth noting that some of the sources more extensive than they seem, even though they don’t take up much space in the reference list (e.g., there is one entry for course calendars, but this covers ~100 documents reviewed!). Moreover, there were many dead-ends in the archives that are not cited (e.g., reviewing 10 years of Senate minutes in the 1940s produced little of relevance), so the reference list is curated to only those sources where relevant materials were found.

Reviewer response to revisions

The new introduction to the piece addresses many of my previous questions about the authors’ general arguments, the Dalhousie context, and the source material. Thank you for addressing these! Reading this version, it is much clearer that the key argument is that standardized, centralized grading practices were “to improve the external communication value of the grades, rather than for pedagogical reasons” (p. 6). I also really enjoyed the added quotes from students in the Dalhousie Gazette.

The authors’ response to Reviewer 2 really gave me a better sense of why they wrote this piece and also helped me to more clearly put my finger on what was troubling me in the first round. It still reads a little like a report for an internal audience – which is just fine and, in fact, can be extremely useful for historians of the future. But, as Reviewer 2 notes, this means it does not really seem like a piece of historical scholarship. I do worry that shaping it into this form would take an extensive revision and might not be in the spirit of what the authors intended to do.

A different version of this article might start with this idea that grades were standardized for external audiences and in response to financial pressures. It would then develop a richer story behind the sudden importance of these external audiences and the nature (i.e. source, type) of financial pressures Dalhousie was facing. It would highlight the impact such changes had on students and their future careers/graduate experiences. It could then connect these trends to other similar changes for external audiences and the increasing interconnectedness of American, Canadian, and British systems through graduate education. It might even turn to sociological theories of organizational change and adaptation and make an argument for when (historically) similar forms of decoupling were likely to occur in the Canadian higher education system. Finally, it might connect these grading changes to current trends – including accusations of grade inflation and accepted best practices for measuring learning outcomes.

But, it doesn’t seem that the authors necessarily want to do this, which I can understand and respect. I think there is enormous value in a piece of scholarship like this existing – both for internal audiences and for future historians. Indeed, imagine if every university had a detailed history of its grading policies like this available somewhere online! Comparing such practices across institutions would certainly tell us a lot about why grading currently looks the way it does.

Decision changed

Verified manuscript: The content is scientifically sound, only minor amendments (if any) are suggested.

Response to Reviewer 2 (Dr. Morris)

The authors dove headfirst into Dalhousie’s archives, unpacking the subtle shifts in grading policy. Their work seems to be comparable to archaeologists, digging deep beneath mountains of primary sources to find nuggets of clues into Dalhousie’s grading evolution. I particularly liked when the authors were able to link these changes to student voices, as seen in moments when they referenced student publications.

Ultimately, I kept coming back to one main comment that I wrote in the margins: “So what?” I would humbly suggest that the authors reflect on why this history matters to them. Granted, they do this in the conclusion, where they touch on Schneider & Hutt’s argument that grades evolved to increasingly be a form of external communication with audiences beyond school communities. Sure. But I want more. I wanted to see a new insight that this microhistory of Dalhousie significant to the history of Canada or the history of education more generally.

If the authors are so inclined, there might be several approaches to transform this manuscript. I would suggest the following. First, instead of tracing the entire history of grading at the institution, choose one moment of change that you think is the most important. Perhaps in the 1920s and the lack of transparency in grading, or the post-war shift toward American grading. Second, show me – don’t tell me – what Dalhousie was like at this moment. Paint a picture of the institution with details about student demographics, curriculum, educational goals, the broader town, etc. Make the community come alive. Show me what makes Dalhousie unique from other institutions of higher ed. Once you establish that picture, perhaps you could link the change in grading practices to subtle changes at the university community, thereby establishing a before and after snapshot. This will require considerable amounts of work, and the skills of a historian. You will have to find primary and secondary sources that go far beyond what you’ve relied on thus far.

In the end, I found myself wanting the authors to humanize this manuscript, meaning I wanted them to show me that changes in grading practices have tangible effects on real-life human beings. A humanization of their research would mean going narrower and deeper; or, in other words, eliminating much of what they have documented.

However, if that is too tall of an order, I would ask that the authors clarify for themselves who this manuscript is for. Is this a chronicling of facts for an internal audience at Dalhousie’s faculty, alumni, and students? Fine. But my guess is that even members of the Dalhousie community want to read something relatable.

I am suggesting revisions, although not because of objective errors. History is more of an art, in my opinion. With that in mind, I would suggest that the authors paint a more vivid picture (metaphorically) of Dalhousie, showing me how changes one moment of change in grading practices impacted the lives of human beings.

Our Response: Thank you very much for taking the time to read our paper and provide your thoughts and recommendations. It may be helpful to begin by describing why I (the first author) decided to write this paper. Ultimately, I wrote this paper to satisfy my own personal curiosity and to connect with other people at my own place of employment by exploring our shared history. At present day, Dalhousie has a letter grading scheme with a standardized percentage conversion scheme that all instructors used. I wanted to know why this particular scheme was used, but I quickly realized that nobody at Dalhousie really knew how we ended up grading this way! There was an institutional memory gap, and a puzzle that was irresistible to me. So, I wrote this paper for the most basic of all academic reasons: Pure curiosity. I do very much recognize that the subject matter is very niche, perhaps too niche for a traditional journal outlet. Thus, my publishing plan is to self-publish a manuscript to the Education Resources Information Center (ERIC) database and a preprint server as a way of sharing my work with others who might be interested in what I found. Nonetheless, I believe in the importance and value of peer review, especially since I am writing in a field different than most of my scholarly work. That is why I chose PeerRef as a place to submit, so that I could undergo rigorous peer review to improve the work while still maintaining the niche subject matter and focus that drives my passion and curiosity for the project. Of course, if you feel the whole endeavor is so flawed that it precludes publication anywhere, then we can consider this a “rejection” and I will not make any further edits through PeerRef.<br /> The core of your critique suggested that I should write a fundamentally different paper on different subject matter. While I don’t necessarily disagree that the kind of paper you describe might have broader appeal, it would no longer answer the core research question I wanted an answer to: How has Dalhousie’s grading changed over time? So, I must decline to rewrite the paper to focus on a single timeframe as recommended. All this said, I did try my best to address the spirit of your various concerns to improve the quality of the manuscript. Below, I will outline the various major changes to the manuscript that we made to improve the manuscript along the lines you described, while maintaining our original vision for the structure and focus of the paper. The specific changes are outline below:

a) Two new paragraphs (now paragraphs 1-2 of the revised manuscript) were added to explain the “so what” part of the question. Specifically, we describe why we think the subject matter might be of interest to others and summarize the general dearth of historical information on grading practices in Canada as a whole.

b) Consistent with recommendations from the other reviewer, we now state a core argument (i.e., that most major grading changes were implemented to improve the external communication value of the grades) earlier in the introduction in paragraph 5 and describe how various pieces of evidence throughout the manuscript tie back to that core theme.

c) In an attempt to “humanize” the manuscript more, we added more student quotes from the Dalhousie Gazette throughout the paper so that readers can get a better sense of how students thought about grading practices at various times throughout history. Specifically, three new quotes were added in the following sections: 1901-1936, late 1940s, 1950s-1970s. We also added this short note about the physical location where grades used to be posted: “Naturally, this physical location was dreaded by students, and was colloquially referred to as “The Morgue” (Anonymous Dalhousie Gazette Author, 1937).”

d) Early in the paper, we describe why we chose Dalhousie and the potential audience of interest: “As employees of Dalhousie, we naturally chose this institution as a case study due to accessibility of records and because it has local, community-level interest. The audience was intended to be members of the Dalhousie community; however, it may also be a useful point of comparison for other institutions, should similar histories be written.”

e) We have described some of the limitations of our sources in paragraph 4, which may explain why the manuscript takes the form it does – it has conformed to the information that is available!

f) We have linked events at Dalhousie to the national context in some more detail, by detailing some national events related to the funding of universities in Canada. See our response to Reviewer 1, #4 above for more details on the specific changes.

g) Consistent with your stylistic recommendations, we have changed various spots throughout the paper from the present tense (e.g., “is”) to the past tense (e.g., “was”), and were careful in our new additions to maintain the past tense, when appropriate. If there are any spots that we missed, let us know the page number / section, and we will make further changes, as necessary.

h) We retained the first person in our writing – this may be discipline-specific, but in Psychology (the first author’s home discipline), first person is acceptable in academic writing. If you feel strongly about this, we can go through the manuscript and remove all instances of the first person, but we would prefer to keep it, if at all possible.

Hopefully this helps address the spirit of your concerns, and I look forward to hearing your thoughts in the second round of reviews.

Decision changed

Verified with reservations: The content is scientifically sound, but has shortcomings that could be improved by further studies and/or minor revisions.

Joint Public Review:

In this work Malis et al introduce a novel spin-labeling MRI sequence to measure cerebrospinal fluid (CSF) outflow. The glymphatic system is of growing interest in a range of diseases, but few studies have been conducted in humans due to the requirement for and invasiveness of contrast injections. By labeling one hemisphere of the brain the authors attempt to assess outflow through the superior sagittal sinus (SSS), one of the major drainage pathways for CSF, signal changes across time were assessed to extract commonly used metrics. Additionally, correlations with age are explored in their cohort of healthy volunteers. The authors report the movement of labeled CSF from the subarachnoid space to the dura mater, parasagittal dura, and ultimately SSS, evidence of leakage from the subarachnoid space to the SSS, and decreases in CSF outflow metrics with older age.

1. I don't think that the description of Parasagittal dura in figure 1 is correct. There is no anatomical structure at the top of SSS that is known as PSD. The location of the lymphatic structures is also incorrect. Please review "Anatomic details of intradural channels in the parasagittal dura: a possible pathway for flow of cerebrospinal fluid" Neurosurgery 1996 Fox at al. There is usually no obvious tissue between the upper wall of the SSS and the calvarium, which can also be seen in the authors' fig 2A and 2B. All of the tissues located lateral to the SSS are known as PSD. Also, the SSS wall is not as thick as the authors stated and is known as PSD in this region. For this reason, the authors need to revise Fig 1 and it should be changed to PSD in the areas referred to as the SSS wall in the article.

2. The authors described tagged CSF in two pathways: from dura mater to PSD and SAS into the SSS and directly from SAS to SSS. Flow from dura mater to PSD and SAS in the main and supplement cannot be seen. Only a flow from PSD to SSS can be seen. Also, regular dura cannot carry flow-collagen-rich fibrous tissue, except parasagittal dura. There is no flow from dura to the CSF in the figures.

3. The authors have conducted many tests to prevent venous contamination. However, measurements were made based on SSS flow rates in all tests. Small parenchymal venous structures, and small cortical-SAS veins might be tagged due to different flow patterns and T2- Relaxation times.

4. The rate of CSF formation in humans is 0.3 - 0.4 ml min-1. ( Brinker et al 2014. Fluids Barriers CNS). We can assume that the absorption rate is also similar to the CSF formation for the entire system brain and Spine. Therefore, the absorption rate of this very small amount of CSF by SSS is very low in seconds. It is hard to detect by MR and especially CSF flow from the PSD to SSS. The authors concluded that using this technique the rate averaged less than a couple of seconds, rather than on the order of hours or days as previously reported with the use of intrathecal administration of GBCA (Ringstad et al., 2020).

5. Overall, I think that the CSF flow from the PSD to the CNS described by the authors - the CSF flow, might be the venous flow that drains into the SSS slowly, predominantly in the rich venous channels, venous lacunae, and previously described channels in the PSD. Additional explanations are needed.

6. The study is generally well described and to the best of my knowledge an innovative approach. The findings are broadly consistent with what might be expected from the literature and the authors make a good argument in support of their findings. However, the lack of validation is a major limitation of the presented work. In introducing a novel technique a comparison with an existing approach, such as Gd enhanced contrast techniques, or phase contrast would have been expected. Several considerations could have been mentioned/addressed in more detail e.g. what effect labeling efficiency, tortuosity of vessels, lack of gating, the effectiveness of the intensity thresholding to remove the signal from blood, etc may have on the quantification, etc. Without a more thorough validation, it is difficult to evaluate the findings. While scans were conducted on two volunteers to assess reproducibility this is a very small sample and it is notable that scans were conducted consecutively, which might be expected to reduce variance relative to scans further apart e.g. on different dates, scanned by a different operator and no information is provided on how the two scans were positioned (i.e. separately vs copied from the first to the second scan), some metrics showed large percentage differences, which were more pronounced in one subject than the other. Without further data, it is difficult to interpret the reproducibility results. No assessment of the effect of physiological parameters e.g. breathing, cardiac pulsations, or factors affecting glymphatic clearance e.g. amount of sleep the evening before was given.

7. Given these limitations it is hard to adequately assess the likely impact or utility. In recent years several groups have published work e.g. doi.org/10.1038/s41467-020-16002-4 , doi.org/10.1016/j.neuroimage.2021.118755 assessing the blood-CSF barrier. However, previous work has generally focused on larger structures, and by labeling in the oblique-sagittal plane it is unclear how drainage and blood flow rates may affect the presented values here.

8. Some validation data would greatly increase the value of the reported work. I would therefore encourage the authors to consider acquiring some additional datasets to compare measures of CSF draining against another method e.g. 2-D or 4-D phase contrast, or Gd-based contrast-enhanced techniques. Some additional points to consider are noted below.

8. Abstract

CSF outflow may also be imaged with phase contrast MRI (albeit in a limited way).<br /> Demographics would fit better in Results, breakdown could be given for the young and old groups i.e. n, ages, sex.<br /> Conclusion - unless further validation can be provided I think some of the claims should be toned down.

9. Introduction

The authors emphasise the role of Nedergaard, however, there was some relevant earlier work (e.g. Rennels et al, PMID: 2396537).

10. Methods

It would be more conventional to summarise the volunteer characteristics in the Results.<br /> Given the age difference between the two groups, and the fact that for conventional ASL we know of differences in labelling efficiency and the need for a different post-labelling duration in more elderly patients how did the authors account for this?<br /> More broadly what would the effect of differences in labeling efficiency be, given the labeling plane is unlikely to be perpendicular to the draining vessels?<br /> While the authors mention circadian effects there is no mention of controlling for other factors before the scan e.g. caffeine consumption, smoking, etc.<br /> Various mechanisms have been hypothesised to drive glymphatic pulsations. Assessing how physiological signals correlated with the flow may have been a useful proof of concept. Why was it not considered necessary to use a gated acquisition? Did the authors consider the potential impact of respiratory and cardiac pulsations on their measurements?<br /> ROI segmentation - manually selected by two raters, was this done independently and blinded? How were consensus ROIs agreed?<br /> Intensity values outwith MEAN +/- 2 SD were excluded from further analyses. This is justified as removing pulsatile blood. However, was this done independently for tag-on and tag-off? Does this mean slight differences were present in the number of voxels between the two?<br /> The starting points and parameter ranges are given in Eq'n 3, how were the ranges defined? Was there a reason for constraining the fit to positive values only, is there a risk of bias from this?<br /> While the main results appear to have a reasonable sample size n=2 for the reproducibility analysis is very limited. Additional datasets would be useful in properly interpreting the results.

11. Results<br /> While the authors have taken some measures to reduce potential contamination from blood I would be concerned about the risk of surface vessels affecting the signal, and there does not seem to be an evaluation of how effective their measures are.<br /> The labeling pulse is applied in the oblique sagittal orientation, but in tandem with differing rates of blood flow and CSF drainage from the labeling plane does that not risk circulating flow from other slices potentially affecting the values?<br /> Figure 4. The authors focus on the parasagittal dura, but in both the subtraction image and panel C showing different slices at TI=1250 ms some movement appears visible in the opposing hemisphere. Similarly in S2 If the signal does represent CSF movement then this seems counterintuitive and should be explained.<br /> In Figures 4 and 5 the angulation of the TIME-SLIP tag pulse seems quite different. What procedure was used to standardise this, and what effect may this have on the results?

12. Discussion<br /> Phrasing error 'which will be assessed in future studies'.<br /> I would suggest that some of the claims of novelty be moderated e.g. 'may facilitate establishment of normative values for CSF outflow' seems a stretch given multiple pathways exist and this is only considered one.<br /> More consideration should be given to some of the points mentioned in the results. The lack of validation should be properly discussed.

Author Response

Reviewer #1 (Public Review):

This manuscript describes the generation and characterization of a mouse knockout model of Cep78, which codes for a centrosomal protein previously implicated in cone-rod dystrophy (CRD) and hearing loss in humans. Previous work in cultured mammalian cells (including patient fibroblasts) also indicated roles for CEP78 in primary cilium assembly and length control, but so far no animal models for CEP78 were described. Here, the authors first use CRISPR/Cas9 to knock out Cep78 in the mouse and convincingly demonstrate loss of CEP78 protein in lysates of retina and testis of Cep78-/- animals. Next, by careful phenotypic analysis, the authors demonstrate significant defects in photoreceptor structure and function in these mutant animals, which become more severe over a 9 (or 18) month period. Specifically, TEM analysis demonstrates ultrastructural defects of the connecting cilium and photoreceptor outer segments in the Cep78 mutants, which is in line with previously reported roles for CEP78 in CRD and in regulating primary cilia assembly in humans. In addition to a CRD-like phenotype, the authors also convincingly show that male Cep78-/- animals are infertile and exhibit severe defects in spermatogenesis, sperm flagella structure and manchette formation (MMAF phenotype). Furthermore, the authors provide evidence for an MMAF phenotype from a male individual carrying a previously reported CEP78 c.1629-2A>G mutation, substantiating that CEP78 is required for sperm development and function in mammals and supporting previously published work (Ascari et al. 2020).

Finally, to identify the underlying molecular mechanism by which CEP78 loss causes MMAF, the authors perform some biochemical analyses, which suggest that CEP78 physically interacts with IFT20 and TTC21A (an ortholog of Chlamydomonas IFT139) and might regulate their stability. The authors conclude that CEP78 directly binds IFT20 and TTC21A in a trimeric complex and that disruption of this complex underlies the MMAF phenotype observed in Cep78-/- male mice. However, this conclusion is not fully justified by the data provided, and the mechanism by which CEP78 affects spermatogenesis therefore remains to be clarified.

Specific strengths are weaknesses of the manuscript are listed below.

Strengths:

Overall, the phenotypic characterisation of the Cep78-/- animals appears convincing and provides new evidence supporting that CEP78 plays an important role in the development and function of photoreceptors and sperm cells in vertebrates.

Weaknesses:

1) The immunoprecipitation experiments of mouse testis extracts that were used for the mass spectrometry analysis in Table S4 were performed with an antibody against endogenous CEP78 (although antibody details are missing). One caveat with this approach is that the antibody might block binding of CEP78 to some of its interactors, e.g. if the epitope recognized by the antibody is located within one or more interactor binding sites in CEP78. This could explain why the authors did not identify some of the previously identified CEP78 interactors in their IP analysis, such as CEP76 and the EDD-DYRK2-DDB1-VprBP complex (Hossain et al. 2017) as well as CEP350 (Goncalves et al. 2021).

We thank Reviewer #1 (Public Review) for agreeing with us on Cep78 plays an important role in photoreceptors and sperm cells development. We also appreciate Reviewer #1 (Public Review) for pointing out the weaknesses which helped us improve our study.

For the immunoprecipitation experiments of mouse testis extracts, the antigenic sequence of the Cep78 antibody used is p457-741 (NP_932136.2). Cep78 was reported to bind DD-DYRK2-DDB1-VprBP complex, the 1-520aa is responsible for Cep78’s interaction with VprBP, and deletion of p450-497 didn’t affect Cep78’s interaction with VprBP, indicating importance of Cep78 (1-450aa) in interaction with VprBp (Hossain et al. 2017). Our anti-Cep78 antibody is generated using antigen sequence p457-741, the binding of p1-450aa to VprBP is not expected to be blocked by our anti-Cep78 antibody. However, VprBp was not detected by our IP-MS experiment. C-terminal region (395-722aa) of Cep78 overlaps with our Cep78 antibody’s antigenic region (p457-741), and was reported to interact with Cep350 (Goncalves et al. 2021). As a polyclonal antibody, our anti-Cep78 antibody didn’t block the interaction with p457-741, because we still identified Cep350 in our IP-MS. Thus, immunoprecipitation experiments using our Cep78 antibody identified some of the previously known interactors, and the interaction with VprBP may not be blocked by our Cep78 antibody.

The detailed antibody information has now been added to Supplementary Table S7 in our revised supplementary materials.

2) Figure 7A-D and page 18-25: based on IPs performed on cell or tissue lysates the authors conclude that CEP78 directly binds IFT20 and TTC21A in a "trimeric complex". However, this conclusion is not justified by the data provided, nor by the previous studies that the authors are referring to (Liu et al. 2019 and Zhang et al. 2016). The reported interactions might just as well be indirect. Indeed, IFT20 is a known component of the IFT-B2 complex (Taschner et al., 2016) whereas TTC21A (IFT139) is part of the IFT-A complex, which suggests that they may interact indirectly. In addition, the IPs shown in Figure 7A-D are lacking negative controls that do not coIP with CEP78/IFT20/TTC21A. It is important to include such controls, especially since IFT20 and CEP78 are rich in coiled coils that tend to interact non-specifically with other proteins.

Thank Reviewer #1 (Public Review) for the comment on protein interaction between Cep78, Ift20, and Ttc21a. As the reviewer pointed out, IFT20 is a known component of the IFT-B2 complex (Taschner et al., 2016) whereas TTC21A (IFT139) is part of the IFT-A complex. Both IFT20 and TTC21a are located at peripheral areas of IFT-B and IFT-A (PMID: 32456460), and are not core components of IFT-A or IFT-B. It is still possible that these two proteins interact with each other. Actually, Liu et al. have revealed interaction between Ift20 and Ttc21a in human sperm (PMID: 30929735). Additionally, to mediate trafficking of ciliary axonemal components, the IFT machinery is recruited to the distal appendages (PMID: 30601682), which is adjacent to the distal end of the (mother) centriole wall, where at the (mother) centriole wall was reported to be located (PMID:35543806). Cep78 may interact with Ift20 and Ttc21a at centriole during cilliogenesis.s

To rule out the nonspecific interaction between Cep78 and Ttc21a or Ift20, we added additional negative controls of Gapdh (Figure 7D) and Ap80-NB-HA (Supplementary Figures S7A-C) in co-IP as the reviewer suggested, and found that the interaction between Cep78 and Ttc21a or Ift20 is specific. To examine if Cep78, Ift20 and Ttc21a formed a complex, we fractionated testicular protein complexes using size exclusion chromatography, and found that Cep78, Ift20 and Ttc21a co-fractioned at the size between158 kDa to 670 kDa (Figure 7E), supporting the formation of a trimeric complex. And our immunofluorescent analysis by SIM also showed co-localization between Cep78 and Ift20 or Ttc21a (Figure 7F). All these data support the interaction among Cep78, Ttc21a and Ift20. In the revised manuscript, we rephrased “direct interaction” as “interaction” at page 18, line 393 in the revised manuscript.

3) In Figure 7D, the input blots show similar levels of TTC21A and IFT20 in control and Cep78-/- mouse testicular tissue. This is in contrast to panels E-G in the same figure where TTC21A and IFT20 levels look reduced in the mutant. Please explain this discrepancy.

Thank you for pointing this out. Deletion of Cep78 caused down-regulation of Ttc21a and Ift20 proteins. To better reveal the change of interaction between Ttc21a and Ift20, we have to normalize their interaction against expression levels. To achieve this, we increased the amount of total Cep78-/- testicular proteins to ensure that Ttc21a and Ift20 in the input are at similar levels between Cep78+/- and Cep78-/- testes. Using 3 times the amount of the Cep78+/- testicular proteins for Cep78-/- testicular proteins, we detected similar protein levels of Ttc21a and Ift20 between Cep78-/- and Cep78+/- testes, and the interaction between Ttc21a and Ift20 was shown to be down-regulated after Cep78 deletion. Consistently, the analysis of GAPDH as a loading control in input proteins showed more Cep78-/- testicular proteins than Cep78+/- testicular proteins subjected to analysis. To avoid confusion, we have added description of “The amount of Cep78-/- testicular proteins used was 3 times of that of Cep78+/- proteins” in the legend of Figure 7D in the revised version of manuscript.

4) The efficiency of the siRNA knockdown shown in 7J-M was only assessed by qPCR (Figure S4), but this does not necessarily mean the corresponding proteins were depleted. Western blot analysis needs to be performed to show depletion at the protein level. Furthermore, it would be desirable with rescue experiments to validate the specificity of the siRNAs used.

Thank the reviewer for the suggestion. To validate the specificity of the siRNAs used, we performed rescue experiments using rescue plasmid with siRNA targeting sequence synonymously mutated (Supplementary Table S6). The efficiency of siRNA knockdown and effects of rescue experiments were evaluated by both qPCR (Supplementary Figures S4.A-C) and Western Blot (Figures 7.J-K, Supplementary Figures S4.D-E, H-I). The results showed that siRNAs significantly reduced the expression of Cep78, Ift20, and Ttc21a at both mRNA (Supplementary Figures S4.A-C) and protein levels (Figures 7.J-K, Supplementary Figure S4.A-C). Meanwhile, with siRNA treatment, the rescue plasmids rescued the expression of Cep78, Ift20, and Ttc21a at both mRNA (Supplementary Figures S4.A-C) and protein levels (Figures 7.J-K, Supplementary Figures S4.D-E, H-I) compared with the control groups.

In the rescue experiments, we further evaluated whether the effects are specific for Cep78, Ift20 and Ttc21siRNAs in the regulation of cilia and centriole lengths. The results showed that suppression of cilia and centriole lengths by Cep78, Ift20 and Ttc21siRNAs could be rescued by overexpression of rescue plasmids of Cep78syn-HA, Ift20syn-Flag and Ttc21asyn-Flag (Figures 7.N-S).

5) Figure 7I: the resolution of the IFM is not very high and certainly not sufficient to demonstrate that CEP78, IFT20 and TTC21A co-localize to the same region on the centrosome, which one would have expected if they directly interact.

Thank the reviewer for the constructive comments. To better demonstrate co-localization of CEP78, IFT20 and TTC21A on the centrosome, we overexpressed Cep78-Halo, Ift20-mCherry and Ttc21a-mEmerald in NIH3T3 cells by lentivirus, and acquired super-resolution images with SIM (N-sim, Nikon, Tokyo, Japan). The SIM results showed that Ift20 and Ttc21a co-localized with Cep78 (Figure 7F). Cep78 was previously reported to localize at the centriole (Goncalves et al., 2021). The co-localization of Cep78, Ift20 and Ttc21a indicated possible important roles of Cep78 in the regulation of Ift20 and Ttc21a in centriole. Our interaction analysis revealed that Cep78 interacted with Ift20 and Ttc21a (Figure 7A-C, Supplementary Figure S7), and formed a complex with Ift20 and Ttc21a (Figure 7E). Loss of Cep78 down-regulated the expression of and interaction between Ift20 and Ttc21a (Figures 7D, G-M).

6) It is not really clear what information the authors seek to obtain from the global proteomic analysis of elongating spermatids shown in Figure 3N, O and Tables S2 and S3. Also, in Table S2, why are the numbers for CEP78 in columns P, Q and R so high when Cep78 is knocked out in these spermatid lysates? Please clarify.

Thank the reviewer for the comments. Our global proteomic analysis showed that majority of differentially expressed proteins were down-regulated (Figure 3N), and many proteins are centrosome- and cilia-related proteins and important for sperm flagella and acrosome structures (Figure 3O), which provide insights of downstream molecular events in sperm flagella and acrosome defects after Cep78 deletion.

As to the quantification of CEP78 expression in TMT-based proteomics analysis, the ratio between Cep78-/- and Cep78+/- is relatively high due to the ratio compression effect, a well-known phenomenon in TMT-based proteomics analysis (PMID: 25337643). The actual difference in protein expression is usually higher than the ratio calculated by TMT signals. Actually, our Western blot analysis of CEP78 protein showed absence of expression in Cep78-/- testis. Although TMT labelling has the disadvantage of ratio compression (PMID: 32040177，PMID: 23969891), it is widely used quantitative proteomics analysis, and is demonstrated to be able to identify key pathways and proteins (PMID: 30683861, 33980814).

7) Figure 1F and Figure 4K: the data needs to be quantified.

Thank the reviewer for this suggestion. For Figure 4K, we stained Cep78+/- and Cep78-/- spermatids with anti-Centrin 1 to measure the centriole length. The statistical data of centriole length were provided (Figure 4L), showing significantly increased centriole lengths in Cep78-/-spermatids.

For Figure 1F, we quantified the immunofluorescence intensities of cone arrestin of light-adapted retinas of Cep78+/- and Cep78-/- mice at 3-month. The results indicate that immunofluorescence intensity of the cone arrestin was lower in Cep78-/- mice.

8) Figure 2A: It is difficult to see a difference in connecting cilium length in control and Cep78-/- mutant retinas based on the images shown here.

Thank you for your suggestion, we have stained retinal cryosections from Cep78+/- and Cep78-/- mice with anti-Nphp1 to visualize connecting cilium, and the data are provided in the revised Figure 2A-B.

Reviewer #2 (Public Review):

In this report, the authors have described the generation and characteristics of Cep78 mutant mice. Consistent with the phenotype observed in patients carrying the mutations in CEP78, Cep78 knock-out mice show degeneration in photoreceptors cells as well as defects in sperm. The author further shows the CEP78 protein can interact with IFT120 and TTC21a. Mutation in CEP78 results in a reduction of protein level of IFT120 and TTC21A and mislocalization of these two proteins, offering mechanistic insights into the sperm defects. Over all the manuscript is well written and easy to follow. Phenotyping is thorough. However, improvement of the background section is needed. In addition, some of the conclusion is not sufficiently supported by the data, warranting further analysis and/or additional experiments. The Cep78 KO mice model established by the author will be a useful model for further elucidating the disease mechanism in human and developing potential therapy.

My comments are the following:

1) Introduction. The statement that "CRD usually exists with combination of immotile cilia defects in other systems" is not correct. CRD due to ciliopathy can have cilia-related syndromic defects in other systems but it is a relatively small portion of all CRDs and the most frequently mutated genes are not cilia-related genes, such as ABCA4, GUCY2D, CRX.

Thank the reviewer for the comments. We agree with the reviewer that only a small portion of CRDs are due to cilia defects and can have cilia-related syndromic defects in other systems. We corrected this statement in Line 4, Page 77-79 of the revised version of our manuscript. In our revised version, the statement has been changed to “A small portion of CRDs are due to retina cilia defects, and they may have cilia-related syndromic defects in other systems[1].”

2) Introduction: Page 4 CNGB1 encodes channel protein and not a cilia gene. It should be removed since it does not fit.

Thank the reviewer for the comment. According to the reviewer’s suggestion, we removed the description of “mutations in CNGB1 cause CRD and anosmia [3]” at Page 4, Line 81 in the revised manuscript.

3) Page 5, given the previous report of CEP78 patients with retina degeneration, hearing loss, and reduced infertility, the statement of "we report CE79 as a NEW causative gene for a distinct syndrome...TWO phenotypes....." Is not accurate.

Thank the reviewer for the comments. We have removed the statement of “NEW” causative gene in Page 5, Line 104 of the revised version of our manuscript. The revised sentence is “In this study, based on results of a male patient carrying CEP78 mutation and Cep78 gene knockout mice, we report CEP78 as a causative gene for CRD and male sterility.”

4) Figure 1F, the OS of the cone seems shorter, which might be the reason for weaker arrestin staining in the mutant compared to the heterozygous. Also, it would be better to quantify the staining to substantiate the statement.

Thanks for this suggestion. For Figure 1F, we have quantified the immunofluorescence intensity of cone arrestin in Cep78+/- and Cep78-/- light-adapted retinas at 3-month. The results indicate that immunofluorescence intensity of the cone arrestin was significantly lower in Cep78-/- mice.

5) Figure 1K, panel with lower magnification would be useful to get a better sense of the overall structure defect of the retina. Is the defect observed in the cone as well?

Thank the reviewer for the comment. As suggested by the reviewer, we have provided images of lower magnification to show the overall structure by TEM, showing disruption of most outer segment in Cep78-/- retina. It is difficult to distinguish whether the disordered outer segment structure belongs to a cone or a rod cell. The images are now provided as Figure 1L in the revised manuscript.

We observed the abnormality of photopic b-wave amplitudes (Figure 1B, E) and decreased intensity of cone arrestin in light-adapted retinas (Figure 1F, G) in Cep78-/- mice, which indicate that the function of cone cells is damaged.

6) Figure 2A, NPHP1 or other markers specifically label CC would be more useful to quantify the length of CC. Also need to provide a notation for the red arrows in Figure 2. In addition, the shape of CC in the mutant seems differ significantly from the control. It seems disorganized and swollen.

Thank the reviewer for the suggestion. According to the reviewer’s suggestion, we have stained anti-Nphp1 in retinal cryosections from Cep78+/- and Cep78-/- mice to visualize connecting cilium, and quantified the length of CC. The results showed that connecting cilia were shorter in Cep78-/- mice. These data are showed in Figure 2A-B.

Besides, we observed that upper parts of connecting cilia were swelled with disorganized microtubules in TEM (Figure 2E-G). The red arrows in Figure 2E-G indicated swelled upper part of connecting cilia and disorganized microtubules of Cep78-/- photphoreceptors, we added this description in the figure legend.

7) Evidence provided can only indicate direct interaction among CEP78/IFT20/TTC21A.

Thanks for the comment. To further validate the interaction between Cep78 and Ttc21a or Ift20, we performed reciprocal co-IP between Cep78 and Ttc21a or Ift20 by overexpression (Figure 7A-C), and also added relevant negative control of Gapdh (Figure 7D) and Ap80-NB-HA (Supplementary Figures S7A-C) in co-IP as negative controls to avoid non-specific interaction. Besides, we provided evidence that Cep78, Ift20 and Ttc21a formed a complex, as they all co-fractioned in a testicular protein complex at the size between158 kDa to 670 kDa using size exclusion chromatography (Figure 7E). Additionally, we performed super-resolution analysis of immunofluorescent localizations, and observed co-localization between Cep78 and Ttc21a or Ift20 by SIM. With these data, we think that Cep78 interacts with Ttc21a and Ift20 and they form a complex. We rephrased “direct interaction” as “interaction” in the manuscript.

Reviewer #3 (Public Review):

Authors were aiming to bring a deeper understanding of CEP78 function in the development of cone-rod dystrophy as well as to demonstrate previously not reported phenotype of CEP78 role in male infertility.

It is important to note, that the authors 're-examined' already earlier published human mutation, 10 bp deletion in CEP78 gene (Qing Fu et al., 10.1136/jmedgenet-2016-104166). This should be seen as an advantage since re-visiting an older study has allowed noting the phenotypes that were not reported in the first place, namely impairment of photoreceptor and flagellar structure and function. Authors have generated a new knockout mouse model with deleted Cep78 gene and allowed to convey the in-depth studies of Cep78 function and unleash interacting partners.

The authors master classical histology techniques for tissue analysis, immunostaining, light, confocal microscopy. They also employed high-end technologies such as spectral domain optical coherence tomography system, electron, and scanning electron microscopy. They performed functional studies such as electroretinogram (ERG) to detect visual functions of Cep78-/- mice and quantitative mass spectrometry (MS) on elongating spermatids.

The authors used elegant co-immunoprecipitation techniques to demonstrate trimer complex formation.

Through the manuscript, images are clear and support the intended information and claims. Additionally, where possible, quantifications were provided. Sample number was sufficient and in most cases was n=6 (for mouse specimens).

The authors could provide more details in the materials and methods section on how some experiments were conducted. Here are a few examples. (i) Authors have performed quantitative mass spectrometry (MS) on elongating spermatids lysates, however, did not present specifically how elongating spermatids were extracted. (ii) In the case of co-IPs authors should provide information on what number of cells (6 well-plate, 10 cm dish etc) were transfected and used for co-IPs. Furthermore, authors could more clearly articulate what were the novel discoveries and what confirmed earlier findings.

The authors clearly demonstrate and present sufficient evidence to show CEP78/Cep78 importance for proper photoreceptor and flagellar function. Furthermore, they succeed in identifying trimer complex proteins which help to explain the mechanism of Cep78 function.

The given study provides a rather detailed characterization of human and mouse phenotype in response to the CEP78/Cep78 deletion and possible mechanism causing it. CEP78 was already earlier associated with Cone-rod dystrophy and, this study provides a greater in-depth understanding of the mechanism underlying it. Importantly, scientists have generated a new knock-out mouse model that can be used for further studies or putative treatment-testing.

CEP78/Cep78 deletion association with male infertility is not previously reported and brings additional value to this study. We know, from numerous studies, that-testes express multiple genes, some are unique to testes some are co-expressed in multiple tissues. However, very few genes are well studied and have clinical significance. Studies like this, combining patient and animal model research, allow to identify and assign function to poorly characterized or yet unstudied genes. This enables data to use in basic research, patient diagnostics and treatment choices.

We would like to thank Reviewer #3 (Public Review) for positive comments on our work.

As to the suggestions to provide some details in the materials and methods by the reviewer, we added the description of STA-PUT method for spermatids purification at Page 34, Line 729-741 in the revised manuscript, the amount of cells used for co-IPs “10 cm dish HEK293T were transfected (Vazyme, Nanjing, China) wit 5μg plasmid for each experimental group.” at Page 36, Line 783-784 in the revised manuscript.

We also highlighted our new discovery and ensured that all previous published findings are accompanied by references, we added “We further explored whether c.1629-2A>G mutation in this previously visited patient would disturb CEP78 protein expression and male fertility. Blood sample was collected from this patient and an unaffected control for protein extraction.” at Page 17, Line 335. We also added “The major findings of our study are as follows: we found CEP78 as the causal gene of CRD with male infertility and multiple morphological abnormalities of the sperm flagella using Cep78-/- mice. A male patient carrying CEP78 c.1629-2A>G mutation, whom we previously reported to have CRD [8], was found to have male infertility and MMAF in this study. Cep78 formed a trimer with sperm flagella formation enssential proteins IFT20 and TTC21A (Figure 8), which are essential for sperm flagella formation[16, 18]. Cep78 played an important role in the interaction and stability of the trimer proteins, which regulate flagella formation and centriole length in spermiogenesis. ” at the first paragraph of discussion, which is Page 21, Line 447-456 of our revised manuscript.

Author Response

Reviewer #1 (Public Review):

This excellent manuscript challenged the premise that NF-kappaB and its upstream kinase IKKbeta play a role in muscle atrophy following tenotomy. Two animal models were used - one leading to enhanced muscle-specific NF-kappaB activation and the other a muscle-specific deletion. In both models, there was no significant relationship to observed muscle changes following tenotomy. Overall this work is significant in that it challenges the existing dogma that NF-kappaB plays a crucial role in muscle atrophy.

Surprisingly the authors noted that there were basal differences observed in the phenotypes of their models that were sex-dependent. They note that male mice lose more muscle mass after tenotomy and specifically type 2b fiber loss.

Overall this is an outstanding study that challenges the notion that NF-kappaB inhibitors are likely to improve muscle outcomes following injuries such as rotator cuff tears. Its main weakness is that there were no pharmacological arms of investigation; this fails to definitively exclude the hypothesis that inhibition may exert some effect in healing, perhaps in surrounding non-muscle matrix tissue that in turn may assist in healing.

Thank you for your careful and thoughtful review. We agree that the finding that NFkb is not driving tenotomy-induced atrophy is both surprising and interesting. We look forward to further uncovering the atrophic mechanisms responsible. We also agree that an investigation using pharmacological NFkb inhibitors will improve our understanding of the full scope of the role of NFkb in the tenotomy pathology. As you and another reviewer note, this work has only blocked NFkb signaling in the mature muscle fiber and thus cannot assess the role of NFkb in satellite cell, fibroblast, immune cell activation etc in the healing response. However, we avoided using these inhibitors in this study due to the potential for these systemic effects to obscure the role of NFkb in the muscle fiber. While we believe that a pharmacological investigation is beyond the scope of this study, it will make an excellent follow on investigation.

Reviewer #2 (Public Review):

The primary strength of this paper is a rigorous approach to 'negative' data. Did the authors definitively prove that NF-kB has no role in the tenotomy-induced atrophy? Probably not entirely, since there are limitations of the mouse model and the knockdown mice. There cannot be complete elimination of load since mice heal with some scar tissue, and the knockdown is not complete elimination. However, even with these limitations, this presents important findings that tenotomy, which induces mechanical unloading of the muscle-tendon unit, provides a unique biomechanical environment for the muscle to undergo atrophy, which warrants a more in-depth look given that these injuries are unique and extremely common. It must be mentioned that the results are entirely supported by their data and that even though the model is not 'perfect' it truly supports that NF-kB has a limited role in atrophy. The sex-mediated differences based on autophagy are a secondary hypothesis and are interesting but possibly less clinically relevant based on the differences shown.

We appreciate your thoughts on the “negative” data in this study. A manuscript in which the data refute your hypothesis and that of the field is difficult to write. There is a higher burden of validation and closer scrutiny of limitations. We agree that the model does have some limitations, but overall strongly supports a limited role for NBkb in tenotomy-induced muscle atrophy.

The important next step for this group and others is to evaluate the 'how and why' of tenotomy atrophy if not through NF-kB. Is it that there are many redundant processes that the muscle may have to circumnavigate the NF-kB pathway given that it is so ubiquitous that the authors didn't see a difference? Could it be differences in axial vs appendicular muscle? Or should there be a closer look at the mechanosensors in the muscle cells to determine if there are other key drivers of atrophy? Regardless, this paper shows that tenotomy-induced muscle atrophy is unique and supports the conclusion that muscle has many ways to atrophy based on the injury it undergoes.

We agree that the major next step for this work is to investigate the mechanism(s) responsible for tenotomy-induced atrophy. Autophagy in particular needs a more thorough investigation using autophagic inhibitors in naive wildtype mice to investigate its role in the sex-specificity of tenotomy-induced atrophy. The question of axial vs. appendicular muscle is intriguing. There could also be an upper vs. lower body difference that is worth exploring in future work.

Reviewer #3Public Review):

The authors provided thorough analyses of muscle morphology, biochemistry, and function, which is a major strength of the study. However, there are some key confounding variables authors failed to address. For example, the difference in the estrous cycle in female animals was not controlled. The study could have been significantly improved by controlling sex hormone levels or at least testing differences in response to injury.

We appreciate your careful and insightful review of our work. We designed this study to assess the role of myofiber NFkb in tenotomy-induced atrophy, which led us to a rigorous assessment of morphology, biochemistry and function, which we agree is the strength of the study. We also agree that a major limitation of this study is that the secondary observations of sex-specificity and autophagic signaling are not as well controlled or supported. This is because these observations were made at the end of the study when the histological analyses were completed by the blinded rater. The sex-specificity in the basophilic puncta that the rater observed sparked us to reconsider the sex-specificity in our other data and to stain for autophagic vesicles. As you suggest, to rigorously assess sex-specificity it would be good to control of estrous cycle and analysis of sex hormones which would require initiation of another study, planning for these variables in advance. We think this is beyond the scope of the current question of the role of NFkb in tenotomy-induced atrophy but think it should be undertaken as a follow on to eliminate confounding variables of genetic manipulation and tamoxifen treatment.

However, since we still need to report the sex specificity we observed while ensuring that our findings are not misconstrued, we reviewed the language in the manuscript to emphasize that these are retrospective observations that require further investigation. We have also added discussion of these variables and their potential influence on the results to the Discussion.

Discussion: “Additionally, it is important to note that estrous cycle was not controlled in these mice and sex hormone levels weren’t measured in this study. These preliminary observations, though intriguing, will require more rigorous follow up evaluations to define the interaction between sex, tenotomy, and autophagy in naïve wildtype mice.”

Furthermore, more data are needed to link NFkB signaling and autophagy to make any kind of conclusions. Overall, in the current form of the manuscript, the presented data seem underdeveloped, and the addition of more supporting data could significantly improve the quality of the manuscript and enhance our understanding of NFkB signaling and muscle wasting in rotator cuff injury.

We agree that more data are needed to complete the picture of autophagy in tenotomy-induced muscle atrophy. The p62 and LC3 positive intracellular puncta in male tenotomized muscle are distinctive, but only limited conclusions can be drawn physiologically because 1) they are only present in a fraction of fibers and 2) it is impossible to tell whether they result from increased autophagic flux or altered vesicle processing. Western blot for LC3 (and now p62) indicates only small changes in total protein, but since these proteins are synthesized and degraded during active autophagy, it is possible for their levels to remain constant while flux increases. Direct measures of autophagic flux would require treating mice with an autophagosome block which would require initiation of another study. However, we agree with the reviewer that we can add some additional measures to better characterize the instantaneous state.

We have added analysis of p62 protein expression to LC3 since p62 protein content in muscle can be decoupled from LC3 (PMID: 27493873). We also added expression data for genes involved in autophagy (Lc3b, Gabarapl1, Becn1, Bnip3, and Atg5). Finally, we have commented on the limitations of our data in the Discussion.

Discussion: “Evidence for autophagy regulating tenotomy-induced atrophy has been mounting over recent years (Bialek et al., 2011; Gumucio et al., 2012; Joshi et al., 2014; Ning et al., 2015; Hirunsai & Srikuea, 2021). The evidence presented here supports this contention, but we find surprisingly small effect sizes for all markers investigated. This could be because we are not directly assessing autophagic flux and so are missing some temporal dynamics since synthesis and degradation are ongoing simultaneously.”

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Reply to the reviewers

Summary of changes

We thank all three reviewers for their constructive feedback on our manuscript. We have now perfomed extensive experiments, analyses, and rewriting of our manuscript to address all their concerns. We believe that these changes significantly improve the rigor of our conclusions and the clarity of our discussion. We highlight below key experiments, analyses, and re-writing in the revised manuscript, which is followed by a detailed point-by-point response. 1) We have now performed experiments using alternative uORF donor sequences to demonstrate the robustness of uORF repression to changes in uORF length.

2) By mutating out near-cognate start codons within uORF2, we have now demonstrated that near-cognate start codon initiation within uORF2 does not impact repression.

3) To quantify the dynamic range of our dual luciferase assay, we have now mutated out the NLuc start codon. We find that repressive uORF2 constructs have expression levels that are still > 20-fold above the no-startcodon control values.

4) We have now analyzed ribosome profiling coverage on uORFs (supplementary figure 5), and we show that several uORFs with known elongation stalls lack evidence of 40S and 80S subunit queueing 5′ to stalls, consistent with our collision-induced ribosome dissociation model.

5) We have now provided detailed discussion of footprint length choice in our modeling and the role of codon choice in our experiments.

6) We have now added a new main figure that provides a graphical representation of reactions considered in our kinetic modeling. This figure will make our modeling assumptions more transparent and accessible to readers with less computational expertise.

Reviewer #1:

Summary

Bottorff et al test several models of uORF-mediated regulation of main ORF translation using the uORF2 of CMV UL4 gene, a system that has been previously experimentally characterized by the authors. They first train a computational model to recapitulate the observed experimental effects of mutations in uORF2, and then use the model to infer which uORF parameters may confer buffering against reduced ribosome loading that typically occurs upon biological perturbation. The authors then find that: i) the uORF2 confers buffering, ii) the uORF2 mechanism adjusts to computational predictions for the collision-mediated 40S dissociation model of uORF-mediated regulation. Significance

This manuscript represents an interesting effort to distinguish mechanisms of uORF-mediated regulation based on mathematical modeling, and might be useful for the translation community. My expertise: Regulation of translation.

We thank Reviewer 1 for a succinct summary of our main conclusions and highlighting the significance of our work to the translation community.

Major comments 1) Figure 4 (Figure 5 in revised version): Which is the dynamic range of the WT vs the no-stall construct? In the WT construct, main ORF translation is already quite repressed, and detecting further repression may be more difficult than in the no-stall construct. In other words, the differences that authors are detecting between the WT and no-stall constructs might be due to a potential lower dynamic range of the WT construct

To measure the dynamic range of our reporter assay, we have now mutated the start codon of the NLuc reporter ORF. We reasoned that this construct provides a lower bound on measurable NLuc signal. The resulting noNLuc-start-codon reporter expression was at least 20-fold lower than WT construct (Fig. S1A). Importantly, we also see that the raw NLuc signal of the WT construct is at least 20-fold over the background (Fig. S1B). Thus, the differential response of WT and no-stall constructs is not simply due to lower dynamic range of the WT construct.

2) The authors conclude that uORF2 follows the collision-mediated 40S dissociation model, based on fitness of their experimental results with predictions from their mathematical modeling regarding distance between uORF2 initiation codon and the stalling site. But can the authors actually directly prove that there are no 40S subunits accumulating behind the stalled 40S using Ribo-Seq or TCP-Seq?

We have now examined existing 80S Ribo-seq and 40S TCP-seq datasets to determine whether queued 40S or 80S ribosomes can be detected at known stall sites. Stern-Ginossar et al. (2012) performed 80S Ribo-seq during hCMV infection. In this dataset, while the stall at the UL4 termination codon has a very high ribosome density, few elongating ribosomes are seen queued behind the stalled 80S, consistent with an absence of 80S ribosome queuing (Fig. RR1). By contrast, another well-studied elongation stall in the Xbp1 mRNA shows ~30 nt periodic peaks in ribosome density indicative of ribosome queues (Fig. RR2). An important caveat is that queued ribosomes could be systematically underrepresented in standard Ribo-seq datasets due to incomplete nuclease digestion (Darnell et al., 2018; Subramaniam et al., 2014; Wolin and Walter, 1988).

Since there is no 40S TCP-Seq dataset during hCMV infection, we examined other known stalls on human mRNAs (Fig. RR3 below; Fig. S5 in our manuscript). We examine small ribosomal subunit profiling data from human uORFs with conserved amino acid-dependent elongating ribosome stalls (Figure S5A). Ribosome density read counts are low across all of these uORFs, showing no evidence of ribosome queuing. Subtle queues might not be observed given these low read counts from insufficient capture of small ribosomal subunits. Nevertheless, we do not observe any evidence of queueing upstream to elongating ribosome stalls in this data. We note these observations in our Discussion section as follows (lines 688-712): “Although our data from UL4 uORF2 does not support the queuing-mediated enhanced repression model (Fig. 1C) (Ivanov et al., 2018), this model might describe translational dynamics on other mRNAs. Translation from near-cognate start codons is resistant to cycloheximide, perhaps due to queuing-mediated enhanced initiation, but sensitive to reductions in ribosome loading (Kearse et al., 2019). Loss of eIF5A, a factor that helps paused elongating ribosomes continue elongation, increases 5′ UTR translation in 10% of studied genes in human cells, augmented by downstream in-frame pause sites within 67 codons, perhaps also through queuing-mediated enhanced initiation (Manjunath et al., 2019). There is also evidence of queuing-enhanced uORF initiation in the 23 nt long Neurospora crassa arginine attenuator peptide (Gaba et al., 2020) as well as in transcripts with secondary structure near and 3′ to start codons (Kozak, 1989). Additional sequence elements in the mRNA might determine whether scanning ribosome collisions result in queuing or dissociation. Small subunit profiling data (Wagner et al., 2020) from human uORFs that have conserved amino acid-dependent elongating ribosome stalls do not show evidence of scanning ribosome queues (Fig. S5A), consistent with the collision-mediated 40S-dissociation model. Subtle queues might not be observed given these low read counts from insufficient capture of small ribosomal subunits.”

3) Experimental data in Figures 2, 4 and 5 include 3 technical replicates. Sound conclusions typically require biological replicates. Further, the number of replicates in Figure 6 has not been indicated.

As suggested by the reviewer, we have now included biological replicates for all luciferase assays [Figures 2, 5, 6, and 7 that were previously 2, 4, 5, and 6] that were technical replicates in the previous version. This replication does not alter any of our conclusions. We have now included the number of biological replicates for Figure 7 (former Figure 6).

Minor comments 1) Figure 4 (Figure 5 in revised version): It is strange that a PEST sequence had to be introduced in the construct of part B in order to observe reliable differences, but not in constructs of parts A and C. Can the authors explain?

We introduced the PEST sequence for part B because we wanted to measure the reporter response to treatment with a drug that reduces translation initiation. The PEST sequence increases the turnover rate of the reporter protein. Without the PEST sequence, the luminescence signal will be dominated by the reporter expression before the drug was added. However, in parts A and C, initiation rate was altered through genetic mutations and measuring their expression under basal conditions does not require a PEST sequence. Except in situations where a quick dynamic response needs to be measured such as in the drug treatment in part B, reporters without PEST sequences are simpler to interpret due to the absence of proteasome-mediated degradation and higher overall signal.

2) Figure 6 (Figure 7 in revised version): Unfortunately, the authors find no other human uORFs with terminal diproline motifs that are so essential for main ORF repression as uORF2. In this light, can the authors comment further on the usefulness of their findings for human genes? Have the authors searched for viral RNAs with similar features? Please, notice that the gene PPP1R37 has not been mentioned in the main text.

The UL4 and human uORFs differ in their sequence determinants of translational repression. UL4 uORF2 represses translation entirely through nascent peptide-mediated stalling. While the terminal diproline motif in UL4 uORF2 is necessary for main ORF repression, it is not sufficient. A number of other residues in the UL4 uORF2 peptide play a critical role in repression (Cao and Geballe, 1996; Matheisl et al., 2015). Thus, it is not surprising that human uORFs that we identified based solely on the presence of terminal diproline motifs confer only modest decrease in repression upon mutating the terminal proline. The human uORFs containing these terminal diprolines may partially repress translation via nascent peptide effects, but the majority of the repression likely arises from siphoning of scanning ribosomes from the main ORF (Fig. 1A in our manuscript) and inefficient termination following translation of consecutive prolines (Cao and Geballe, 1996; Cao and Geballe, 1998; Janzen et al., 2002; Matheisl et al., 2015). Our current understanding of features in nascent peptide that mediate translational repression (Wilson et al., 2016) is insufficient to bioinformatically identify elongation-stall containing uORFs in human or viral genomes, so we simply looked for terminal diprolines. Despite this limitiation, we note that the modeling approaches and experimental perturbations developed in our work can be applied to study ribosome kinetics on any repressive uORF, independent of the mRNA or peptide sequence underlying the repression. As suggested by Reviewer 1, we have now included all the studied uORFs in the main text.

Reviewer #2:

Summary

In this paper, the authors are exploring the uORF regulatory mechanism. They first discussed five general models how uORFs might work to repress and buffering main ORF translation, then they mainly focus on the UL4 uORF2 for the potential mechanism. They use both computer modeling and experimental validation with reporter assay in 293t cell line. Based on their model, and few experimental results when they change the translation initiation rate and/or length of dORF, they propose it may work through 40S dissociation model, since the buffering effect is not uORF length sensitive. Significance

It is an interesting area, using modeling with experiment validation to understand uORF regulation mechanism, the kinetics and interplay between different translation steps, it will help us to understand uORF buffering in stress conditions. Also bring modeling method with reporter validation to the translation field, will provide clues to the molecular mechanism study, especially in complex situation.

We thank Reviewer 2 for a comprehensive summary of our work and noting the uniqueness and usefulness of our experiment-integrated modeling approach to the translation field.

Major comments • Are the key conclusions convincing? The modeling for different mechanisms is insightful, but some modeling parameters and experimental validation are not conclusive and validation of few of them can enforce the conclusions.

We have now performed key validation experiments suggested by Reviewer 2, notably: 1. mutating out of nearcognate start codons in the UL4 uORF2 coding sequence and 2. increasing UL4 uORF2 length using two unrelated protein coding sequences. Please see responses to specific comments below for further details.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Yes, the part about queuing and length sensitive is not convincing to me, it should be modified and reduce the statement strength.

We agree about reducing the statement strength and have altered our statements as suggested by the reviewer. Specifically, we have now expanded the rationale for the choice of footprint lengths of 40S subunits. Please see responses to specific comments below for further details.

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. Yes, please see the specific concerns • Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. They will need to re-think about the modeling, and validation in Figure 5, there are validation experiments that can be done in weeks and in a cost-efficient manner that can enforce the conclusions.

We have performed the experiments suggested by the reviewer. See responses below.

• Are the data and the methods presented in such a way that they can be reproduced? Most of them are good • Are the experiments adequately replicated and statistical analysis adequate? Yes Specific concerns 1) It is a bit confusing to me in Figure 2C, the reporter assays, that non-start codon reporter and non-stall reporter has same expression level. In theory, the non-stall reporter still has uORF there, so it should repress main ORF expression, and have lower expression level than the non-start reporter, where there is no uORF, no repression. In other uORFs they tested in Figure 6 (Figure 7 in revised version), the non-stall reporters are lower than non-start reporter. Since data they use to build the model is Figure 2B, and calculate the parameters for the whole paper, I just want to make sure it is making sense. I noticed there is another CTG in frame on the 4th codon, this may be alternative start codon in the non-start reporter to trigger some repression.

To address Reviewer 2’s concern about alternative start codon usage in the non-start reporter, we have now mutated out all near-cognate start codons known to initiate translation with high frequency (Kearse and Wilusz, 2017). These near-cognate start codons consisted of Leu4 CTG, Leu11 CTG, Leu14 TTG, and Leu15 CTG and were mutated to CTA, CTA, TTA, and CTA, respectively. We find that removing the uORF2 near-cognate start codons does not significantly alter NLuc expression (Fig. S1A). This experiment merely rules out one possible source of these similar expression levels. We expect that uORF2 no-start and no-stall reporters’ very similar NLuc expression levels can be rationalized for the several following reasons: 1. uORF2 initiation frequency is quite low. We estimate it to be 5% or less in our modeling based on previous measurements (Cao and Geballe, 1995). Thus, the maximum theoretically possible difference in NLuc expression between no-start and no-stall reporters is 5% or less. 2. Further, re-initiation after uORF2 translation is frequent. We estimate it to be around 50% within our manuscript, which will further decrease repression in the no-stall mutant. Thus, we expect the no-stall mutant to decrease the flux of scanning ribosomes at the main ORF by 2-3% compared to the no-start mutant. 3. Finally, a subtle but important point to note is that our reporter assays are measuring NLuc expression and not the flux of scanning ribosomes at the main ORF NLuc start codon. Since NLuc ORF has a strong start codon context (GCCACC) and the flux of scanning ribosomes is already high for the no-start and no-stall mutants, slight changes in the flux of scanning ribosomes are unlikely to impact NLuc expression. This is because start codon selection is not rate-limiting for protein expression under these conditions. This last point is clearly seen in high throughput reporter assays where the mutations which impact reporter expression in a non-optimal context have little or no effect in an optimal context (see Fig. 5B, 5C in Noderer et al., 2014).

Thus, in summary, even if the flux of scanning ribosomes is decreased by 3-5% by the no-stall uORF2 mutant compared to the no-start uORF2 mutant, we expect the effect on NLuc expression to be negligible and below the limit of our experimental resolution (which is ~10% based on the standard error across technical replicates).

Regarding the different behavior of the human uORFs in our manuscript and UL4 uORF2, note the response to Reviewer 1 regarding the usefulness of our human uORF findings.

2) All the modeling and prediction the authors do are based on average, but we know translation is very heterogeneous. For each ribosome or each 40S, the kinetics varies a lot, the authors should discuss about this part.

We now discuss translation heterogeneity in the Discussion section in lines 781-794 as follows: “Translation heterogeneity among isogenic mRNAs has been observed in several single molecule translation studies (Boersma et al., 2019; Morisaki et al., 2016; Wang et al., 2020; Wu et al., 2016; Yan et al., 2016). This heterogeneity may arise from variability in intrasite RNA modifications (Yu et al., 2018), RNA binding protein occupancy, or RNA localization. We do not capture these sources of heterogeneity in our modeling since the observables in our simulations are averaged over long simulated time scales and used to predict only bulk experimental measurements. However, our models studied here can readily extended through compartmentalized and state-dependent reaction rates (Harris et al., 2016) to account for the different sources of heterogeneity observed in single molecule studies.”

3) For modeling related with the queuing-mediated model in Figure 1C. they use 30nt as the ribosome length to count the potential queuing to start codon. But 30nt is the 80S protected fragment with specific conformation. The protected fragment for 80S will change based on different status of ribosome conformation or elongation step. More importantly, for queuing, it is 40S, so they may have a different size. Based on previous 40S ribosome profiling (Archer, Stuart K., et al. Nature 535.7613 (2016): 570-574. And other papers), the length can vary from 19nt to very long, so I don’t think the 30nt length can be used to model queuing in 40S and length sensitivity in the uORF working mechanism.

We thank Reviewer 2 for highlighting this issue of footprint length heterogeneity that we had not previously addressed. In our modeling, we assume homogenous ribosome footprints. While, heterogeneous ribosome footprints have been observed for small ribosomal subunits (Bohlen et al., 2020; Wagner et al., 2020; Young et al., 2021) and elongating ribosomes (Lareau et al., 2014; Wu et al., 2019), we believe that our modeling of homogenous footprint length is appropriate for the following three reasons: First, with respect to the small ribosomal subunit footprint heterogeneity, we note that TCP-seq studies include crosslinking of eukaryotic initiation factors (eIFs). The presence of these eIFs is thought to be the main source of heterogeneity in scanning ribosome footprints (Bohlen et al., 2020; Wagner et al., 2020). Although crosslinking is often performed, it is not necessary to obtain scanning ribosome footprints, and homogenous 30 nt footprints are observed in the absence of crosslinking (Bohlen et al., 2020). Notably, figure S2 of Bohlen et al. (2020), reproduced as Fig. RR4 below, shows that scanning SSU footprint lengths are tightly distributed around 30 nt when crosslinking is not used.

Second, in the context of the strong, minutes-long UL4 uORF2 elongating ribosome stall (Cao and Geballe, 1998), collided ribosomes will wait for long periods of time relative to normal elongating or scanning ribosomes. Thus, we expect that associated eIFs dissociate from these dwelling ribosomes as they typically do during start codon selection or during translation of short uORFs (Bohlen et al., 2020). Third, a significant fraction of mRNAs exhibit cap-tethered translation in which eIFs must dissociate from ribosomes before new cap-binding events, and therefore collisions, can occur (Bohlen et al., 2020). Based on above three points, we believe that modeling the footprint of only the scanning ribosomes, and not the associated eIFs, using a single 30 nt length is biologically reasonable. Footprint length heterogeneity of elongating ribosomes is much less drastic than that observed for scanning ribosomes and likely arises from different conformational states such as an empty or occupied A site (Lareau et al., 2014; Wu et al., 2019). While the different elongating ribosome footprints arise from differences in mRNA accessibility to nucleases, it is unclear whether the distance between two collided ribosomes changes across different ribosome conformations. For instance, the queues of elongating ribosomes observed at the Xbp1 mRNA stall occur at regular ~30 nt periodicity (Fig. RR2). Additionally, the stalled elongating ribosome is stuck in a pretranslocation state and has a defined, ~30 nt footprint (Wu et al., 2019), which only leaves room for 1 5′ queued ribosome within UL4 uORF2 whose footprint is conformation sensitive. Finally, a small degree of scanning footprint heterogeneity is also accounted for by our modeling of backward scanning which effectively introduces heterogeneity to collided scanning ribosome location on mRNAs (Figures 6A, S2D in our manuscript). We have now summarized the above points in the Discussion section of the revised manuscript (lines 713-740).

4) For Figure 5B (Figure 6B in revised version), besides the modeling length part I have mentioned above, when the authors increase the length of uORF, the sequence is also changed, which may introduce other side effect. So, if the authors want to conclude about the queuing part, they should rethink about the length for both modeling and validation, plus control for the sequence they added to increase the length of uORF, for example use different sequence when manipulate the length.

As suggested by the Reviewer, we have now varied the length of uORF2 using a different, unrelated donor sequence encoding the FLAG peptide and observe similar results (Fig. S4 in our manuscript) to our original experiment with the YFP-encoding sequence (Fig. 6B in our manuscript). A slight trend towards derepression with longer uORFs is observed in both cases. This effect might arise due to decreased stall strength caused by higher nascent peptide protrusion out of the exit tunnel leading to cotranslational folding (Bhushan et al., 2010; Nilsson et al., 2015; Wilson et al., 2016) or nascent chain factors (Gamerdinger et al., 2019; Weber et al., 2020) exerting a pulling force on the peptide. Importantly, we do not see the periodic change in repression predicted by the queueing model (Figure 6A, yellow-green lines).

Minor comments • Specific experimental issues that are easily addressable. 5) It is unclear how the luciferase assays were analyzed considering the background noise. If the NLuc expression is low, close to the background, then how to extract or normalize the background will influence the expression level, thus fold change for different reporter/condition.

To account for the luciferase background, we subtracted background from measured data values. To show that expression is rarely close to background (from mock transfections), we included a supplementary figure showing raw NLuc and FLuc values (Fig. S1B). Also note the response to Reviewer 1 regarding a no-start-codon control having a 20-fold lower signal than the WT UL4 uORF2 construct.

• Are prior studies referenced appropriately? yes • Are the text and figures clear and accurate? Mostly good • Do you have suggestions that would help the authors improve the presentation of their data and conclusions? Have a main figure about the modeling part.

As suggested by the Reviewer, we have now added visual representations of the reactions as a new main figure (Fig. 3). We also moved the modeling workflow figure from the supplementary set of figures to this main figure (Fig. 3). We thank the reviwer for this suggestion that greatly improves the presentation of our modeling methodology

• Place the work in the context of the existing literature (provide references, where appropriate). Recent years, there has been a lot of study about small open reading frames, while for uORFs are known to repress translation, the regulatory mechanism is not known yet, there are just different models not validated yet (Young & Wek, 2016). Also, under normal conditions and stress conditions, uORF can play both repressive and stimulative role in main ORF translation (Orr, Mona Wu, et al. NAR 48.3 (2020): 1029-1042.). This paper is the first study to put all the uORF working hypothesis with buffering effect together, they use modeling to explain how under each hypothesis, buffering may happen or not. >• State what audience might be interested in and influenced by the reported findings. It will be interesting to people, who study molecular biology, biochemistry for translation regulation, especially uORFs. The modeling people may also find it interesting, how they could adapt modelinbeew keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. I have extensive experience working in the translation regulation field and I feel extremely comfortable to discus all the experimental part including individual reporters as well as genome wide. But I do not consider an expert in the modelling section of this work.

Reviewer #3 :

Summary Small ORFs are prevalent in eukaryotic genomes with variety of functions. Recent technological advances enable their detection, yet our understanding on the mode of action remains quite rudimentary. The manuscript by Bottorff, Geballe and Subramaniam aims at elucidating the function of UL4 uORF in the CMV, and thus, it is on timely and topical research. The authors measure the uORF -controlled expression of the well-studies UL4 uORF and kinetically model the initiation behavior. Within a second uORF, a diproline pair controls initiation of the downstream main ORF sensing ribosomal collisions between a scanning small subunit and an 80S positioned at the canonical start of the main ORF. The stalling at both proline codons is envisioned as a kinetic window to sense any elongation-competent 80S at initiation and thus, control the ribosomal load and expression. Such diproline tandems are present in some uORFs in human transcriptome, hence representing more pervasive control mechanism. Significance I am unable to comment in depth on the modeling algorithms and simulations as this is outside of my expertise. The experiments are reasonably designed to test various models of uORF regulation and set the frame for the modelling. The idea that various stress factors would decrease canonical initiation and consequently would reflect the number of initiating ribosomes are adequately tested by varying the number of initiating ribosomes. The discovery of the two terminal prolines, that are also found in other human uORFs, is appealing mode of controlling stalling-driven downstream initiation. However, the lack of experimental support with the human uORFs may indicate additional contributions. This raises the question as to whether the proline codon identity plays a role? Since codons are read with different velocity which is mirrored by the tRNA concentration. It would be good to address whether special proline codons have been evolutionarily selected in CMV and whether the kinetics of stalling strongly depends on the codon identity. Are both prolines in the tandem using the same codon? Along that line, are the same proline codons used in the human diproline-containing counterparts? Consequently, the P to A mutation may have altered the codon usage and could be the reason for the nonlinear effect in the human sequenced. In this case, it would make sence to use Ala-codons with similar codon usage as the natural prolines?

We thank the Reviewer for raising this point about the role of codon usage. The tandem proline residues do not use the same codon (CCG then CCT). The two C-terminal proline residues in uORF2 are necessary for the elongating ribosome stall (Bhushan et al., 2010; Degnin et al., 1993; Wilson et al., 2016), but it has been previously shown that the identity of the codon does not significantly impact repression (Degnin et al., 1993). The human uORFs generally have 1 of the 2 Pro codons in common with the uORF2 Pro codons. Given that most of the human uORF P to A mutations behave similarly (Figure 7) irrespective of the original proline codon, we believe that codon usage does not impact repression by these uORFs. Moreover, as explained in response to Reviewer 1 and 2’s questions, we believe that the human uORFs containing terminal diprolines may partially repress translation via nascent peptide effects, but the majority of the repression likely arises from efficient siphoning of scanning ribosomes from the main ORF by the uORF (Fig. 1A in our manuscript).

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this paper, the authors are exploring the uORF regulatory mechanism. They first discussed five general models how uORFs might work to repress and buffering main ORF translation, then they mainly focus on the UL4 uORF2 for the potential mechanism. They use both computer modeling and experimental validation with reporter assay in 293t cell line. Based on their model, and few experimental results when they change the translation initiation rate and/or length of dORF, they propose it may work through 40S dissociation model, since the buffering effect is not uORF length sensitive.

Major comments:

• Are the key conclusions convincing?<br /> The modeling for different mechanisms is insightful, but some modeling parameters and experimental validation are not conclusive and validation of few of them can enforce the conclusions.
• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?<br /> Yes, the part about queuing and length sensitive is not convincing to me, it should be modified and reduce the statement strength.
• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.<br /> Yes, please see the major concerns
• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.<br /> They will need to re-think about the modeling, and validation in Figure 5, there are validation experiments that can be done in weeks and in a cost-efficient manner that can enforce the conclusions.
• Are the data and the methods presented in such a way that they can be reproduced?<br /> Most of them are good
• Are the experiments adequately replicated and statistical analysis adequate?<br /> Yes

I have some major concerns about the paper:

1. It is a bit confusing to me in Figure 2C, the reporter assays, that non-start codon reporter and non-stall reporter has same expression level. In theory, the non-stall reporter still has uORF there, so it should repress main ORF expression, and have lower expression level than the non-start reporter, where there is no uORF, no repression. In other uORFs they tested in Figure 6, the non-stall reporters are lower than non-start reporter. Since data they use to build the model is Figure 2B, and calculate the parameters for the whole paper, I just want to make sure it is making sense. I noticed there is another CTG in frame on the 4th codon, this may be alternative start codon in the non-start reporter to trigger some repression.
2. All the modeling and prediction the authors do are based on average, but we know translation is very heterogeneous. For each ribosome or each 40S, the kinetics varies a lot, the authors should discuss about this part.
3. For modeling related with the queuing-mediated model in Figure 1C. they use 30nt as the ribosome length to count the potential queuing to start codon. But 30nt is the 80S protected fragment with specific conformation. The protected fragment for 80S will change based on different status of ribosome conformation or elongation step. More importantly, for queuing, it is 40S, so they may have a different size. Based on previous 40S ribosome profiling (Archer, Stuart K., et al. Nature 535.7613 (2016): 570-574. And other papers), the length can vary from 19nt to very long, so I don't think the 30nt length can be used to model queuing in 40S and length sensitivity in the uORF working mechanism.
4. For Figure 5B, besides the modeling length part I have mentioned above, when the authors increase the length of uORF, the sequence is also changed, which may introduce other side effect. So, if the authors want to conclude about the queuing part, they should rethink about the length for both modeling and validation, plus control for the sequence they added to increase the length of uORF, for example use different sequence when manipulate the length.

Minor comments:

• Specific experimental issues that are easily addressable.<br /> It is unclear how the luciferase assays were analyzed considering the background noise. If the NLuc expression is low, close to the background, then how to extract or normalize the background will influence the expression level, thus fold change for different reporter/condition.
• Are prior studies referenced appropriately?<br /> yes
• Are the text and figures clear and accurate?<br /> Mostly good
• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?<br /> Have a main figure about the modeling part.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.<br /> It is an interesting area, using modeling with experiment validation to understand uORF regulation mechanism, the kinetics and interplay between different translation steps, it will help us to understand uORF buffering in stress conditions.<br /> Also bring modeling method with reporter validation to the translation field, will provide clues to the molecular mechanism study, especially in complex situation.
• Place the work in the context of the existing literature (provide references, where appropriate).<br /> Recent years, there has been a lot of study about small open reading frames, while for uORFs are known to repress translation, the regulatory mechanism is not known yet, there are just different models not validated yet (Young& Wek, 2016). Also, under normal conditions and stress conditions, uORF can play both repressive and stimulative role in main ORF translation (Orr, Mona Wu, et al. NAR 48.3 (2020): 1029-1042.). This paper is the first study to put all the uORF working hypothesis with buffering effect together, they use modeling to explain how under each hypothesis, buffering may happen or not.
• State what audience might be interested in and influenced by the reported findings.<br /> It will be interesting to people, who study molecular biology, biochemistry for translation regulation, especially uORFs. The modeling people may also find it interesting, how they could adapt modeling to complex biology process and contribute to the understanding.
• 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.<br /> I have extensive experience working in the translation regulation field and I feel extremely comfortable to discus all the experimental part including individual reporters as well as genome wide. But I do not consider an expert in the modelling section of this work.

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Reply to the reviewers

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We appreciate the efforts the two reviewers had invested in reviewing our manuscript. Their constructive comments will help improve the paper overall.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

Reviewer #1 (Evidence, reproducibility and clarity):

The main point of the current report is that 6mA is present in DNA of Hydractinia, and is introduced randomly into the genome by DNA polymerases, originating from degradation of maternally provided RNA via nucleotide salvage pathway. The authors observed that 6mA levels are changing over development and peak at 16-cell stage, with a sudden decrease to 'background levels' at 64 cell stage, a stage when zygotic genome gets activated. The 6mA drop is Alkbh1 dependent, since upon K/D of Alkbh1, 6mA levels were significantly higher than in control embryos. Authors also observed that AlkbH1 K/D delays zygotic genome activation (ZGA) to later stages, but without any noticeable consequences for the proper development. To demonstrate that 6mA is not controlled via direct DNA methylation, they show that K/D of two potential DNA methyl transferases N6amt1 and Mettl4 does not have any effect on 6mA levels. Supporting their hypothesis, authors demonstrate high activity and imperfect selectivity towards non-modified nucleotides of salvage pathway during embryo development using EU labeling experiments.<br /> In general, the provided data support their model, however, the paper needs some improvements to include missing information and controls before publication.

Major comments:<br /> 1. Fig 1A shows a schematic where D3-6mA is added to only QTRAP but not QQQ experiment, usually QQQ methods also require isotopic standards for each component quantified to normalize for ionization differences and provide true quantitative information. Why did authors not use dA isotope? The ionization suppression is more pronounced at high concentrations of the components, which is true for dA in the current set up. How do authors control or at least test this?

We have limited resources of isotopic-labelled standards. Therefore, we initially used QQQ without these standards to obtain data that covered many time points in development to identify the general pattern and key time points of high and low 6mA. Once the QQQ indicated that the 16-cell stage has the highest 6mA and that this drops to background at the 64-cell stage (and remains so later on), we performed QTRAP with the isotope-labeled standard control only for these two stages. Looking at the data resulting from both techniques, it appears that they essentially revealed the same pattern. Since the main focus of the study is on 16- and 64-cell embryos, we feel that the contribution of performing all stages by QTRAP would be marginal. We have performed control experiments to assess ionization suppression for dA and found that it was insignificant. We will add the corresponding data to the Materials and Methods section.

Fig S1 show that quantification works well, but were the total DNA amounts comparable to the gDNA amount used in actual samples? If yes, please indicate so.

Yes, the amounts were the same (2mg). We will change the methods sections accordingly.

1. In line 68 and in fig 1B, 1C there is a mysterious 'Neg. Ctrl 'sample. It is unclear what was the sample and more interestingly in fig 1B the levels in this sample are 0.015% but in fig 1C it is much below 0.001%. Why there is such a striking difference for the identical sample.

Negative controls were the same amounts (2 µg) of oligonucleotides without 6mA, DNAse-treated exactly like the samples. Figure 1B shows that QQQ is not sensitive enough to reliably detect 6mA concentrations below 0.02%, incapable to distinguish the background 6mA in the negative control from the level of 6mA in the 64-cell stage and later. Therefore, we utilized D3-6mA labelled QTRAP (Figure 1C) and determined that the level in the 64 cells stage embryos was actually ~0.01%. In the negative control, the amount was considerably lower, around 6 ppm (0.0006%).

1. As I can see authors measured natural isotopologue of 6mA, however traces of contaminant bacterial DNA originating even from recombinant DNA degradation enzymes also have 6mA, giving background signal. In their LC/MS experiments, did authors check if the 6mA comes truly from the gDNA and not from contaminant during DNA purification and processing before MS?

Yes, we did. As control for the level of 6mA contamination from the enzymatic digestion (sourced from bacteria), we also performed digestion of the negative control (see also answer to previous comment).

1. Fig 1D in the legend: authors should indicate that samples were already RNAse treated, and Line 80 in the text mentions a second RNase treatment (fig S1C) to confirm the specificity of the DNA staining.

The samples were indeed RNase-treated. We will modify the legend and the reference to figure 1D on line 80 accordingly.

1. In lines 86-87, authors compare the LC/MS and sequencing based quantifications, and say they are consistent. Can authors make a figure analogous to fig 1B but using sequencing data?

The data are already provided in Figure S1E. However, we used a Venn diagram to denote that these figures were generated by a different type of analysis (SMRT-sequencing as opposed to QTRAP). They are consistent but not identical.

1. Fig 3B and 3C, controls showing the validity of EU staining, are required, such as RNAse treated sample with a signals disappearing; or control embryos without EU, thus having only background signal.

Indeed, Fig 3C shows an RNase treated sample in which the EU signal is abolished as expected.

1. Fig 3D specificity control is missing, control embryos without EdU having only background signal.

The control is provided in Figure 3B. It shows a sample without EdU (treated with EU) and shows the background signal.

1. Fig 4A legend: 'rescue solution (see text)'. Please describe in the legend what the solution was. Moreover, I did not find clear explanation in the text either, my only guess was from the materials in methods section, where authors used both shAlkbh1 and Alkbh1 mRNA with silent mutations.

The reviewer is right, this was indeed the control that was used. We will modify the text to clarify this point.

1. Fig 4B shows many data points per condition and the legend says EU signals (in triplicate), was these triplicate animals with multiple cells, where EU signal from each cell was plotted as a point? Please specify in the legend.

Yes, triplicate embryos and each cell used as point. The legend will be adapted.

1. Lines 169-170 state 'the lack of premature ZGA following N6amt1/Mettl4 knockdown (Figure S7B) indicate a lack of methyl transferase that maintains 6mA through embryogenesis' while an experiment indeed demonstrates that these are not the major players in this process, it does not prove these are not DNA methyl transferases. The absence of evidence is not the evidence of absence. I think authors should at least soften this conclusion.

We agree and will tone down the relevant statement.

1. Discussion section describes many experimental data that belong to Results section.

This is a point also raised by Reviewer #2. We will move these points to the results and expand the discussion.

1. Fig S8 I think should be a part of the main figure since it is one of the important experiments to prove the high activity and somewhat low selectivity of salvage pathway in the embryos during the critical early stages.

We had originally left it out to save space. We prefer to leave this decision with the editor.

1. Fig 5C the model is confusing, authors should improve it.

It is difficult to describe a complex story using a single static model. Therefore, we will add an animation to the supplemental material to clarify the model.

1. Fig S8 negative controls showing the specificity of CuAAC staining are missing: control animals/ embryos without EU.

We will redo these experiments and include appropriate controls.

1. Authors may find this reference useful: PMID: 32355286.

We will add this ref.

1. It is known that in mammals ADAL protein is the one which demethylates m6A nucleotide to clear it from the nucleotide pools and prevent it entering into the salvage pathway (PMID: 29884623). Does Hydractinia Symbiolongicarpus have an ADAL analog? If yes then it would be important to see if knock down/overexpression of this enzyme has any effect on the timing of ZGA. In principle, passively introduced 6mA may be regulatory to proper time the ZGA, and is controlled via an activity of Adal and Alkbh1.

The gene is present in the Hydractinia genome. We could perform the experiments recommended. We will knock the gene down and look at the effect of this manipulation on ZGA.

1. Material and methods are missing information:<br /> a. Line 370-371 provide references to the protocols listed or describe the steps.<br /> b. Line 373 standard column based purification protocol, what is it either explain or provide a reference.

References will be provided.

Minor points:<br /> Line 79 : 'Fig 1D and S1B', Did authors meant 'Fig1D and S1C'?<br /> Fig 5A Y axis title is missing.<br /> Line 379: 3D1-6mA should be D3-6mA please correct the other appearances as well.<br /> Line 405: terms : dsDNA solutions and standard solutions are confusing please rephrase.<br /> Line 410: Cleaned embryos, what does cleaned mean, be specific.<br /> Line 413: PTx is mentioned, please explain what is it.<br /> Line 415 and line 440 : HCl was washed and embryos were neutralized, I guess it should state : HCl was neutralized and embryos were washed with...'<br /> Line 431: ' before fixed by incubation in PAGA-T..." did authors meant : 'before fixation with PAGA-T...?<br /> Line 435: Permeabilization was done by further washes the fixed embryos with...", did authors meant: Permeabilization was done by an additional wash of the fixed embryos with...?<br /> Line 440: The HCL was washed with what solution?<br /> Line 446: For how long were the PTx washes?<br /> Lines 458-460: the sentence is confusing.<br /> Line 500: 'then used detect' should be 'then used to detect'

We will adopt all minor points above.

Reviewer #1 (Significance):

There are many high profile papers describing the existence of 6mA in gDNA of different organism including insects and mammals. However, there is no proof that it has any biological function. Indeed, recent reports (PMID: 32355286 and 32203414) indicate that in mammalian cells, 6mA is indeed primarily incorporated by DNA polymerases and originates from a salvage pathway. The present report is the first in vivo evidence that confirms this to be the case more generally and, importantly, demonstrates a 6mA effect on ZGA. Hence, this is an important and timely report, which will be interesting to the field, as well as a broad audience to clarify the role of 6mA and the mechanism whereby it is introduced into gDNA.<br /> My expertise: Biochemistry and biology of DNA and RNA modifications, including 6mA. Fair expertise: bioinformatics analysis.

Reviewer #2 (Evidence, reproducibility and clarity):

The manuscript reports developmental dynamics of DNA 6mA in the cnidarian Hydractinia symbiolongicarpus. The authors describe an event of a seemingly random accumulation of this DNA modification in 16-cell stage embryos of Hydractinia symbiolongicarpus followed by an apparent clearance of 6mA by the 64-cell stage. Interestingly, the depletion of cnidarian orthologue of the putative 6mA 'demethylase', Alkbh1, results in delay in zygotic transcription accompanied by high levels of DNA 6mA in 64-cell stage cnidarian embryos. The authors suggest that the 6mA they observe originates from random misincorporation of recycled degraded m6A-marked ribo-nucleotides during early cnidarian embryogenesis.<br /> Overall, most of the experiments are performed at high technical level and the paper is generally nicely written. Despite this, in my opinion, the manuscript would benefit from incorporation of several addition controls and answering a number of points on the description/presenation of the data.<br /> Major comments:

1. In the present version of the manuscript, the authors demonstrate the negative correlation between the presence of 6mA in the genome of cnidarian embryos and transcription. Although, the depletion of Alkbh1 leads to the delay in ZGA, strictly speaking, this effect may be independent of the catalytic function of Alkbh1. Therefore, to make a statement that m6A "random incorporation into the early embryonic genome inhibits transcription" the authors should use a catalytically inactive form of this enzyme as a control in the corresponding experiments and/or (ideally) perform in vitro transcription assays using 6mA-containing substrates.

We could perform shRNA-mediated Alkbh1 KD and try rescue ZGA by co-injecting a catalytically-inactive Alkbh1 mRNA.

The suggested in vitro experiment would be inconclusive for two reasons: first, Hydractinia polymerase may respond differently to 6mA; second, 6mA-mediated transcription inhibition could be indirect, requiring the in vivo context. We would like to add that transcription inhibition of 6mA has been demonstrated in vitro using yeast DNA polymerase as cited in the paper.

1. Despite several experiments suggesting that random incorporation of recycled ribonucleotides occurs in cnidarian embryos, the source of 6mA in their DNA seems currently unclear. Would it be possible to directly test the author's hypothesis by comparing the levels of 6mA upon maternal (and possibly zygotic) depletion of the cnidarian orthologue of RNA m6A methyltransferase Mettl3 in cnidarian embryos? Alternatively, the authors could incubate the embryos in medium supplemented with labeled ribo-m6A followed by checking the levels of DNA 6mA in the embryonic DNA?

We show that maternal mRNAs are already methylated in the early embryo (Figure 5). Therefore, it would indeed make sense to ablate Mettl3 from the maternal tissue while maternal mRNAs are methylated. However, in the absence of a conditional knockout technique in Hydractinia, this would require generation of CRISPR-Cas9 mutants that would likely die early in their development, long before reaching sexual maturity.

Instead, we are happy to perform the other experiment suggested by the reviewer to directly demonstrate m6A to 6mA transition.

Minor comments:<br /> 1. It would be nice to complement Fig. 4, 5, and S7 with immunostaining of the corresponding embryos for 6mA.

6mA immunostaning is not compatible with EU labeling because, first, they require different types of fixation (PAGA-T vs formaldehyde); second, immunostaining requires RNase treatment to remove m6A which would also remove the EU signal.

1. The current Discussion contains references for several figures with experimental results. I suggest separating these experimental data from the Discussion. The authors should, in my opinion, make an additional Results chapter and, if possible, expand the Discussion section (that is currently minimal) speculating on significance of their results for different biological systems.

This has also been requested by Reviewer #1. We will follow the reviewer's recommendation.

1. The present Title reads like a clear overstatement (at least currently, please see major comments above). The Title should also reference the organism where the observations have been made.

Following the revision, we believe that both random incorporation of 6mA and a delay in zygotic transcription will be well supported by our data. We will add the organism's name to the title as suggested.

Reviewer #2 (Significance):

The presence and significance of DNA 6mA in animal genomes is a very interesting and highly controversial topic. Although a number of studies suggest that relatively high levels of this DNA modification occur in multicellular eukaryotes in different biological/functional contexts, other reports challenged these observations attributing them to different experimental artifacts. In this context, the current paper that provides high quality novel experimental data on the developmental dynamics of DNA 6mA in cnidarian is extremely interesting and timely. Moreover, the author's results and the hypotheses on the function/origin of 6mA in cnidarian embryogenesis may provide a conceptual framework for the interpretation of other 6mA/m6A-related studies performed on different experimental models. Thus, this manuscript will definitely be of interest for a wide range of researchers working in the fields of epigenetics, cancer biology and developmental biology.<br /> I strongly believe that this is an interesting and important study that definitely deserves to be published in a high impact journal.

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

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

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

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

Reviewer #2 suggested four experiments, three of which are either impossible in our system or expected to reveal insignificant information. First, the reviewer suggests ablating Mettl3 from the maternal tissue. While being a good idea in principle, there is no conditional ablation technique available for Hydractinia. Generating CRISPR-Cas9 mutants would likely result in embryonic lethality, long before sexual maturation has been reached.

Second, the reviewer proposed to perform in vitro experiments with m6A-containing substrates. These experiments are unlikely to reveal useful data since the Hydractinia polymerase may respond differently to methylated adenine than commercially available polymerases. Also, transcription inhibition may be indirect, depending on the in vivo context that cannot be mimicked in vitro.

Finally, the reviewer suggested expressing a catalytically-dead Alkbh1 in the background of endogenous Alkbh1 knockdown to demonstrate that its function depends on the enzymatic activity to remove 6mA from the genome. While we could perform the experiment (see our reply above), the information emanating from it would arguably be outside the scope of this study.

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

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Reply to the reviewers

1. General Statements [optional]

The newly identified azyx-1 ORF was named peu-1 in the initial submission of this manuscript, a name that was under consideration with WormBase, who supervise nomenclature of C. elegans genes. In consultation with WormBase, the locus was named azyx-1 instead (the final decision being “azyx-1 will be attributed to F42G4.11. It will be released in WS287 at the beginning of 2023”). We updated this nomenclature in our submission files, including in reviewer comments pasted below. Please note that other than this, no changes whatsoever were made to the reviewer comments.

2. Description of the planned revisions

REV #3: Specific thoughts for consideration:

Figure 5, Moderate is really minor/moderate with other metrics, and severe is definitely moderate with other metrics. Thus, I'm not sure if normal vs. moderate is needed. This really is a minor point as it doesn't impact results/overall story/importance.

This was also pointed out by reviewer #1. We will rename classification more mildly so.

REV #1 Fig. 5 Even the 'severe' muscle disruption is quite mild (say, in comparison to loss of talin). Perhaps rephrase these categories? The moderate and severe categories also do not look different to me. Show what the muscle cells look like in zyx-1 deletion and overexpression animals. Is there a way to use quantitative imaging to score these? Can azyx-1 phenotypes be rescued or enhanced by expression (or RNAi) of zyxin in the muscle? Also, clarify what age animals are being tested in the muscle and burrowing assay.

We agree and will rename the classes in milder terms. Qualitative scoring (which was done blinded) is the standard in the field as was done according to Dhondt et al. (2021 Dis Model Mech). When tested for muscle integrity and burrowing capacity, animals were day 1 adults. This is mentioned in the Methods section of the current manuscript and will also be included in the captions of the revised figures.

REV #2: I am not convinced by the data presented in Figure 5. There does not seem to be much to distinguish the five genotypes, but I concede that I am not used to looking at this type of data. But why was the muscle phenotype not also examined in the azyx-1 rescue lines?

Because other reviewers that are familiar with these data point out that the observed differences of panels A-B are indeed milder that what is usually seen, we will rename classifications in the manuscript (see responses above). Because the azyx-1 deletion mutant does not differ from controls in the muscle phenotype, there is no phenotype to rescue for this readout, and no rescue strains were generated.

We are not sure what the reviewer may struggle with in (assumedly) panel C (~‘to distinguish the five genotypes’). The positive control (zyx-1) behaves as expected in the burrowing assay, with our own mutants within that range, also as expected. All data were scored blinded to avoid any bias and statistical analysis supports the interpretations, all granting confidence to the observed differences. However, because reviewer#3 also would prefer another representation of the data shown in this panel (see below), we will provide an updated panel representation in the revised manuscript.

REV #3: Figure 5C- Hard to read. Would displaying lines/tragectories make it easier to understand? Would displaying as violin plots for each timepoint/condition make it easier to visualize? Basically in black and white and in color this is hard to visually process.

We will work on another representation for the revised manuscript, since reviewer2 also seemed to struggle with this panel representation.

REV #1: Fig. S2 Match font sizes on Y-axes. Also, indicate any statistical differences and statistics used.

Figure adjustments will be implemented in the revised manuscript as requested.

REV#1: Fig. S3 C, indicate any statistical differences and statistics used.

Figure adjustments will be implemented in the revised manuscript as requested.

REV #2: I am not convinced by the "overexpression" experiments. These are not well controlled, since no evidence is presented that AZYX-1 is being overexpressed in these lines. Also, since we know that extrachromosomal transgenic lines are highly variable, one would need to test the effect of several independent lines to ensure that the effects that the authors observe are indeed associated with AZYX-1 overexpression and not simply an idiosyncratic effect of the genetic background of a given strain. Finally, there does not seem to be an obvious mechanism by which overexpression of AZYX-1 can impact ZYX-1 function. That doesn't rule out an effect, but based on the data as it is, it is premature to propose such a mechanism. The authors need to show that multiple overexpression lines do reproducibly overexpress AZYX-1 and that this results in reproducible effects of zyx-1 phenotypes.

The extrachromosomal strains are indeed variable, but because the background is wild type (in contrast to a deletion mutant background for rescue strains), an overdose of the target provided is expected. As requested in the cross-consultation reviewer communication, we will include quantitative data in our revised manuscript that shows that the used strains (LSC1950, LSC1960, LSC2000) indeed are overexpressors.

REV #2: The data presented in Figure 4F needs to be quantified using the same format as was presented in Figure 4B.

Due to the different genetic background of the strains, this is not possible in the exact same way (the red signal of LSC1998 & LSC1999 is not unique to zyxin). We understand that in essence, the reviewer would like us to include a more quantitative representation of these data, and will update the figure accordingly.

REV #2: What is the difference between the overexpression transgenic lines and the "rescuing" transgenic lines? In the Materials and Methods, the same concentration of plasmid was used in injections - so these likely give the same approximate level of transgenic expression.

The genetic background: a rescue line adds wt DNA back to a mutant background, while in an OE strain it is added into a wt background. While this can already be derived from the genotype details in Supplemental Table S1, we apologize for not specifying this in the methods section, as it is common practice in the field. These specifications will be added to the revised manuscript.

REV #2: I am not clear what features are being used to characterise the myofibril structures into the three categories. Can the authors annotate the images to indicate the diagnostic features?

The reviewer is correct that manual classification is rather poorly defined in general, which is why it is scored blinded (here as per Cothren et al., 2018 Bio Protoc). We adhered to the reference images by Dhondt et al. (2021, Dis Mod Mech) with visual assessment based on how tightly organized (~parallel) myofilaments are organized, assessing overall increases of bends or breaks in individual myofibers as leading to a less aligned pattern (cf. Fig. 1 of Dhondt et al.). We will add this information more explicitly to the Methods section of the revised manuscript.

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

REV #1: Fig. 4 would be better if the control (A) and azyx-1OE (B) worms were more similar in age and size

The panels of this figure were not to the exact same scale, we apologize if the reviewer found this confusing. We have rescaled the panels so that this is less confusing. The animals are all day 1 adults.

REV #1: Abstract: Clarify what is meant by 'putative syntenic conservation' or rephrase, simply stating that the existence of an ORF overlapping with the 5' region of zyxin is conserved

This has been rephrased according to request.

REV #1: Line 24: Clarify these are synthetic phenotypes (not caused by loss of zyx-1/azyx-1 alone). Loss of zyx-1 alone results in very mild phenotypes.

While the original sentence already pointed this out, we rephrased the text to make clear that these observations require the dystrophic mutant background.

REV #1: Line 28: Start new paragraph

The new paragraph was started a sentence earlier, according to rev#2 request.

REV #1: Line 31: Not clear what is meant by 'post-transcriptional regulation can be further propagated'- maybe reword to 'alternative and overlapping open reading frames (ORFs) arising from polycistronic mRNA can regulate translation' or something simpler like that.

This has been rephrased according to request.

REV #1: Line 56-57: Is this because most C. elegans transcripts start with the splice leader SL1 or SL2 rather than the adjacent 5' sequence? Is that relevant for zyx-1? Recommend commenting briefly on this.

We did not look into this for all possible u(o)ORFs in C. elegans, which also is not the focus of the manuscript, so we cannot make general statements. As part of the annotation procedure of azyx‑1, WormBase verified that indeed several pieces of evidence, including available phyloCSF data for exon 1, SL1s, RNASeq and Nanopore data, all support its annotation, as well as its translation from the zyx-1 long transcripts (albeit with different start and in different reading frame).

REV #1: Line 78: Delete the word 'other'

Done

REV #1: Line 122: zyx-1

Done

REV #1: Line 137: 'lead' should be 'led'

Done

REV #1: Line 158: rephrase 'only the long ones' to indicate which isoforms more precisely

Done (these are a/e, cf. Luo et al. 2014, Development)

REV #1: Line 195: Rephrase. Unclear what is meant by 'highlights the evasiveness of non-canonical ORFs from functional annotation'

Done; this was rephrased to “This exemplifies how non-canonical ORFs can escape functional annotation, …”.

REV #1: Various locations: I think it will be more clear to the reader to consistently refer to the burrowing assay as 'burrowing assay' rather than chemotaxis. I recommend adding a brief description of the burrowing assay to the results section.

Wording has been updated, we can provide a short context sentence to the results section of the revised manuscript.

REV #2: I'm not sure how to interpret the significance of the u/ouORFs across short and large phylogenetic distances. One would presume that there might not be primary amino acid conservation if the regulation simply takes by interference with ribosome scanning and translocation. Here some statistical analysis would help with assessing the significance of these observations. How unusual is it to find u/uoORFs in the 5' UTRs of gene encoding zyxin family members versus in general for the species analysed?

This is indeed the very question we are asking in the manuscript, and there is a clear reason why we refrain from making significance statements. At the moment, all relevant available metadata are used for the analysis in the manuscript, leading to the communication of the synteny-related findings as they are currently presented. This is due to the dependency on translatomics data to find credible u(o)ORFs, and there aren’t very many translatomics datasets available, only for a limited set of species so far. Our manuscript contains all relevant OpenProt data, which are derived from only 9 animal species so far. As shown in Table S4, 14 zyxin orthologs belonging to 7 species have associated u(o)ORFS, for two species only overlapping ORFs are present in the database. While more and more datasets will undoubtedly become available in the next years, the findings in the manuscript are as complete as currently possible: we do find evidence of u(o)ORFs associated with zyxin orthologs in these species, some of which are evolutionarily distantly related to C. elegans.

REV #2: The authors state that there is evidence for synteny and coding region conservation. The data supporting this assertion is not well presented. Presentation and analysis of multiple sequence alignments of the putative homologues involved would strengthen the assertion of synteny considerably.

We apologize if the reviewer misunderstood: we discuss likely syntenic conservation, not coding region conservation. The latter is not mentioned in our manuscript, and in fact not convincing indeed. This is not surprising given the bigger sequence diversity observed at the N terminus of zyxins and the partial overlap of these coding sequences, and in line with observations of several others in the RiboSeq community that many identified uORFs are conserved between orthologous genes, but poorly conserved at the amino acid level (e.g. community-driven communication by Mudge et al., BioRxiv 2021 and references therein).

REV #2: The authors are oddly coy about the molecular details of the 27 bp deletion used to study the loss of azyx-1 function. In the absence of these details, it is not possible to assess the validity of these experiments. We need to be given the full molecular details of the allele - precisely which nucleotides are deleted? And how do they affect the coding regions of zyx-1 and azyx-1?

I am also confused about why the authors made a deletion allele rather than mutating the AUG of AZYX-1? This would be a cleaner experiment to interpret. Based on the data presented, there are two possible interpretations in addition to the one suggested by the authors: 1) the 27 bp deletion impacts zyx-1 expression due to its impact on the zyx-1 coding region (the coding regions of azyx-1 and zyx-1 overlap); 2) the deletion mutation deletes critical transcriptional control elements. A simpler mutation of the azyx-1 AUG via CRISPR might allow them to rule out the possibility that they have simply compromised a transcriptional control element or damaged the coding region of ZYX-1.

As mentioned above and as will be included more clearly so in the revised manuscript: the deletion is 182-155bp (27bp) upstream of the zyx-1a start site. This was a mutant that could easily be generated via CRISPR, so we proceeded with this one. This edit rules out option1 (there is no change of the zyxin coding region), but (as also considered but addressed differently in the manuscript; see below) retains alternative interpretation 2. There are no regulatory regions or transcription factor binding sites known for the (a)zyx-1 locus (verified in current WormBase version WS285), but that does certainly not fully rule out the possibility either. Rather than creating a series of azyx-1 mutants, be they SNP or small deletion mutants, that would suffer from the exact same duality in possible interpretation, we chose to combine the deletion mutant with rescue and overexpression strains. Because these latter strains do not affect the endogenous zyxin regulatory region, they add far more credibility to the interpretation, than alternative mutants in the azyx-1/zyx-1 locus would.

REV#2. The narrative flow of the introduction could be improved by the judicious use of paragraphs. Line 12, for instance is a clear paragraph break, as is line 24.

Done

REV #3: Specific thoughts for consideration:<br /> 3) Could more be said about overlapping genes/regulation in humans? Again, not critical but this is such a great piece of work that it would be useful to guide human subjects researchers as to how to best further your work.

It is unclear whether the reviewer would like to see an extended introduction and/or discussion. We tried to meet this request without drifting too much from the focus of our current communication by adding the following to the introduction (lines 41-47 of the current draft): “From a more human-centred future perspective, uORFs are a rather unexplored niche for translational research: with a predicted prevalence in over 50% of human genes and first examples regulating translation of disease-associated genes already emerging (Lee et al. 2021; Schulz et al. 2018), the field is bound to not only lead to more fundamental, but also application-oriented insights. Keeping this broader context in mind, we here focus on more fundamental principles of uORFs in a model organism context.”.

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

REV#1: Does azyx-1 have zyx-1-independent functions or other regulatory targets?

This is an interesting question that is not yet addressed. While this is possible, it is beyond the scope of our current communication. Since the reviewer does not request anything concrete, we would prefer to leave this for follow-up research. While this notion is included in the manuscript, we are happy to more explicitly address this question in the discussion as well.

REV#1: Do the burrowing assay results reflect a neuronal or a muscle function for AZYX-1? Or both?

Our manuscript indeed does not yet delve into tissue-specific actions of this newly discovered ORF. While interesting, and in line with reviewer #3’s remark, this would be valuable for follow-up research, but is beyond the scope of our current communication. We will make sure the concept is clearly mentioned in the discussion of our findings.

REV #3: Specific thoughts for consideration:

Could more be done/said about neruo vs, muscular effects of azyx-1 and zyx-1. I appreciate this is beyond the scope of the present manuscript and therefore does not require response if you don't have data or it makes telling the story you want to tell more difficult.

We agree with the reviewer that spatially resolving some of these observations would be a next interesting step, which indeed is beyond the scope of our current communication.

REV#1: Fig. 2A very faint, increase brightness/contrast?

We did not adjust brightness or contrast for any of the figures, an no such requests were made by other reviewers. We greatly prefer presenting the data as unedited as possible, and would like to request the journal’s preference for action here.

5. Remaining reviewer comments & responses not highlighted above

CROSS-CONSULTATION COMMENTS<br /> _The following is a conversation among the three referees:<br /> _REFEREE #2: I appear to be the dissenting voice in terms of concern about the details of the 27 bp deletion and the "overexpression" constructs. I would be interested to know your opinions regarding my comments on these issues.<br /> REFEREE #1: I think adding the details of the 27 bp deletion is a reasonable request. It is probably not possible to disambiguate entirely the two effects of the deletion, and changing the start codon may result in an alternate start with other downstream effects. I think just explaining it more fully in the methods would satisfy my concerns.<br /> REFEREE #2: What about the issues with the overexpresssion? In my experience, presence of multicopy transgenes on an extrachromosomal arrays might not lead to over expression of the gene involved? This needs to be verified in some way.<br /> REFEREE #1: You are right about that. If the construct is tagged in some way they could try a western. I would recommend they integrate the transgenes, or just show results from several lines as you suggest.<br /> REFEREE #3: I agree the 27 bp deletion and over expression are reasonable technical issues. However, I view this a techical details vs. critical details for the novel regulatory mechanism. The point about ability to judge conservation is also reasonable but until the theory is firmly out there it is hard to test the conservation and broader applicability to other genes/proteins. Thus, while asking for additional information on these issues is reasonable I do not see the inability to address beyond highlighting as limitation in the text as critical to the overall validity of the work.<br /> REFEREE #2: I disagree with Reviewer #3, without knowing the details of 27 bp deletion the most reasonable interpretation of the data is simply that it is a loss-of-function allele of zyx-1. This goes beyond "technical" - at present there is no unequivocal evidence that azyx-1 has any functional significance beyond that it is expressed as a peptide.<br /> REFEREE #3: I've been back through the manuscript. They have sequenced the deletion and therefore should be able to provide that information to satisfy the issue(s). For the over expression, short of silencing my experience is that they do over express and when you have multiple lines some express more than others (and some silence more than others). If you want evidence that the peptide is over expressed ask them to quantify via mass spec if it isn't tagged and they can't do a Western. Clearly they have work leading expertise in quantitative mass spec proteomics in C. elegans and should be able to do that. Generally speaking, rescue of a deletion is a pretty good sign that the expression is working though (and is an accepted standard).

We apologize if this was not clear from the manuscript, and will clearly include the details in the Methods section: the deletion is 182-155bp (27bp) upstream of the zyx-1a start site, at AT|G+26|TTC. This was confirmed by sequencing; the oligos used for this are listed in table S3 of the manuscript. We address the confusion of rescue and overexpression above, in response to reviewer #2 (who echoes this confusion here).

Reviewer #1 (Evidence, reproducibility and clarity):

**This is a very interesting paper about a gene regulatory mechanism in a type of poly-cistronic mRNA in which alternate starts/open reading frames lead to production of two different proteins from the same locus. AZYX-1 is a predicted 166 aa protein, translated from the 5'UTR of zyx-1. Two isoforms are expressed from the 5' UTR and coding region of zyx-1. The presence of overlapping transcripts with zyxin orthologs appears to be conserved in other animals. The authors provide spectroscopic evidence AZYX-1 is indeed translated, and show AZYX-1 can regulate zyx-1 expression. Intriguingly, it seems azyx-1 inhibits zyx-1 expression in cis (deletion of azyx-1 increases ZYX-1 peptides), but AZYX-1 promotes zyx-1 expression in trans (overexpression of AZYX-1 increases ZYX-1 expression).

Reviewer #1 (Significance):

Nature and significance of the advance: This is a very interesting paper about a gene regulatory mechanism in a type of poly-cistronic mRNA encoding azyx-1 and zyx-1. Intriguingly, it seems azyx-1 inhibits zyx-1 expression in cis (deletion of azyx-1 increases ZYX-1 peptides), but AZYX-1 promotes zyx-1 expression in trans (overexpression of AZYX-1 increases ZYX-1 expression).

Compare to existing published knowledge: This is the first study of its type on zyx-1.

Audience: Those interested in gene regulatory mechanisms and in zyxin.

My expertise: C. elegans cytoskeleton, cell migration, acto-myosin contractility.

Reviewer #2 (Evidence, reproducibility and clarity):

**Summary:<br /> The authors build on previous work defining upstream and upstream-overlapping open reading frames (uORF and uoORFs, respectively) by focussing on a specific locus azyx-1, which the authors propose influences the expression of the gene encoding the sole zyxin family in C. elegans, zyx-1. They present evidence suggestive of u/uoORFs being a common feature of zyxin family genes in other animals, hinting that perhaps this is a conserved mechanism of gene expression regulation for these genes. In which case, studies in C. elegans would be valuable to elucidate the mechanism involved.<br /> Using a fluorescent reporter strategy, they show that azyx-1 is expressed in the same tissues as zyx-1, which is to be expected since their share the same transcriptional control elements.<br /> They also characterise the peptide steady state levels of both ZYX-1 and AZYX-1 isoforms, suggesting that while overall ZYX-1 levels decline with age, those for AZYX-1 are generally maintained. The significance of these observations was not immediately obvious to me - a priori it is difficult to assess what relative wild type steady-state levels one might expect if AZYX-1 translation impacted ZYX-1 expression.<br /> The authors propose that expression of AZYX-1 leads to inhibition of ZYX-1 translation through the standard model by which u/uoORFs impact translation of downstream ORFs. To test this, they generated a 27 bp deletion "at the beginning of the azyx-1 ORF". This deletion clearly correlated with a reduction in ZYX-1 expression.<br /> Finally, the authors generated lines designed to overexpress AZYX-1, testing the hypothesis that AZYX-1 might influence ZYX-1 in trans. Though here, it is not obvious by what mechanism this might operate, and the effect-sizes involved are modest.

Reviewer #2 (Significance):

The authors propose an interesting interaction between an important regulator of cellular behaviour (zyxin) and the u/uoORF that potentially regulates its expression - if validated by further experimentation, this would add to the growing evidence for the importance of the 5' UTR as a source of gene regulatory activity. Such regulation is well described in yeast, but there are fewer examples in animals, particularly in genetically tractable systems such as C. elegans. The work would primarily be of interest to researchers interested in understanding the spectrum of such activity in C. elegans. My own area of expertise, RNA-splicing and the post-transcriptional regulation of C. elegans gene expression, is not directly related to the research presented in the manuscript, but I am familiar with the general concepts and developments involved.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:<br /> The authors find that azyx-1 is a non-cononical gene with overlapping genomic localization to the gene zyx-1 in C. elegans. The authors also find preliminary evidence that similar genes with overlapping localization to zyxin genes exist in other species. The authors provide evidence for the tissue specific distribution of azyx-1 expression. The authors further provide evidence for azyx-1 and zyx-1 expression with age. Importantly, these data demonstrate differences in azyx-1 and zyx-1 protein products biological importance/relevance as they display differences with age. The authors provide evidence that azyx-1 expression influences zyx-1 expression in multiple ways. Lastly, the authors demonstrate that azyx-1 expression influences muscle structure and neuromuscular function. The authors use a combination of bioinformatic, protein biochemistry, genetic/transgenic, histologic, and physiologic methods to make these points. With regards to methods, the range/breadth is impressive and appropriate. In many ways the manuscript it is a tour de force in modern molecular biology with a focus on translational medicine. With regards to species, the in vivo experiments are solely C. elegans but the computational data include Fly, Bull, and Mouse.

The key conclusions are convincing. There are no major claims that require qualification as preliminary or speculative. No additional experiments are essential to support the claims of the paper. The data and methods are presented in such a way that they can be reproduced. The experiments are adequately replicated and the statistical analysis is adequate.

Prior studies are references appropriately. The text and figures are mostly clear and accurate.

We would like to thank the reviewer for their appreciation of our efforts and research approach.

Reviewer #3 (Significance):

**Conceptually this is a massive/ground breaking piece of work. Essentially, the authors are demonstrating a novel mechanism of regulation of gene/protein expression that, really, hasn't been reported before. What is particularly notable is that it appears, unsurprisingly, as correctly stated by the authors, to be evolutionarily conserved and not well reported in the literature. As with many classical molecular biology papers, and the more recent (e.g. RNAi, lncRNA) genetic papers, this manuscript hold the promise of transforming biology/medicine. The range of methods employed and the linking of molecular biology to pathophysiology was impressive. The audience that will be interested in this work includes: geneticists, proteomics researchers, evolutionary researchers, molecular biologists, physiologists, ageing researchers, muscle researchers, and muscle disease researchers. Thus, the interested audience is broad. My field of expertise with regards to this manuscript is: C. elegans, Mass Spec, Proteomics, genomic regulation, genetics, transgenics, histology, muscle, and physiology. There are no parts of this manuscript that I do not feel I have insufficient expertise to evaluate. I congratulate the authors on a highly significant, cross disciplinary, manuscript, that should impact multiple sub-areas of biology.

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

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors build on previous work defining upstream and upstream-overlapping open reading frames (uORF and uoORFs, respectively) by focussing on a specific locus peu-1, which the authors propose influences the expression of the gene encoding the sole zyxin family in C. elegans, zyx-1. They present evidence suggestive of u/uoORFs being a common feature of zyxin family genes in other animals, hinting that perhaps this is a conserved mechanism of gene expression regulation for these genes. In which case, studies in C. elegans would be valuable to elucidate the mechanism involved.<br /> Using a fluorescent reporter strategy, they show that peu-1 is expressed in the same tissues as zyx-1, which is to be expected since their share the same transcriptional control elements.<br /> They also characterise the peptide steady state levels of both ZYX-1 and PEU-1 isoforms, suggesting that while overall ZYX-1 levels decline with age, those for PEU-1 are generally maintained. The significance of these observations was not immediately obvious to me - a priori it is difficult to assess what relative wild type steady-state levels one might expect if PEU-1 translation impacted ZYX-1 expression.<br /> The authors propose that expression of PEU-1 leads to inhibition of ZYX-1 translation through the standard model by which u/uoORFs impact translation of downstream ORFs. To test this, they generated a 27 bp deletion "at the beginning of the peu-1 ORF". This deletion clearly correlated with a reduction in ZYX-1 expression.<br /> Finally, the authors generated lines designed to overexpress PEU-1, testing the hypothesis that PEU-1 might influence ZYX-1 in trans. Though here, it is not obvious by what mechanism this might operate, and the effect-sizes involved are modest.

Major comments:

1. I'm not sure how to interpret the significance of the u/ouORFs across short and large phylogenetic distances. One would presume that there might not be primary amino acid conservation if the regulation simply takes by interference with ribosome scanning and translocation. Here some statistical analysis would help with assessing the significance of these observations. How unusual is it to find u/uoORFs in the 5' UTRs of gene encoding zyxin family members versus in general for the species analysed?
2. The authors state that there is evidence for synteny and coding region conservation. The data supporting this assertion is not well presented. Presentation and analysis of multiple sequence alignments of the putative homologues involved would strengthen the assertion of synteny considerably.
3. The authors are oddly coy about the molecular details of the 27 bp deletion used to study the loss of peu-1 function. In the absence of these details, it is not possible to assess the validity of these experiments. We need to be given the full molecular details of the allele - precisely which nucleotides are deleted? And how do they affect the coding regions of zyx-1 and peu-1?<br /> I am also confused about why the authors made a deletion allele rather than mutating the AUG of PEU-1? This would be a cleaner experiment to interpret. Based on the data presented, there are two possible interpretations in addition to the one suggested by the authors: 1) the 27 bp deletion impacts zyx-1 expression due to its impact on the zyx-1 coding region (the coding regions of peu-1 and zyx-1 overlap); 2) the deletion mutation deletes critical transcriptional control elements. A simpler mutation of the peu-1 AUG via CRISPR might allow them to rule out the possibility that they have simply compromised a transcriptional control element or damaged the coding region of ZYX-1.
4. I am not convinced by the "overexpression" experiments. These are not well controlled, since no evidence is presented that PEU-1 is being overexpressed in these lines. Also, since we know that extrachromosomal transgenic lines are highly variable, one would need to test the effect of several independent lines to ensure that the effects that the authors observe are indeed associated with PEU-1 overexpression and not simply an idiosyncratic effect of the genetic background of a given strain. Finally, there does not seem to be an obvious mechanism by which overexpression of PEU-1 can impact ZYX-1 function. That doesn't rule out an effect, but based on the data as it is, it is premature to propose such a mechanism. The authors need to show that multiple overexpression lines do reproducibly overexpress PEU-1 and that this results in reproducible effects of zyx-1 phenotypes.
5. I am not convinced by the data presented in Figure 5. There does not seem to be much to distinguish the five genotypes, but I concede that I am not used to looking at this type of data. But why was the muscle phenotype not also examined in the peu-1 rescue lines?

Minor comments:

1. The narrative flow of the introduction could be improved by the judicious use of paragraphs. Line 12, for instance is a clear paragraph break, as is line 24.
2. The data presented in Figure 4F needs to be quantified using the same format as was presented in Figure 4B.
3. I am not clear what features are being used to characterise the myofibril structures into the three categories. Can the authors annotate the images to indicate the diagnostic features?
4. What is the difference between the overexpression transgenic lines and the "rescuing" transgenic lines? In the Materials and Methods, the same concentration of plasmid was used in injections - so these likely give the same approximate level of transgenic expression.

Referees cross-commenting

The following is a conversation among the three referees:

REFEREE #2: I appear to be the dissenting voice in terms of concern about the details of the 27 bp deletion and the "overexpression" constructs. I would be interested to know your opinions regarding my comments on these issues.

REFEREE #1: I think adding the details of the 27 bp deletion is a reasonable request. It is probably not possible to disambiguate entirely the two effects of the deletion, and changing the start codon may result in an alternate start with other downstream effects. I think just explaining it more fully in the methods would satisfy my concerns.

REFEREE #2: What about the issues with the overexpresssion? In my experience, presence of multicopy transgenes on an extrachromosomal arrays might not lead to over expression of the gene involved? This needs to be verified in some way.

REFEREE #1: You are right about that. If the construct is tagged in some way they could try a western. I would recommend they integrate the transgenes, or just show results from several lines as you suggest.

REFEREE #3: I agree the 27 bp deletion and over expression are reasonable technical issues. However, I view this a techical details vs. critical details for the novel regulatory mechanism. The point about ability to judge conservation is also reasonable but until the theory is firmly out there it is hard to test the conservation and broader applicability to other genes/proteins. Thus, while asking for additional information on these issues is reasonable I do not see the inability to address beyond highlighting as limitation in the text as critical to the overall validity of the work.

REFEREE #2: I disagree with Reviewer #3, without knowing the details of 27 bp deletion the most reasonable interpretation of the data is simply that it is a loss-of-function allele of zyx-1. This goes beyond "technical" - at present there is no unequivocal evidence that peu-1 has any functional significance beyond that it is expressed as a peptide.

REFEREE #3: I've been back through the manuscript. They have sequenced the deletion and therefore should be able to provide that information to satisfy the issue(s). For the over expression, short of silencing my experience is that they do over express and when you have multiple lines some express more than others (and some silence more than others). If you want evidence that the peptide is over expressed ask them to quantify via mass spec if it isn't tagged and they can't do a Western. Clearly they have work leading expertise in quantitative mass spec proteomics in C. elegans and should be able to do that. Generally speaking, rescue of a deletion is a pretty good sign that the expression is working though (and is an accepted standard).

Significance

The authors propose an interesting interaction between an important regulator of cellular behaviour (zyxin) and the u/uoORF that potentially regulates its expression - if validated by further experimentation, this would add to the growing evidence for the importance of the 5' UTR as a source of gene regulatory activity. Such regulation is well described in yeast, but there are fewer examples in animals, particularly in genetically tractable systems such as C. elegans. The work would primarily be of interest to researchers interested in understanding the spectrum of such activity in C. elegans. My own area of expertise, RNA-splicing and the post-transcriptional regulation of C. elegans gene expression, is not directly related to the research presented in the manuscript, but I am familiar with the general concepts and developments involved.

Author Response

Reviewer #1 (Public Review):

This fMRI study investigated how memories are updated after reinterpreting past events. Participants watched a movie and subsequently recalled individual scenes from that movie. Importantly, the movie ends with a twist that changes the interpretation of earlier scenes in the movie. One group of participants watched the movie with the twist at the end, one group did not get to see the twist, and a third group was already informed about this twist before watching the movie. Analyses compared the similarity of activity patterns to (encoded or recalled) events across participants within regions of the default mode network (DMN). The design allowed for multiple relevant comparisons, confirming the prediction that activity patterns in DMN regions reflect the (re)interpretation of the movie (during movie viewing and/or during recall).

The study is well-designed and executed. The inclusion of multiple analyses involving distinct comparisons strengthens the evidence for the role of the DMN in memory updating.

The following points may be relevant to consider:

1) The cross-participant pattern analysis method used here is not standard, with such analyses typically done within participants (or across participants, but after aligning representational spaces). Considering individual variability in functional organization, the method is likely only sensitive to coarse-scale patterns (e.g., anterior vs posterior parts of an ROI). This is not necessarily a weakness but is relevant when interpreting the results.

We agree with the reviewer that functional misalignment might have played against us here. We designed this study as a natural successor of our previous work in which we captured reliable and multimodal scene-specific cross-participant pattern similarity during encoding and recall in standard space. In this revised version, we provide further evidence on how scene content is captured and influences our results. Nonetheless, we agree with your comment and add the following section to the discussion to encourage considering this point while interpreting the results.

"Moreover, our current method relies on averaging spatially-coarse activity patterns across subjects (and time points within an event). Future extensions of this work may benefit from using functional alignment methods (Haxby et al 2020, Chen et al 2015) to capture more fine-grained event representations which are shared across participants."

2) Unlike previous work, analyses are not testing for scene-specific information. Rather, each scene is treated separately to establish between-group differences, and results are averaged across scenes. This raises the question of whether the patterns reflect scene-specific information or generic group differences. For example, knowing the twist may increase overall engagement, both when viewing the movie (spoiled group) and when recalling it (spoiled group + twist group). The DMN may be particularly sensitive to such differences in overall engagement.

You have brought up great points. We addressed them in two ways: (1) We ran a univariate analysis in each DMN ROI to look at the role of overall regional-average response magnitude in our results. We did not observe a significant effect of group or an interaction between group and condition. (2) We ran a scene-specificity analysis in a new Results section entitled “The role of scene content” (Figure 4). This section is focused on comparing interaction index (Figure 2C), as an indicator of memory updating, under different manipulations. Interaction index reflects the reversal of neural similarity during encoding and recall. Our results suggest that we don’t see the same effects if we shuffle the scene labels and recompute the pattern similarity analyses. Please see added text and figures below:

"To test whether our reported results were mainly driven by the similarities and differences in multivariate spatial patterns of neural representations, as opposed to by univariate regional-average response magnitudes, we ran a univariate analysis in each ROI. This analysis revealed no significant effect of group (“spoiled”, “twist”, “no-twist”) or interaction between group and condition (movie, recall) (Table 1, see Methods for details).

Next, to determine whether scene-specific neural event representations—as opposed to coarser differences in general mental state across all scenes with similar interpretations—drive our observed pISC differences, we shuffled the labels of critical scenes within each group before calculating and comparing pISC across groups. By repeating this procedure 1000 times and recalculating the interaction index at each iteration, we constructed a null distribution of interaction indices for shuffled critical scenes (light magenta distributions in Figure 4B). In 12 out of 24 DMN regions, interaction indices were statistically significant based on the shuffled-scene distribution (p < .025, FDR controlled at q < .05). All of these 12 regions were among the ROIs that showed meaningful effects in our original analysis (Figure 2C). Regions with significant scene-specific interaction effects are marked as blue dots with black borders in Figure 4B. Overall, the findings from this analysis confirm that our results are driven by changes to scene-specific representations."

3) The study does not reveal what the DMN represents about the movie, such that its activity changes after knowing the twist. The Discussion briefly mentions that it may reflect the state of the observer, related to the belief about the identity of the doctor. This suggests a link to the theory of mind/mentalizing, but this is not made explicit. Alternatively, the DMN may be involved in the conflict (or switching) between the two interpretations.

Great points. We added to the discussion about the role of mentalizing network and in the particular temporo-parietal cortex. About your last point, we think our whole brain findings outside DMN (ACC and dlPFC) might relate to that point. We discussed these further in the paper.

"We performed two targeted analyses to look for evidence of memory updating across encoding and recall: the interaction analysis (Figure 2C) and the encoding-recall analysis (Figure 3). We hypothesized that a shift in direction of pISC difference would occur when neural representations during recall in the “twist” group start to reflect the Ghost interpretation. The interaction analysis probed this shift indirectly by taking into account the effects of both encoding-encoding and recall-recall analyses. Unlike the interaction analysis, in the encoding-recall analysis, we directly compared neural event representations during encoding and recall. Interestingly, all regions exhibiting an effect across the two encoding-recall analyses, excluding left anterior temporal cortex, were present in the interaction results. Among these regions, the left angular gyrus/TPJ exhibited an effect across all three analyses. As a core hub in the mentalizing network, temporo-parietal cortex has been implicated in theory of mind through perspective-taking, rationalizing the mental state of someone else, and modeling the attentional state of others (Frith and Frith 2006, Guterstam et. al 2021, Saxe and Kanwisher 2003). The motivations behind some actions of the main character in the movie heavily depend on whether the viewer perceives them as a Doctor or a Ghost, and participants may focus on this during both encoding and recall. We speculate that neural event representations in AG/TPJ in the current experiment may be related to mentalizing about the main character’s actions. Under this interpretation, the updated event representations during recall following the twist would be more closely aligned to the “spoiled” encoding representations, as a consequence of memory updating in the “twist” group.

In our whole brain analysis, these regions did not have significant interaction effects, which suggests that the effects were isolated to encoding. In the whole-brain analysis, we also observed a significant encoding-encoding and interaction effects in anterior cingulate cortex, as well as recall-recall and interaction effects in dlPFC. These results suggest that both the "spoiled" manipulation and the "twist" may recruit top-down control and conflict monitoring processes during naturalistic viewing and recall."

4) The design has many naturalistic aspects, but it is also different from real life in that the critical twist involves a ghost. Furthermore, all results are based on one movie with a specific plot twist. It is thus not clear whether similar results would be obtained with other and more naturalistic plot twists.

We added this as a limitation of the study.

"Our findings provide further insight into the functional role of the DMN. However, these results have been obtained using only one movie. While naturalistic paradigms better capture the complexity of real life and provide greater ecological generalizability than highly-controlled experimental stimuli and tasks (Nastase et al., 2020), they are still limited by the properties of the particular naturalistic stimulus used. For example, this movie—including the twist itself—hinges on suspension of disbelief about the existence of ghosts. Future work is needed to extend our findings about updating event memories to a broader class of naturalistic stimuli: for example, movies with different kinds of (non-supernatural) plot twists, spoken stories with twist endings, or using autobiographical real-life situations where new information (e.g. discovering a longtime friend has lied about something important) triggers re-evaluation of the past (e.g. reinterpreting their friend’s previous actions)."

5) Only 7 scenes (out of 18) were included in the analysis. It is not clear if/how the results depend on the selection of these 7 scenes.

Thank you for bringing this up. These scenes were pre-selected for the analyses, as they are the only scenes that are rated high by our independent raters (not study participants) on “twist influence”, meaning that knowing the twist could dramatically change their interpretation. So, we had a priori reasons to hypothesize that the effect will be strong in these scenes. To address your point, we report results by including all 18 scenes in a new Results section entitled “The role of scene content” and in Figure 4A. While the effect was weaker for all scenes it was still apparent in this conservative analysis. As expected, however, including 7 critical scenes produces stronger results than including all scenes or the uncritical scenes (all minus critical scenes). Please see the “The role of scene content” in Results and in Figure 4 for more detailed information.

"The role of scene content In the prior analyses, we focused on “critical scenes”, selected based on ratings from four raters who quantified the influence of the twist on the interpretation of each scene (see Methods). An independent post-experiment analysis of the verbal recall behavior of the fMRI participants yielded “twist scores” that were also highest for these scenes; that is, the expected and perceived effect of twist information on recall behavior were found to match. In our next analysis, we asked whether the neural event representations reflect these differences in the twist-related content of the scenes. In other words, are the “critical scenes” with highly twist-dependent interpretations truly critical for our observed effects?

To answer this question, we re-ran our main encoding-encoding and recall-recall pISC analysis in each DMN ROI (Figure 2-3). We calculated interaction indices (Figure 2C) first by including all scenes, and second by including only the 11 non-critical scenes. To better compare the effect of including different subsets of scenes to our original results, in Figure 4 we show the results in 15 ROIs that exhibited meaningful effects in our main analyses (Figure 2C). Figure 4A demonstrates that “critical scenes” yielded higher interaction indices compared to all scenes or non-critical scenes across all ROIs. The interaction score across all DMN ROIs was significantly higher in “critical scenes” than all scenes (t(23) = 7.19, p = 2.53 x 10-7) and non-critical scenes (t(23) = 7.3, p = 1.95 x 10-7). These results show that critical scenes are indeed responsible for the observed pISC differences across groups."

Reviewer #2 (Public Review):

In this manuscript titled "Here's the twist: How the brain updates the representations of naturalistic events as our understanding of the past changes", the authors reported a study that examined how new information (manipulated as a twist at the end of a movie) changes the neural representations in the default mode network (DMN) during the recall of prior knowledge. Three groups of participants were compared - one group experienced the twist at the end, one group never experienced the twist, and one group received a spoiler at the beginning. At retrieval, participants received snippets of 18 scenes of the movie as cues and were asked to freely describe the events of each scene and to provide the most accurate interpretation of the scene, given the information they gathered throughout watching.

All three groups were highly accurate in the recall of content. The groups that experienced the twist at the end as well as at the beginning as a spoiler showed a higher twist score (the extent to which twist information was incorporated into the recall), while seemingly also keeping the interpretation without the twist ("Doctor representation") intact. Neurally, several regions in the DMN showed significant interaction effects in their neural similarity patterns (based on intersubject pattern correlation), indicating a change in interpretation between encoding and recall in the twist group uniquely, presumably reflecting memory updating.

Several points that I think should be addressed to strengthen the manuscript:

1) The results from encoding-retrieval similarity analysis (particularly the one depicted in Figure 3B) don't match the results from encoding/retrieval interaction (particularly those shown in Figure 2C). While they were certainly based on different comparisons, I would think that both analyses were set up to test for memory updating. Can the authors comment on this divergence in results?

Thank you for your comment. Except for one ROI, the other two regions in Figure 2C are present in the interaction analysis. The ROI at the frontal pole might be hard to see from this angle but in fact it holds a high effect size in interaction analysis. So we do not see a big divergence between these two results. But taking into account the recall-recall results, we agree that there seems to be inhomogeneity. We discussed these further in the discussion.

"We performed two targeted analyses to look for evidence of memory updating across encoding and recall: the interaction analysis (Figure 2C) and the encoding-recall analysis (Figure 3). We hypothesized that a shift in direction of pISC difference would occur when neural representations during recall in the “twist” group start to reflect the Ghost interpretation. The interaction analysis probed this shift indirectly by taking into account the effects of both encoding-encoding and recall-recall analyses. Unlike the interaction analysis, in the encoding-recall analysis, we directly compared neural event representations during encoding and recall. Interestingly, all regions exhibiting an effect across the two encoding-recall analyses, excluding left anterior temporal cortex, were present in the interaction results. Among these regions, the left angular gyrus/TPJ exhibited an effect across all three analyses. As a core hub in the mentalizing network, temporo-parietal cortex has been implicated in theory of mind through perspective-taking, rationalizing the mental state of someone else, and modeling the attentional state of others (Frith and Frith 2006, Guterstam et. al 2021, Saxe and Kanwisher 2003). The motivations behind some actions of the main character in the movie heavily depend on whether the viewer perceives them as a Doctor or a Ghost, and participants may focus on this during both encoding and recall. We speculate that neural event representations in AG/TPJ in the current experiment may be related to mentalizing about the main character’s actions. Under this interpretation, the updated event representations during recall following the twist would be more closely aligned to the “spoiled” encoding representations, as a consequence of memory updating in the “twist” group.

Our findings are consistent with the view that DMN synthesizes incoming information with one’s prior beliefs and memories (Yeshurun et al 2021). We add to this framework by providing evidence for the involvement of DMN regions in updating prior beliefs in light of new knowledge. Across our different encoding and recall analyses, we observe memory updating effects in a varied subset of DMN regions that do not cleanly map onto a specific subsystem of DMN (Robin and Moscovitch 2017, Ranganath and Ritchey 2012, Ritchey and Cooper 2020). Rather than being divergent, these results might be reflecting inherent differences between the processes of encoding and recall of naturalistic events. It has been proposed that neural representations corresponding to encoding of events are systematically transformed during recall of those events (Chen et al 2017, Favila et al 2020, Musz and Chen 2022). While we provide evidence for reinstatement of memories in DMN, our findings also support a transformation of neural representation during recall, as encoding-recall results were weaker in some areas than recall-recall findings. This transformation could affect how different regions and sub-systems of DMN represent memories, and suggests that the concerted activity of multiple subsystems and neural mechanisms might be at play during encoding, recall and successful updating of naturalistic event memories."

2) The recall task was self-paced. Can reaction time information be provided on how long participants needed to recall? Did this differ across groups? Presumably in the twist group and spoiled group participants might have needed a longer time to incorporate both the original and twist interpretation.

This is an interesting idea. Unfortunately, we could not measure this accurately because our recall cues were snippets from the beginning of each scene with different length (selected based on content). And updating could begin from the beginning of those snippets (but we wouldn’t know when). We will consider this point in the future related designs.

How was the length difference across events taken into consideration in the beta estimates?

They were used as event durations in the GLM model.

Also, is there an order effect, such that one type of interpretation tended to be recalled first?

This is hard to measure as this only occurs in a subset of scenes. But we assume it happens in other people’s brains as well

This is indeed hard to measure as you mentioned. We will provide the transcripts when sharing the data and hopefully this will facilitate future text-analysis work on this dataset to answer interesting questions like this.

3) The correlation analysis between neural pattern change and behavioral twist score is based on a small sample size and does not seem to be well suited to test the postulation of the authors, namely that some participants may hold both interpretations in their memory. Interestingly, the twist score of the spoiled group was similar to the twist group, indicating participants in this group might have held both interpretations as well. Could this observation be leveraged, for example by combining both groups (hence better powered with larger sample size), in order to relate individual differences in neural similarity patterns and behavioral tendency to hold both interpretations?

Even though both groups showed signs of holding both interpretations in mind, the process happening in their brain during the recall is different. In particular, we do not expect to see any updating effect in the spoiled group. So it wouldn’t seem accurate to combine these groups to test the effect of incomplete updating.

4) Several regions within the DMN were significant across the analysis steps, specifically the angular gyrus, middle temporal cortex, and medial PFC. Can the authors provide more insights on how these widely distributed regions may act together to enable memory updating? The discussion on the main findings is largely at a rather superficial level about DMN, or focuses specifically on vmPFC, but neglects the distributed regions that presumably function interactively

Thanks for bringing this up. We added text to discussion to respond to this very valid point. Please see the added text in our response to your first point. One more snippet added to the discussion about this:

"In addition to mPFC, right precuneus and parts of temporal cortex exhibited significantly higher pattern similarity in the “twist” and “spoiled” groups who recalled the movie with the same interpretation. Precuneus is a core region in the posterior medial network, which is hypothesized to be involved in constructing and applying situation models (Ranganath and Ritchey 2012). Our findings support a role for precuneus in deploying interpretation-specific situation models when retrieving event memories. In particular, we suggest that the posterior medial network may encode a shift in the situation model of the “twist” group in order to accommodate the new Ghost interpretation.

We performed two targeted analyses to look for evidence of memory updating across encoding and recall: the interaction analysis (Figure 2C) and the encoding-recall analysis (Figure 3). We hypothesized that a shift in direction of pISC difference would occur when neural representations during recall in the “twist” group start to reflect the Ghost interpretation. The interaction analysis probed this shift indirectly by taking into account the effects of both encoding-encoding and recall-recall analyses. Unlike the interaction analysis, in the encoding-recall analysis, we directly compared neural event representations during encoding and recall. Interestingly, all regions exhibiting an effect across the two encoding-recall analyses, excluding left anterior temporal cortex, were present in the interaction results. Among these regions, the left angular gyrus/TPJ exhibited an effect across all three analyses. As a core hub in the mentalizing network, temporo-parietal cortex has been implicated in theory of mind through perspective-taking, rationalizing the mental state of someone else, and modeling the attentional state of others (Frith and Frith 2006, Guterstam et. al 2021, Saxe and Kanwisher 2003). The motivations behind some actions of the main character in the movie heavily depend on whether the viewer perceives them as a Doctor or a Ghost, and participants may focus on this during both encoding and recall. We speculate that neural event representations in AG/TPJ in the current experiment may be related to mentalizing about the main character’s actions. Under this interpretation, the updated event representations during recall following the twist would be more closely aligned to the “spoiled” encoding representations, as a consequence of memory updating in the “twist” group.

Our findings are consistent with the view that DMN synthesizes incoming information with one’s prior beliefs and memories (Yeshurun et al 2021). We add to this framework by providing evidence for the involvement of DMN regions in updating prior beliefs in light of new knowledge. Across our different encoding and recall analyses, we observe memory updating effects in a varied subset of DMN regions that do not cleanly map onto a specific subsystem of DMN (Robin and Moscovitch 2017, Ranganath and Ritchey 2012, Ritchey and Cooper 2020). Rather than being divergent, these results might be reflecting inherent differences between the processes of encoding and recall of naturalistic events. It has been proposed that neural representations corresponding to encoding of events are systematically transformed during recall of those events (Chen et al 2017, Favila et al 2020, Musz and Chen 2022). While we provide evidence for reinstatement of memories in DMN, our findings also support a transformation of neural representation during recall, as encoding-recall results were weaker in some areas than recall-recall findings. This transformation could affect how different regions and sub-systems of DMN represent memories, and suggests that the concerted activity of multiple subsystems and neural mechanisms might be at play during encoding, recall and successful updating of naturalistic event memories."

Reviewer #3 (Public Review):

Zadbood and colleagues investigated the way key information used to update interpretations of events alter patterns of activity in the brain. This was cleverly done by the use of "The Sixth Sense," a film featuring a famous "twist ending," which fundamentally alters the way the events in the film are understood. Participants were assigned to three groups: (1) a Spoiled group, in which the twist was revealed at the outset, (2) a Twist group, who experienced the film as normal, and (3) a No-Twist group, in which the twist was removed. Participants were scanned while watching the movie and while performing cued recall of specific scenes. Verbal recall was scored based on recall success, and evidence for descriptive bias toward two ways of understanding the events (specifically, whether a particular character was or was not a ghost). Importantly, this allowed the authors to show that the Twist group updated their interpretation. The authors focused on regions of the Default Mode Network (DMN) based on prior studies showing responsiveness to naturalistic memory paradigms in these areas and analyzed the fMRI data using intersubject pattern similarity analysis. Regions of the DMN carried patterns indicative of story interpretation. That is, encoding similarity was greater between the Twist and No-Twist groups than in the Spoiled group, and retrieval similarity was greater between the Twist and Spoiled groups than in the No-Twist group. The Spoiled group also showed greater pattern similarity with the Twist group's recall than the No-Twist group's recall. The authors also report a weaker effect of greater pattern similarity between the Spoiled group's encoding and the Twist group's recall than between the Twist group's own encoding and recall. Together, the data all converge on the point that one's interpretation of an event is an important determinant of the way it is represented in the brain.

This is a really nice experiment, with straightforward predictions and analyses that support the claims being made. The results build directly on a prior study by this research group showing how interpretational differences in a narrative drive distinct neural representations (Yeshurun et al., 2017), but extend an understanding of how these interpretational differences might work retrospectively. I do not have any serious concerns or problems with the manuscript, the data, or the analyses. However I have a few points to raise that, if addressed, would make for a stronger paper in my opinion.

1) My most substantive comment is that I did not find the interpretive framework to be very clear with respect to the brain regions involved. The basic effects the authors report strongly support their claims, but the particular contributions to the field might be stronger if the interpretations could be made more strongly or more specifically. In other words: the DMN is involved in updating interpretations, but how should we now think about the role of the DMN and its constituent regions as a result of this study? There are a number of ideas briefly presented about what the DMN might be doing, but it just did not feel very coherent at times. I will break this down into a few more specific points:

While many of us would agree that the DMN is likely to be involved in the phenomena at hand, I did not find that the paper communicated the logic for singularly focusing on this subset of regions very compellingly. The authors note a few studies whose main results are found in DMN regions, but I think that this could stand to be unpacked in a more theoretically interesting way in the Introduction.

Relatedly, I found the summary/description of regional effects in the Discussion to be a bit unsatisfying. The various pattern similarity comparisons yielded results that were actually quite nonoverlapping among DMN regions, which was not really unpacked. To be clear, it is not a 'problem' that the regional effects varied from comparison to comparison, but I do think that a more theoretical exploration of what this could mean would strengthen the paper. To the authors' credit, they describe mPFC effects through the lens of schemas, but this stands in contrast to many other regions which do not receive much consideration.

Finally, although there is evidence that regions of the DMN act in a coordinated way under some circumstances, there is also ample evidence for distinct regional contributions to cognitive processes, memory being just one of them (e.g., Cooper & Ritchey, 2020; Robin & Moscovitch, 2017; Ranganath & Ritchey, 2012). The authors themselves introduce the idea of temporal receptive windows in a cortical hierarchy, and while DMN regions do appear to show slower temporal drift than sensory areas, those studies show regional differences in pattern stability across time even within DMN regions. Simply put, it is worth considering whether it is ideal to treat the DMN as a singular unit.

Thank you for your helpful comments. We added text to the introduction and discussion to address your point:

"Introduction:

The brain’s default mode network (DMN)—comprising the posterior medial cortex, medial prefrontal cortex, temporoparietal junction, and parts of anterior temporal cortex—was originally described as an intrinsic or “task-negative” network, activated when participants are not engaged with external stimuli (Raichle et al. 2001, Buckner et al 2008). This observation led to a large body of work showing that the DMN is an important hub for supporting internally driven tasks such as memory retrieval, imagination, future planning, theory of mind, and creating and updating situation models (Svoboda et al. 2006; Addis et al. 2007; Hassabis and Maguire 2007, 2009; Schacter et al. 2007; Szpunar et al. 2007; Spreng et al. 2009, Koster-Hale & Saxe, 2013 2013, Ranganath and Ritchey 2012). However, it is not fully understood how this network contributes to these varying functions, and in particular—the focus of the present study—memory processes. Activation of this network during “offline” periods has been proposed to play a role in the consolidation of memories through replay (Kaefer et al 2022). Interestingly, prior work has also shown that the DMN is reliably engaged during “online” processing (encoding) of continuous rich dynamic stimuli such as movies and audio stories (Stephens et al 2013, Hasson et al 2008). Regions in this network have been shown to have long “temporal receptive windows” (Hasson et al 2008; Lerner et al., 2011; Chang et al., 2022), meaning that they integrate and retain high-level information that accumulates over the course of extended timescales (e.g. scenes in movies, paragraphs in text) to support comprehension. This combination of processing characteristics suggests that the DMN integrates past and new knowledge, as regions in this network have access to incoming sensory input, recent active memories, and remote long-term memories or semantic knowledge (Yeshurun et al 2021, Hasson et al 2015). These integration processes feature in many of the “constructive” processes attributed to DMN such as imagination, future planning, mentalizing, and updating situation models (Schacter and Addis 2007, Ranganath and Ritchey 2012). Notably, constructive processes are highly relevant to real-world memory updating, which involves selecting and combining the relevant parts of old and new memories. Recent work has shown that neural patterns during encoding and recall of naturalistic stimuli (movies) are reliably similar across participants in this network (Chen et al. 2017; Oedekoven et al., 2017; Zadbood et al., 2017; see Bird 2020 for a review of recent naturalistic studies on memory), and the DMN displays distinct neural activity when listening to the same story with different perspectives (Yeshurun et al 2017). Building on this foundation of prior work on the DMN, we asked whether we could find neural evidence for the retroactive influence of new knowledge on past memories."

"Discussion :

In addition to mPFC, right precuneus and parts of temporal cortex exhibited significantly higher pattern similarity in the “twist” and “spoiled” groups who recalled the movie with the same interpretation. Precuneus is a core region in the posterior medial network, which is hypothesized to be involved in constructing and applying situation models (Ranganath and Ritchey 2012). Our findings support a role for precuneus in deploying interpretation-specific situation models when retrieving event memories. In particular, we suggest that the posterior medial network may encode a shift in the situation model of the “twist” group in order to accommodate the new Ghost interpretation.

We performed two targeted analyses to look for evidence of memory updating across encoding and recall: the interaction analysis (Figure 2C) and the encoding-recall analysis (Figure 3). We hypothesized that a shift in direction of pISC difference would occur when neural representations during recall in the “twist” group start to reflect the Ghost interpretation. The interaction analysis probed this shift indirectly by taking into account the effects of both encoding-encoding and recall-recall analyses. Unlike the interaction analysis, in the encoding-recall analysis, we directly compared neural event representations during encoding and recall. Interestingly, all regions exhibiting an effect across the two encoding-recall analyses, excluding left anterior temporal cortex, were present in the interaction results. Among these regions, the left angular gyrus/TPJ exhibited an effect across all three analyses. As a core hub in the mentalizing network, temporo-parietal cortex has been implicated in theory of mind through perspective-taking, rationalizing the mental state of someone else, and modeling the attentional state of others (Frith and Frith 2006, Guterstam et. al 2021, Saxe and Kanwisher 2003). The motivations behind some actions of the main character in the movie heavily depend on whether the viewer perceives them as a Doctor or a Ghost, and participants may focus on this during both encoding and recall. We speculate that neural event representations in AG/TPJ in the current experiment may be related to mentalizing about the main character’s actions. Under this interpretation, the updated event representations during recall following the twist would be more closely aligned to the “spoiled” encoding representations, as a consequence of memory updating in the “twist” group.

Our findings are consistent with the view that DMN synthesizes incoming information with one’s prior beliefs and memories (Yeshurun et al 2021). We add to this framework by providing evidence for the involvement of DMN regions in updating prior beliefs in light of new knowledge. Across our different encoding and recall analyses, we observe memory updating effects in a varied subset of DMN regions that do not cleanly map onto a specific subsystem of DMN (Robin and Moscovitch 2017, Ranganath and Ritchey 2012, Ritchey and Cooper 2020). Rather than being divergent, these results might be reflecting inherent differences between the processes of encoding and recall of naturalistic events. It has been proposed that neural representations corresponding to encoding of events are systematically transformed during recall of those events (Chen et al 2017, Favila et al 2020, Musz and Chen 2022). While we provide evidence for reinstatement of memories in DMN, our findings also support a transformation of neural representation during recall, as encoding-recall results were weaker in some areas than recall-recall findings. This transformation could affect how different regions and sub-systems of DMN represent memories, and suggests that the concerted activity of multiple subsystems and neural mechanisms might be at play during encoding, recall and successful updating of naturalistic event memories."

2) I think that some direct comparison to regions outside the DMN would speak to whether the DMN is truly unique in carrying the key representations being discussed here. I was reluctant to suggest this because I think that the authors are justified in expecting that DMN regions would show the effects in question. However, there really is no "null" comparison here wherein a set of regions not expected to show these effects (e.g., a somatosensory network, or the frontoparietal network) in fact do not show them. There are not really controls or key differences being hypothesized across different conditions or regions. Rather, we have a set of regions that may or may not show pattern similarity differences to varying degrees, which feels very exploratory. The inclusion of some principled control comparisons, etc. would bolster these findings. The authors do include a whole-brain analysis in Supplementary Figure 1, which indeed produced many DMN regions. However, notably, regions outside the DMN such as the primary visual cortex and mid-cingulate cortex appear to show significant effects (which, based on the color bar, might actually be stronger than effects seen in the DMN). Given the specificity of the language in the paper in terms of the DMN, I think that some direct regional or network-level comparison is needed.

In the original submission, we included additional analyses for visual and somatosensory networks, which we hypothesized would serve as control networks. Following your comment, in the revision, we added a separate section (included below) more thoroughly examining these analyses. We also added text to the results and discussion to explain our interpretation of these findings.

"Changes in neural representations beyond DMN We focused our core analyses on regions of the default mode network. Prior work has shown that multimodal neural representations of naturalistic events (e.g. movie scenes) are similar across encoding (movie-watching or story-listening) and verbal recall of the same events in the DMN (Chen et al., 2017; Zadbood et al., 2017). Therefore, in the current work we hypothesized that retrospective changes in the neural representations of events as the narrative interpretation shifts would be observed in the DMN. We did not, for example, expect to observe such effects in lower-level sensory regions, where neural activity differs dramatically for movie-viewing and verbal recall. To be thorough, we ran the same set of analyses we performed in the DMN (Figure 2-3) in regions of the visual and somatomotor networks extracted from the same atlas parcellation (Schaefer et al., 2018). Our results revealed larger overall differences in DMN than in visual and somatosensory networks for the key comparisons discussed previously (Figure S2). In particular, the only regions showing significant differences in pISC in recall-recall and encoding-recall comparisons (p < 0.01, uncorrected) were located in the DMN. We did not observe a notable difference between DMN and the two other networks when comparing recall “twist” to movie “spoiled” and recall “twist” to movie “twist” (RG – MG > RG – MD) which is consistent with the weak effect in the original comparison (Figure 3B). In the encoding-encoding comparison, several ROIs from the visual and somatomotor networks showed relatively strong effects as well (see Discussion).

In addition, we qualitatively reproduced our results by performing an ROI-based whole brain analysis (Figure S3, p < 0.01 uncorrected). This analysis confirmed the importance of DMN regions for updating neural event representations. However, strong differences in pISC in the hypothesized direction were also observed in a handful of other non-DMN regions, including ROIs partly overlapping with anterior cingulate cortex and dorsolateral prefrontal cortex (see Discussion)."

"Discussion: While our main goal in this paper was to examine how neural representations of naturalistic events change in the DMN, we also examined visual and somatosensory networks. Aside from the encoding-encoding analysis in which some visual and somatosensory regions showed stronger similarity between two groups with the same interpretation of the movie, we did not find any regions with significant effects in these two networks in the other analyses. Unlike the recall phase where each participant has their unique utterance with their own choice of words and concepts to describe the movie, the encoding (move-watching) stimulus is identical across all groups. Therefore, the effects observed during encoding-encoding analysis in sensory regions could reflect similarity in perception of the movie guided by similar attentional state while watching scenes with the same interpretation (e.g. similarity in gaze location, paying attention to certain dialogues, or small body movements while watching the movie with the same Doctor or Ghost interpretations). In our whole brain analysis, these regions did not have significant interaction effects, which suggests that the effects were isolated to encoding. In the whole-brain analysis, we also observed a significant encoding-encoding and interaction effects in anterior cingulate cortex, as well as recall-recall and interaction effects in dlPFC. These results suggest that both the "spoiled" manipulation and the "twist" may recruit top-down control and conflict monitoring processes during naturalistic viewing and recall."

3) If I understand correctly, the main analyses of the fMRI data were limited to across-group comparisons of "critical scenes" that were maximally affected by the twist at the end of the movie. In other words, the analyses focused on the scenes whose interpretation hinged on the "doctor" versus "ghost" interpretation. I would be interested in seeing a comparison of "critical" scenes directly against scenes where the interpretation did not change with the twist. This "critical" versus "non-critical" contrast would be a strong confirmatory analysis that could further bolster the authors' claims, but on the other hand, it would be interesting to know whether the overall story interpretation led to any differences in neural patterns assigned to scenes that would not be expected to depend on differences in interpretation. (As a final note, such a comparison might provide additional analytical leverage for exploring the effect described in Figure 3B, which did not survive correction for multiple comparisons.)

This is a helpful suggestion, and we’ve added an analysis addressing your comment. We found that the interaction index capturing the difference between the three groups was stronger for the critical scenes than for the non-critical scenes for almost all DMN ROIs.

"The role of scene content In the prior analyses, we focused on “critical scenes”, selected based on ratings from four raters who quantified the influence of the twist on the interpretation of each scene (see Methods). An independent post-experiment analysis of the verbal recall behavior of the fMRI participants yielded “twist scores” that were also highest for these scenes; that is, the expected and perceived effect of twist information on recall behavior were found to match. In our next analysis, we asked whether the neural event representations reflect these differences in the twist-related content of the scenes. In other words, are the “critical scenes” with highly twist-dependent interpretations truly critical for our observed effects?

To answer this question, we re-ran our main encoding-encoding and recall-recall pISC analysis in each DMN ROI (Figure 2-3). We calculated interaction indices (Figure 2C) first by including all scenes, and second by including only the 11 non-critical scenes. To better compare the effect of including different subsets of scenes to our original results, in Figure 4 we show the results in 15 ROIs that exhibited meaningful effects in our main analyses (Figure 2C). Figure 4A demonstrates that “critical scenes” yielded higher interaction indices compared to all scenes or non-critical scenes across all ROIs. The interaction score across all DMN ROIs was significantly higher in “critical scenes” than all scenes (t(23) = 7.19, p = 2.53 x 10-7) and non-critical scenes (t(23) = 7.3, p = 1.95 x 10-7). These results show that critical scenes are indeed responsible for the observed pISC differences across groups."

4) I appreciate the code being made available and that the neuroimaging data will be made available soon. I would also appreciate it if the authors made the movie stimulus and behavioral data available. The movie stimulus itself is of interest because it was edited down, and it would be nice for readers to be able to see which scenes were included.

Unfortunately due to copyright, we cannot share the movie stimulus outright. However, we will share the timing of the cuts used, as well as the time-stamped transcripts of verbal recall.

To sum up, I think that this is a great experiment with a lot of strengths. The design is fairly clean (especially for a movie stimulus), the analyses are well reasoned, and the data are clear. The only weaknesses I would suggest addressing are with regards to how the DMN is being described and evaluated, and the communication of how this work informs the field on a theoretical level.

Author Response

Reviewer #1 (Public Review):

In a very interesting and technically advanced study, the authors measured the force production of curved protofilaments at depolymerizing mammalian microtubule ends using an optical trap assay that they developed previously for yeast microtubules. They found that the magnesium concentration affects this force production, which they argue based on a theoretical model is due to affecting the length of the protofilament curls, as observed previously by electron microscopy. Comparing with their previous force measurements, they conclude that mammalian microtubules produce smaller force pulses than yeast microtubules due to shorter protofilament curls. This work provides new mechanistic insight into how shrinking microtubules exert forces on cargoes such as for example kinetochores during cell division. The experiments are sophisticated and appear to be of high quality, conclusions are well supported by the data, and language is appropriate when conclusions are drawn from more indirect evidence. Given that the experimental setup differs from the previous optical trap assay (antibody plus tubulin attached to bead versus only antibody attached to bead), a control experiment could be useful with yeast microtubules using the same protocol used in the new variant of the assay, or at least a discussion regarding this issue. One open question may be whether the authors can be sure that measured forces are only due to single depolymerizing protofilaments instead of two or more protofilaments staying laterally attached for a while. How would this affect the interpretation of the data?

This work will be of interest to cell biologists and biophysicists interested in spindle mechanics or generally in filament mechanics.

Thank you for your careful reading of our manuscript, your kind remarks, and your favorable review.

Reviewers #1 and #2 both mentioned a concern about potential differences between our previous setup with yeast microtubules, versus our new setup with predominantly bovine microtubules, and whether such differences might underlie the different pulse amplitudes we measured. We think this concern comes mainly from a misunderstanding of how the beads in both setups were tethered to the sides of the microtubules, and we apologize for not making this aspect clearer in our original submission.

It is true that our new setup requires one additional step, pre-decoration of the anti-His beads with His6-tagged yeast tubulin. However, in both cases, the anti-His antibodies were kept very sparse on the beads to ensure that most beads, if they became tethered to a microtubule, were attached by a single antibody. (~30 pM beads were mixed with 30 pM of anti-His antibody, for a molar ratio of 1:1.) And even though the anti-His beads in our previous work did not undergo a separate incubation step for pre-decoration with tubulin, they undoubtedly were decorated immediately after being mixed into the microtubule growth mix, which in that case included ~1 µM of unpolymerized His6-tagged yeast tubulin dimers. Thus, the arrangement with beads tethered laterally to the sides of microtubules via single antibodies was created in both cases by essentially the same three-step process: First, beads decorated very sparsely with anti-His antibodies were bound to unpolymerized His6-tagged yeast tubulin. Second, a bead-tethered His6-tagged yeast tubulin was incorporated into the growing tip of a microtubule (which could be assembling from either yeast or bovine tubulin, depending on the experiment). Third, the tip grew past the bead to create a large extension. Because the beads in both scenarios were tethered by a single antibody to the same C-terminal tail of yeast β-tubulin, the differences in pulse amplitude cannot be explained by differences in the tethering. In our revised manuscript, we now mention explicitly in Results that the beads were tethered by single antibodies (lines 95 to 100). In Methods we significantly expanded the section about preparation of beads and how they became tethered (lines 365 to 393). [We refer here, and below, to line numbers when the document is viewed with “All Markup” shown.]

You also raise an interesting, open question: Do protofilaments curl outward entirely independently of their lateral neighbors? Or under some conditions might they tend to stay laterally associated during the curling process, perhaps curling outward in pairs rather than as individual protofilaments? We cannot formally rule out the possibility that such lateral associations sometimes persist during protofilament curling. However, changes in lateral association seem unlikely to explain the magnesium- and species-dependent differences we measured in pulse amplitude, for several reasons: First, there is good evidence for lengthening of protofilament curls at disassembling tips (e.g., Mandelkow 1991, Tran & Salmon 1997), but we are not aware of convincing evidence for magnesium or species-dependent increases in the propensity of curling protofilaments to remain laterally associated. Second, an increase in lateral association should increase the effective flexural rigidity of the curls, but under all the conditions we examined, pulse enlargement was associated with a steepening of the amplitude-vs-force relation – i.e., with softening, not stiffening. Our model indicates that this softening can be fully explained by an increase in protofilament contour length, without any change in the intrinsic flexural rigidity of the protofilament curls.

Reviewer #2 (Public Review):

Microtubules are regarded as dynamic tracks for kinesin and dynein motors that generate force for moving cargoes through cells, but microtubules also act as motors themselves by generating force from outward splaying protofilaments at depolymerizing ends. Force from depolymerization has been demonstrated in vitro and is thought to contribute to chromosome movement and other contexts in cells. Although this model has been in the field for many years, key questions have remained unanswered, including the mechanism of force generation, how force generated might be regulated in cells, and how this system might be tuned across cellular contexts or organisms. The barrier is that we lack an understanding of experimental conditions that can be used to control protofilament shape and energetics. This study by Murray and colleagues makes an important advance towards overcoming that barrier.

This study builds on previous work from the authors where they developed a system to directly measure forces generated by outward curling protofilaments at depolymerizing microtubule ends. That study showed for the first time that protofilaments act like elastic springs and related the generated force to the estimated energy contained in the microtubule lattice. Furthermore, they showed that slowing polymerization rate did not diminish force generation. That study used recombinant yeast tubulin, including a 6x histidine tag on beta tubulin that created attachment points for the bead on the microtubule lattice. The current study extends that system to show that work output is related to the length of protofilament curls.

We are grateful for your very thoughtful and thorough review, which has helped us improve our manuscript.

Murray and colleagues show this by manipulating curls in two ways - using bovine brain tubulin instead of yeast tubulin and altering magnesium concentration. Previous EM studies indicated that protofilaments on depolymerizing bovine microtubules have similar curvature but are shorter. The authors here use a blend of bovine brain tubulin and bead-linked recombinant yeast tubulin with the 6x histidine tag in their in vitro system and find smaller deflections of the laser-trapped bead than previously observed with pure yeast tubulin. A concern with comparing this heterogeneous bovine/yeast system to the previous work with homogeneous yeast tubulin is that density of 6x histidine-tagged tubulin subunits is likely to be different between the two systems. Also, the rate of incorporation of 6x histidine yeast tubulin into bovine microtubules in the current study may be different from the rate of incorporation into yeast microtubules in the previous study. These differences could lead to changes in the strength of bead attachment to the microtubule lattice and alter the compliance of the bead to deflection by curling protofilaments. These possibilities and lattice attachment strength are not explored in this study, raising concerns about comparing the two systems.

Reviewers #1 and #2 both mentioned a concern about potential differences between our previous setup with yeast microtubules, versus our new setup with predominantly bovine microtubules, and whether such differences might underlie the different pulse amplitudes we measured. As detailed in our response to Reviewer #1 above, we think this concern comes mainly from a misunderstanding of how the beads in both setups were tethered to the sides of the microtubules, and we apologize for not making this aspect clearer in our original submission. For both our yeast and bovine microtubule experiments, the anti-His antibodies were kept very sparse on the beads to ensure that most beads, if they became tethered to a microtubule, were attached by a single antibody. Because the beads in both scenarios were tethered by a single antibody to the same C-terminal tail of yeast β-tubulin, the differences in pulse amplitude cannot be explained by differences in the tethering. In our revised manuscript, we now mention explicitly in Results that the beads were tethered by single antibodies (lines 95 to 100). In Methods we significantly expanded the section about preparation of beads and how they became tethered (lines 365 to 393).

The authors go on to show that magnesium increases bead deflection and work output from the system. The use of magnesium was motivated by earlier studies which showed that increasing magnesium speeds up depolymerization and increases the lengths of protofilament curls. The use of magnesium here provides the first evidence that work output can be tuned biochemically. This is an important finding. The authors then go on to show that the effect of magnesium on bead deflection can be separated from its effect on depolymerization speed. They do this by proteolytically removing the beta tubulin tail domain, which previous studies had shown to be necessary to mediate the magnesium effect on depolymerization rate. The authors arrive at a conclusion that magnesium must promote protofilament work output by increasing their lengths. How magnesium might do this remains unanswered. The mechanistic insight from the magnesium experiments ends there, but the authors discuss possible roles for magnesium in strengthening longitudinal interactions within protofilaments or perhaps complexing with the GDP nucleotide at the exchangeable site, although that seems less likely at the concentrations in these experiments.

The major conclusion of the study is the finding that work output from curling protofilaments is a tunable system. The examples here demonstrate tuning by tubulin composition and by divalent cations. Whether these examples relate to tuning in biological systems will be an important next question and could expand our appreciation for the versatility of depolymerizing microtubules as a motor.

We fully agree that two very important next questions are whether work output from curling protofilaments is truly harnessed in vivo, and whether protofilament properties in vivo might be actively regulated for this purpose. Based on your recommendations, and as detailed below (under Major point 2), we have expanded our discussion of these possibilities in our revised manuscript.

Reviewer #3 (Public Review):

The authors used a previously established optical tweezers-based assay to measure the regulation of the working stroke of curled protofilaments of bovine microtubules by magnesium. To do so, the authors improved the assay by attaching bovine microtubules to trapping beads through an incorporated tagged yeast tubulin.

The assay is state-of-the-art and provides a direct measurement of the stroke size of protofilaments and its dependence on magnesium.

The authors have achieved all their goals and the manuscript is well written.

The reported findings will be of high interest for the cell biology community.

Thank you for reading and evaluating our manuscript. We are grateful for your positive comments.

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In these paragraphs pathos is used and more specifically this would be part of scare tactics when it comes to the reader realizing that they should take action to lessen addition to gaming after the reader list some ways on how to prevent gaming addiction or lessen addiction.

I think it may be even harder to abandon control than to come up with a new policy sometimes. Introducing regulation for the Internet was not the same as the regulation of other media, and it definitely required extensive discussion and research. However, the fact that Maganizer was able to leave the conference after initiating the discussion demonstrates an important trend of more flexible regulations.

The moral issue I notice is that the overall group which is made up of middle-class caucasian students is having an issue with having a person of color on the board. The reason I came to that decision is because historically they mention that they at times are lenient on the guidelines of having someone override the process to select new members for the team. Everyone seemed to in agreeance that Reuben was a great candidate to make the decision on his own. Reuben selected a candidate that he found social interests in diversity by expressing their involvement in other programs related to diversity. The coalition members also gave Reuben some options but those were not the people he had choose. His choice was Jameela because he was interested in the fact that she was a generational first to go to school, she had interest in women's studies and the LGBTQ committee, and she stated that she wasn't afraid of challenges. I feel like that there may be some closeted angst against diversity even though they are seated on the board. I feel like maybe they feel like having a person of color on the board may be uncomfortable to them as the majority are middle class white kids. For me I think that Reuben was taking part in deontological ethics. This means, "believe that we ought to base our choices on our duty to follow universal truths that we discover through our intuition or reason." (Hackman and Johnson). I feel that Reuben felt that he was doing the right thing based on what his firm beliefs are for their group. He followed through thinking it was the right decision.

Author Response

Reviewer #1 (Public Review):

Auwerx et al. have taken a new approach to mine large existing datasets of intermediary molecular data between GWAS and phenotype, with the aim of uncovering novel insight into the molecular mechanisms which lead a GWAS hit to have a phenotypic effect. The authors show that you can get additional insight by integrating multiple omics layers rather than analyzing only a single molecular type, including a handful of specific examples, e.g. that the effect of SNPs in ANKH on calcium are mediated by citrate. Such additional data is necessary because, as the authors' point out, while we have thousands of SNPs with significant impact on phenotypes of interest, we often don't know at all the mechanism, given that the majority of significant SNPs found through GWAS are in non-coding (and often intergenic) regions.

This paper shows how one can mine large existing datasets to better estimate the cellular mechanism of significant, causal SNPs, and the authors have proven that by providing insight into the links between a couple of genes (e.g. FADS2, TMEM258) and metabolite QTLs and consequent phenotypes. There is definitely a need and utility for this, given how few significant SNPs (and even fewer recently-discovered ones) hit parts of the DNA where the causal mechanism is immediately obvious and easily testable through traditional molecular approaches.

I find the paper interesting and it provides useful insight into a still relatively new approach. However, I would be interested in knowing how well this approach scales to the general genetics community: would this method work with a much smaller N (e.g. n = 500)? Being able to make new insights using cohorts of nearly 10,000 patients is great, but the vast majority of molecular studies are at least an order of magnitude smaller. While sequencing and mass spectrometry are becoming exponentially cheaper, the issue of sample size is likely to remain for the foreseeable future due to the challenges and expenses of the initial sample collection.

We thank the reviewer for his assessment and have now addressed – in the revised version of the manuscript, as well as in the below point-by-point reply – his specific comments/questions.

Reviewer #2 (Public Review):

Auwerx et al. present a framework for the integration of results from expression quantitative trait loci (eQTL), metabolite QTL (mQTL) and genome-wide association (GWA) studies based on the use of summary statistics and Mendelian Randomization (MR). The aim of their study is to provide the field with a method that allows for the detection of causal relationships between transcript levels and phenotypes by integrating information about the effect of transcripts on metabolites and the downstream effect of these metabolites on phenotypes reported by GWA studies. The method requires the mapping of identical SNPs in disconnected mQTL and eQTL studies, which allows MRbased inference of a causal effect from a transcript to a metabolite. The effect of both transcripts and metabolites on phenotypes is evaluated in the same MR-based manner by overlaying eQTL and mQTL SNPs with SNPs present in phenotypic GWA studies.

The aim of the presented approach is two-fold: (1) to allow identification of additional causal relationships between transcript levels and phenotypes as compared to an approach limited to the evaluation of transcript-to-phenotype associations (transcriptome-wide MR, TWMR) and (2) to provide information about the mechanism of effects originating from causally linked transcripts via the metabolite layer to a phenotype.

The study is presented in a very clear and concise way. In the part based on empirical study results, the approach leads to the identification of a set of potential causal triplets between transcripts, metabolites and phenotypes. Several examples of such causal links are presented, which are in agreement with literature but also contain testable hypotheses about novel functional relationships. The simulation study is well documented and addresses an important question pertaining to the approach taken: Does the integration of mQTL data at the level of a mediator allow for higher power to detect causal transcript to phenotype associations?

We thank the reviewer for his/her assessment and have now addressed – in the revised version of the manuscript, as well as in the below point-by-point reply – his/her specific comments/questions.

Major Concerns

1) Our most salient concern regarding the presented approach is the presence of multiple testing problems. In the analysis of empirical datasets (p. 4), the rational for setting FDR thresholds is not clearly stated. While this appears to be a Bonferroni-type correction (p-value threshold divided by number of transcripts or metabolites tested), the thresholds do not reflect the actual number of tests performed (7883 transcripts times 453 metabolites for transcript-metabolite associations, 87 metabolites or 10435 transcripts times 28 complex phenotypes). The correct and more stringent thresholds certainly decrease the overlap between causal relationships and thus reduce the identifiable number of causal triplets. Furthermore, we believe that multiple testing has to be considered for correct interpretation of the power analysis. The study compares the power of a TWMR-only approach to the power of mediation-based MR by comparing "power(TP)" against "power(TM) * power(MP)" (p. 12). This comparison is useful in a hypothetical situation given data on a single transcript affecting a single phenotype, and with potential mediation via a single metabolite. However, in an actual empirical situation, the number of non-causal transcript-metabolite-phenotype triplets will exceed the number of non-causal transcript-phenotype associations due to the multiplication with the number of metabolites that have to be evaluated. This creates a tremendous burden of multiple testing, which will very likely outweigh the increase in power afforded by the mediation-based approach in the hypothetical "single transcript-metabolite-phenotype" situation described here. Thus, for explorative detection of causal transcript-phenotype relationships, the TWMR-only method might even outperform the mediation-based method described by the authors, simply because the former requires a smaller number of hypotheses to be tested compared to the latter. The presented simulation would only hold in cases where a single path of causality with a known potential mediator is to be tested.

We thank the reviewer for pointing out the multiple testing issue. Based on this comment, we have revised our approach by mainly implementing two major modifications to our approach.

First, we reduce the number of assessed metabolites to 242 compounds for which we were able to identify a Human Metabolome Database (HMDB) identifier through manual curation. This was triggered by the suggestion of reviewer #1 to facilitate the database/literature-based follow-up of our discoveries. The motivation is to only test metabolites that if found to be significantly associated would yield interpretable results, thereby reducing the number of tests to be performed. This modification is described in the revised manuscript:

Results: “Summary statistics for cis-eQTLs stem from the eQTLGen Consortium metaanalysis of 19,942 transcripts in 31,684 individuals [3], while summary statistics for mQTLs originate from a meta-analysis of 453 metabolites in 7,824 individuals from two independent European cohorts: TwinsUK (N = 6,056) and KORA (N = 1,768) [6]. After selecting SNPs included in both the eQTL and mQTL studies, our analysis was restricted to 7,884 transcripts with ≥ 3 instrumental variables (IVs) (see Methods, Supplemental Figure 1) and 242 metabolites with an identifier in The Human Metabolome Database (HMDB) [28] (see Methods, Supplemental Table 1).”

Methods: “mQTL data originate from Shin et al. [6], which used ultra-high performance liquid chromatography-tandem mass spectrometry (UPLC-MS/MS) to measure 486 whole blood metabolites in 7,824 European individuals. Association analyses were carried out on ~2.1 million SNPs and are available for 453 metabolites at the Metabolomics GWAS Server (http://metabolomics.helmholtz-muenchen.de/gwas/). Among these metabolites, 242 were manually annotated with Human Metabolome Database (HMDB) identifiers (Supplemental Table 1) and used in this study.”

Second, to account for all remaining tests, we now select significant causal effects based on FDR < 5% in all performed univariable MR analyses. With 5% FDR on both the transcript-to-metabolite and metabolite-to-phenotype effects, the FDR for triplets is slightly inflated to 9.75% (= 1-0.952), a consideration that we now explicitly describe. Note that selecting triplets based on transcript-tometabolite and metabolite-to-phenotype effects FDR < 2.5%, result in a FDR < 5% (1-0.9752) for the triplets. This more stringent threshold identifies 135 causal triplets, 39 of which would be missed by TWMR. Overall, Results and Supplemental Tables have been updated and now read as follow:

“Mapping the transcriptome onto the metabolome […] By testing each gene for association with the 242 metabolites, we detected 96 genes whose transcript levels causally impacted 75 metabolites, resulting in 133 unique transcriptmetabolite associations (FDR 5% considering all 1,907,690 instrumentable gene-metabolite pairs Supplemental Table 2) […].

Mapping the metabolome onto complex phenotypes […] Overall, 34 metabolites were associated with at least one phenotype (FDR 5% considering all 1,344 metabolite-phenotype pairs), resulting in 132 unique metabolitephenotype associations (Supplemental Table 4).

Mapping the transcriptome onto complex phenotypes […] In total, 5,140 transcripts associated with at least one phenotype (FDR 5% considering all 292,170 gene-phenotype pairs) resulting in 13,141 unique transcript-phenotype associations (Supplemental Table 5).

Mapping metabolome-mediated effects of the transcriptome onto complex phenotypes […] We combined the 133 transcript-metabolite (FDR ≤ 5%) and 132 metabolite-trait (FDR ≤ 5%) associations to pinpoint 216 transcript-metabolite-phenotype causal triplets (FDR = 1-0.952 = 9.75%) (Supplemental Table 6).”

In the simulations performed for the power analysis, we used a Bonferroni correction. We ran each simulation for 500 transcripts, measuring 80 metabolites at each run and performed TWMR and MWMR. The power of TWMR was calculated by counting how many times we obtain p-values ≤ 0.05/500. The power of the mediation analysis was calculated as 𝑝𝑜𝑤𝑒𝑟"$ ∗ 𝑝𝑜𝑤𝑒𝑟$#, where 𝑝𝑜𝑤𝑒𝑟"$ was calculated by counting how many times we obtain p-values ≤ 0.05/(500*80), and 𝑝𝑜𝑤𝑒𝑟$# was calculated by counting how many times we obtain p-values ≤ 0.05/80. In the revised manuscript, we additionally repeated each simulated scenario 10 times to increase robustness of results. This has been clarified in both the Methods and Results sections of the revised manuscript:

Methods: “Ranging 𝜌 and 𝜎 from -2 to 2 and from 0.1 and 10, respectively, we run each simulation for 500 transcripts measuring 80 metabolites at each run and performed TWMR and MWMR starting from above-described 𝛽7<"=, 𝛽4<"= and 𝛽>?,(. For each MR analysis we calculated the power to detect a significant association as well as the difference in power between TWMR and the mediation analyses (i.e., 𝑝𝑜𝑤𝑒𝑟"# − 𝑝𝑜𝑤𝑒𝑟"$ ∗ 𝑝𝑜𝑤𝑒𝑟$#). Each specific scenario was repeated 10 times and the average difference in power across simulation was plotted as a heatmap.”

Results: “To characterize the parameter regime where the power to detect indirect effects is larger than it is for total effects, we performed simulations using different settings for the mediated effect. In each scenario we evaluated 500 transcripts and 80 metabolites and varied two parameters characterizing the mediation: a. the proportion (𝜌) of direct (𝛼!) to total (𝛼"#) effect (i.e., effect not mediated by the metabolite) from -2 to 2 to cover the cases where direct and mediated effect have opposite directions (51 values); b. the ratio (𝜎) between the transcript-to-metabolite (𝛼"$) and the metabolite-to-phenotype (𝛼$#) effects, exploring the range from 0.1 to 10 (51 values).<br /> Transcripts were simulated with 6% heritability (i.e., median ℎ@ in the eQTLGen data) and a causal effect of 0.035 (i.e., ~65% of power in TWMR at a = 0.05) on a phenotype. Each scenario was simulated 10 times and results were averaged to assess the mean difference in power (see Methods).”

2) A second concern regards the interpretation of the results based on the empirical datasets. For the identified 206 transcript-metabolite-phenotype causal triplets, the authors show a comparison between TWMR-based total effect of transcripts on phenotypes and the calculated direct effect based on a multivariable MR (MVMR) test (Figure 2B), which corrects for the indirect effect mediated by the metabolite in the causal triplet. The comparison shows a strong correlation between direct and total effect. A thorough discussion of the potential reasons for deviation (in both negative and positive directions) from the identity line is missing.

Deviation from the identity line, as observed in Figure 2B, indicates that while there is a strong correlation between direct and total effect, it is not perfect, and part of the total effect is due to an indirect effect mediated by metabolites. This is explained and discussed in the Results and Discussion section:

Results: “Regressing direct effects (𝛼!) on total effects (𝛼"#) on (Figure 2A), we estimated that for our 216 mediated associations, 77% [95% CI: 70%-85%] of the transcript effect on the phenotype was direct and thus not mediated by the metabolites (Figure 2B).”

Discussion: “The observation that 77% of the transcript’s effect on the phenotype is not mediated by metabolites suggests that either true direct effects are frequent or that other unassessed metabolites or molecular layers (e.g., proteins, post-translational modifications, etc.) play a crucial role in such mediation. It is to note that in the presence of unmeasured mediators or measured mediators without genetic instruments, our mediation estimates are lower bounds of the total existing mediation. […] Thanks to the flexibility of the proposed framework, we expect that in the future and upon availability of ever larger and more diverse datasets, our method could be applied to estimate the relative contribution of currently unassessed mediators in translating genotypic cascades.”

Furthermore, no test of significance for potential cases of mediation is presented. Due to the issues of multiple testing discussed above, the significance of the inferred cases of mediation is drawn into question. The examples presented for causal triplets (involving the ANKH and SLC6A12 transcripts) feature transcripts with low total effects and a small ratio between direct and total effect, in line with the power analysis. However, in these examples, the total effects are also quite low. Its significance has to be tested with an appropriate statistical test, incorporating multiple testing correction.

Following the reviewer’s suggestion, we have modified our criteria to call significant associations to account for multiple testing (see extensive reply to major concern #1). With 5% FDR on both the transcript-to-metabolite and metabolite-to-phenotype effects, the FDR for triplets is slightly inflated to 9.75% (= 1-0.952). We mention this limitation in the revised manuscript:

“We combined the 133 transcript-metabolite (FDR ≤ 5%) and 132 metabolite-trait (FDR ≤ 5%) associations to pinpoint 216 transcript-metabolite-phenotype causal triplets (FDR = 1-0.952 = 9.75%) (Supplemental Table 6).”

All examples presented in the original manuscript remained significant. The fact that the total effect in these examples is low makes them particularly interesting as it highlights how our approach can detect biologically plausible associations between a transcript and a phenotype that only show mild evidence through TWMR but are strongly supported when accounting for metabolites that mediate the transcript-phenotype relation, showcasing situations in which our method can provide a true advantage over classical approaches such as TWMR. Such examples may emerge due to opposite signed direct and indirect effects, which cancel each other out when it comes to testing total effects. What is key that we do not claim the total and the mediated effects to be different (as we would have very limited power to do so), but simply point out that under certain settings we are better powered to detect mediated effects than total ones. In the ANKH example (more details below), the total ANKH-calcium effect is almost exactly the same as the product of the 𝛼,-.%→056157 and 𝛼056157→0120*34 effects, simply the latter ones are detectable, while the total effect is not.

In the revised manuscript the case for our selected examples is made even stronger thanks to an analysis proposed by Reviewer #1 that aimed at estimating the proportion of previously reported associations through automated literature review. For instance, while our literature review found previously reported evidence of the ANKH-calcium link and of the ANKH-citrate link, we did not identify any publication mentioning all 3 terms in combination in the abstract and/or title, illustrating how our approach can establish bridges between knowledge gaps. We revised the Results section describing the ANKH example accordingly:

“The 126 triplets that were not identified through TWMR due to power issues represent putative new causal relations. This is well illustrated by a proof-of concept example involving ANKH [MIM: 605145] and calcium levels, for which 48 publications were identified through automated literature review (Supplemental Table 6). While the TWMR effect of ANKH expression on calcium levels was not significant (𝛼,-.%→012034 = −0.02; 𝑃 = 0.03), we observed that ANKH expression decreased citrate levels (𝛼,-.%→056157 = −0.30; 𝑃 = 2.2 × 1089:), which itself increased serum calcium levels (𝛼056157→012034 = 0.07; 𝑃 = 6.5 × 108;9). Mutations in ANKH have been associated with several rare mineralization disorders [MIM: 123000, 118600] [32] due to the gene encoding a transmembrane protein that channels inorganic pyrophosphate to the extracellular matrix, where at low concentrations it inhibits mineralization [33]. Recently, a study proposed that ANKH instead exports ATP to the extracellular space (which is then rapidly converted to inorganic pyrophosphate), along with citrate [34]. Citrate has a high binding affinity for calcium and influences its bioavailability by complexing calcium-phosphate during extracellular matrix mineralization and releasing calcium during bone resorption [35]. Together, our data support the role of ANKH in calcium homeostasis through regulation of citrate levels, connecting previously established independent links into a causal triad.”

Furthermore, the analysis of the empirical data indicates that the ratio between direct and indirect effect of a transcript on a phenotype is in most cases close to identity, except for triplets with low total effects. This fact should be considered in the power analysis, which assigned the highest gain in power by the mediation analysis to cases of low direct to total effect ratio. The empirical data indicate that these cases might be rare or of minor relevance for the tested phenotypes.

As our previous power analyses did not fully reflect scenarios observed from empirical data, we extended the range of covered 𝜌 (i.e., the ratio between direct and total effect), so that it mimics more closely the observed range of 𝜌. In the revised manuscript, 𝜌 varies from -2 to 2, so that we also consider configurations where direct and total effects have opposite direction. To provide the readers with a rough idea how frequent the different parameter combinations occur in real data, we now provide another heatmap indicating the density of detected associations in those parameter regimes as Supplemental Figure 4.

This map can be brought in perspective of Figure 4A that illustrates the power of TWMR vs. mediation analysis over the same range of parameter settings.

It becomes apparent from Supplemental Figure 4 that in real data, 𝜎 is always larger than 1 and often exceeds 10. Note, however, that this heatmap must be interpreted with care, since the “detected” density will be low in regions where both methods have low power.

3) Related to the interpretation of causal links: horizontal pleiotropy needs to be considered. The authors report the identification of causal links between TMEM258, FADS1 and FADS2, arachidonic acid-derived lipids and complex phenotypes. However, they also mention the high degree of pleiotropy due to linkage disequilibrium at the underlying eQTL and mQTL region as well as the network of over 50 complex lipids known to be associated with the expression of the above transcripts. Thus, it seems possible that the levels of undetected lipid species may be more important for the phenotypic effect of variation in these transcripts and that the reported "mediators" are rather covariates. Such horizontal pleiotropy would violate a basic assumption of the MR approach. While we think that this does not invalidate the approach altogether, it does affect the interpretation of specific metabolites as mediators. This is aggravated by the fact that metabolic networks are more tightly interconnected than macromolecular interaction networks (assortative nature of metabolic networks) and that single point-measurements of metabolites may not be generally informative about the flux through a specific metabolic pathway.

This is a valid point and we discuss this limitation in the revised Discussion:

“It is to note that in the presence of unmeasured mediators or measured mediators without genetic instruments, our mediation estimates are lower bounds of the total existing mediation. In addition, unmeasured mediators sharing genetic instruments with the measured ones, can modify result interpretation as some of the observed mediators may simply be correlates of the true underlying mediators. While this is a limitation of all MR methods, metabolic networks may harbor particularly large number of genetically correlated metabolite species.”

Reviewer #2 (Public Review):

Auwerx et al. present a framework for the integration of results from expression quantitative trait loci (eQTL), metabolite QTL (mQTL) and genome-wide association (GWA) studies based on the use of summary statistics and Mendelian Randomization (MR). The aim of their study is to provide the field with a method that allows for the detection of causal relationships between transcript levels and phenotypes by integrating information about the effect of transcripts on metabolites and the downstream effect of these metabolites on phenotypes reported by GWA studies. The method requires the mapping of identical SNPs in disconnected mQTL and eQTL studies, which allows MR-based inference of a causal effect from a transcript to a metabolite. The effect of both transcripts and metabolites on phenotypes is evaluated in the same MR-based manner by overlaying eQTL and mQTL SNPs with SNPs present in phenotypic GWA studies.

The aim of the presented approach is two-fold: (1) to allow identification of additional causal relationships between transcript levels and phenotypes as compared to an approach limited to the evaluation of transcript-to-phenotype associations (transcriptome-wide MR, TWMR) and (2) to provide information about the mechanism of effects originating from causally linked transcripts via the metabolite layer to a phenotype.

The study is presented in a very clear and concise way. In the part based on empirical study results, the approach leads to the identification of a set of potential causal triplets between transcripts, metabolites and phenotypes. Several examples of such causal links are presented, which are in agreement with literature but also contain testable hypotheses about novel functional relationships. The simulation study is well documented and addresses an important question pertaining to the approach taken: Does the integration of mQTL data at the level of a mediator allow for higher power to detect causal transcript to phenotype associations?

Major Concerns<br /> 1. Our most salient concern regarding the presented approach is the presence of multiple testing problems. In the analysis of empirical datasets (p. 4), the rational for setting FDR thresholds is not clearly stated. While this appears to be a Bonferroni-type correction (p-value threshold divided by number of transcripts or metabolites tested), the thresholds do not reflect the actual number of tests performed (7883 transcripts times 453 metabolites for transcript-metabolite associations, 87 metabolites or 10435 transcripts times 28 complex phenotypes). The correct and more stringent thresholds certainly decrease the overlap between causal relationships and thus reduce the identifiable number of causal triplets. Furthermore, we believe that multiple testing has to be considered for correct interpretation of the power analysis. The study compares the power of a TWMR-only approach to the power of mediation-based MR by comparing "power(TP)" against "power(TM) * power(MP)" (p. 12). This comparison is useful in a hypothetical situation given data on a single transcript affecting a single phenotype, and with potential mediation via a single metabolite. However, in an actual empirical situation, the number of non-causal transcript-metabolite-phenotype triplets will exceed the number of non-causal transcript-phenotype associations due to the multiplication with the number of metabolites that have to be evaluated. This creates a tremendous burden of multiple testing, which will very likely outweigh the increase in power afforded by the mediation-based approach in the hypothetical "single transcript-metabolite-phenotype" situation described here. Thus, for explorative detection of causal transcript-phenotype relationships, the TWMR-only method might even outperform the mediation-based method described by the authors, simply because the former requires a smaller number of hypotheses to be tested compared to the latter. The presented simulation would only hold in cases where a single path of causality with a known potential mediator is to be tested.

2. A second concern regards the interpretation of the results based on the empirical datasets. For the identified 206 transcript-metabolite-phenotype causal triplets, the authors show a comparison between TWMR-based total effect of transcripts on phenotypes and the calculated direct effect based on a multivariable MR (MVMR) test (Figure 2B), which corrects for the indirect effect mediated by the metabolite in the causal triplet. The comparison shows a strong correlation between direct and total effect. A thorough discussion of the potential reasons for deviation (in both negative and positive directions) from the identity line is missing. Furthermore, no test of significance for potential cases of mediation is presented. Due to the issues of multiple testing discussed above, the significance of the inferred cases of mediation is drawn into question. The examples presented for causal triplets (involving the ANKH and SLC6A12 transcripts) feature transcripts with low total effects and a small ratio between direct and total effect, in line with the power analysis. However, in these examples, the total effects are also quite low. Its significance has to be tested with an appropriate statistical test, incorporating multiple testing correction. Furthermore, the analysis of the empirical data indicates that the ratio between direct and indirect effect of a transcript on a phenotype is in most cases close to identity, except for triplets with low total effects. This fact should be considered in the power analysis, which assigned the highest gain in power by the mediation analysis to cases of low direct to total effect ratio. The empirical data indicate that these cases might be rare or of minor relevance for the tested phenotypes.

3. Related to the interpretation of causal links: horizontal pleiotropy needs to be considered. The authors report the identification of causal links between TMEM258, FADS1 and FADS2, arachidonic acid-derived lipids and complex phenotypes. However, they also mention the high degree of pleiotropy due to linkage disequilibrium at the underlying eQTL and mQTL region as well as the network of over 50 complex lipids known to be associated with the expression of the above transcripts. Thus, it seems possible that the levels of undetected lipid species may be more important for the phenotypic effect of variation in these transcripts and that the reported "mediators" are rather covariates. Such horizontal pleiotropy would violate a basic assumption of the MR approach. While we think that this does not invalidate the approach altogether, it does affect the interpretation of specific metabolites as mediators. This is aggravated by the fact that metabolic networks are more tightly interconnected than macromolecular interaction networks (assortative nature of metabolic networks) and that single point-measurements of metabolites may not be generally informative about the flux through a specific metabolic pathway.

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

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

Summary<br /> The authors have set out to study the Drosophila immune response against the fungus Aspergillus fumigatus. They found that Aspergillus fumigatus kills Drosophila Toll pathway mutants. The fungus does this without invasion because its dissemination is blocked by melanization. They suggest that there is a role for Toll in host defense distinct from resistance. The findings are interesting, and looks like the mycotoxins play a role. It also seems that there is some role of the Bomanins here, but I find that in particular Figure4 experiments are not convincing enough to provide a mechanistic insight as to what is going on. I think the authors need to think through what their results mean, and also, explain better (especially regarding Fig 4) their ideas and how the data fits them.

We thank the reviewer for scrutinizing our manuscript as well as for suggestions to improve it.

The role of mycotoxins is demonstrated:

i) the fungus does not proliferate nor disseminate, also in Toll pathway mutant flies: thus, it must kill through diffusible substances, in as much as these immuno-deficient flies exhibit tremors toward the end of the infection;

ii) a fungal strain devoid of the capacity to produce secondary metabolites is no longer virulent, even in Toll pathway mutant flies.

The role of Bomanins is also demonstrated: the finding of a susceptibility of Bom__D__55C deletion flies to A. fumigatus and to mycotoxin challenges clearly shows that at least one or several Bomanin genes are required in the host defense against these challenges. The observation that this susceptibility can be rescued by the genetic overexpression of specific Bomanins indicates which ones are likely to mediate protection. The novel data we have included with the protection from mycotoxin action in neurons point clearly to BomS6 being the major mediator of protection against verruculogen action since it is the only one of two Bom genes to be induced in the head and with a proven potential for rescue of the Bom__D__55C phenotype.

As regards the concept of the article, it is simple: we show that the Toll pathway does not control A. fumigatus infection by directly attacking the fungus but does so by neutralizing the effects of secreted virulence factors such as restrictocin and verruculogen. We further identify some of the relevant effectors such as Bomanins by using a genetic complementation strategy. To make our point clearer, we have now included additional data in which we show that BomS6 and BomS4 are the only Bomanins induced in the head of flies upon the injection of these two toxins. We next determine that BomS6 and not BomS4 expression in the nervous system dominantly protects the flies from the deleterious effects of verruculogen injection, both in terms of recovery from tremors and survival. Mechanistically, the Toll pathway protects the host from the action of verruculogen by expressing and likely secreting BomS6 from neurons.

Major comments:<br /> Page 5: .."the fungal burden did not increase much in MyD88 flies challenged with 50 conidia (Fig. 1B)" - What do you mean did not increase much? There is a clear increase in Myd88 mutants compared to controls; would you expect a bigger increase (e.g. log scale induction)? Explain.

When the injected dose is higher than 50 injected colonies, the fungal burden remains very close to that of the injected inoculum (Fig. EV1_F, J_). As for other pathogens regulated by the Toll pathway, it has been published that the microbial burden increases by log factors for filamentous fungi (Huang et al.., in revision), pathogenic yeasts (e.g., work from our laboratory Quintin et al. Journal of Immunology, 2013), bacteria (e. g., Duneau et al., eLife 2017; Huang et al., in revision). The pathogens usually proliferate exponentially in immuno-deficient hosts, which is clearly not the case of A. fumigatus, the first example we know of.

Page 6: "the SPZ/Toll/MyD88 cassette is required for host defense against A. fumigatus infections, even though this pathogen only mildly stimulates the Toll pathway." - Should you rather say that A. fumigatus only mildly induces the Toll pathway target gene Drosomycin?

The answer is negative. Fig. EV1_C_ clearly shows that BomS1 is also modestly induced as compared to an infection with E. faecalis. The promoter of BomS1 contains a canonical Dif-response element (Busse et al., EMBO J., 2007_)_. For a more thorough discussion of this point, please, see reply to Reviewer 2, Major Comment 2.

Page 6: "...we tested Hayan mutant flies defective for this arm of innate immunity (Nam et al., 2012)." - elaborate this, which arm/which pathway?

The title of the paragraph is “Drosophila melanization curbs A. fumigatus invasion”. The full first sentence of the paragraph actually read: “As melanization is a host defense of insects effective against fungal infections, we tested Hayan mutant flies defective for this arm of innate immunity”.

This has not been introduced in the introduction. Explain.

We have now added a couple of lines (82-83) to introduce melanization for the nonspecialist reader.

Can you really draw this conclusion: "We conclude that melanization limits the proliferation and the dissemination of A. fumigatus injected into wild-type flies yet does not eradicate it at the injection site, where a melanization plug forms." Maybe you can based on the function/importance of the pathway to melanization, but you need to explain.

Melanization is mediated by the Hayan protease and three phenol oxidases (two in adults) that catalyze the enzymatic reactions leading to melanin production (for Drosophila, please see Nam et al. EMBO J. (2012), Bingelli et al., PLoS Pathogen (2014), Dudzic et al., BMC Biology (2015), Cell Reports, 2019). Thus, finding that there is an increased proliferation and dissemination in null Hayan mutants is a strong indication for a role of melanization. The identification of a similar phenotype for PPO2 and PO1-PPO2 mutants demonstrates that melanization is curbing A. fumigatus. Our sentence is therefore fully justified.

Page 10: "The cleavage of the 18S RNA was however much less pronounced in wild-type flies as compared to MyD88" - I am not sure what this means. Do you mean 28S?

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

And that the 28S peak is lower? Is this a quantitative method?

The technique is liquid electrophoresis on a microchip. It is both a qualitative and quantitative technique that replaces traditional agarose or polyacrylamide gels.

Fig. legend: "Arrows show the position of the 28S RNA sarcin fragment" - there are three arrows in both Fig 4E and F; specify which arrows point what.

The thick arrow is now indicated in the figure legend to correspond to the much smaller sarcin fragment whereas the thin arrows on the graph clearly specify the position of the 28S RNA peaks.

Based on the results, I am not convinced about the conclusion, that "restrictocin is able to inhibit translation to a detectable degree in vivo, likely through the cleavage of the ribosomal 28S a-sarcin/ricin loop as described in vitro." <- Do you draw this conclusion before doing the actual in vitro experiment, which is described next in the text (The rabbit reticulocute assay, S2 cells)?

The existing literature (line 259 for a few selected references) has largely proven that restrictocin cleaves 28S RNA in vitro. We are demonstrating that this also happens in vivo in flies based on the generation of the alpha-sarcin fragment as well as the decreased 28S peaks. Our transgenic approach also indicates that restrictocin blocks translation in vivo. The in vitro approach has been implemented so that we could test the effect of synthetic BomS1 and BomS3 in cell culture. As to our knowledge, no one had demonstrated that restrictocin blocks translation in Drosophila cultured cells. It was therefore important to demonstrate it in cell culture using well-characterized in vitro techniques mastered by AT and FM.

4H: Not sure what should be seen here, is it the darkest band at 0 uM that disappears?

We have improved the figure and added an arrow to point out to the relevant band on the gel.

HI & J need more explanation than what is now included in the text or Figure legend, is the conclusion that there is no difference? Write the stats above the Figs 4I & J (n.s.?).

We have added NS on the figures and made our conclusion clearer (lines 295-298).

Minor comments:

It would have helped commenting if the manuscript contained line numbers

We apologize for having initially provided a version in which lines were not numbered. At the prompting of Review Commons we immediately provided such a version, that was actually used by Reviewer 2.

Why do you have the title "Hayan" on top of Fig 1F; you don't have this marking system in the other survival curves

This point has now been addressed and the survival experiments checked for consistency.

Fig 2A: Can you speculate why MyD88 flies die rapidly at day 10 if you inject PBST (your control)? What would happen to uninjected controls in otherwise the same conditions? (you could include an uninjected control here?)

We suspect that this is linked to the trauma induced by the injection. Trauma has been shown to impact the homeostasis of the midgut epithelium (Lee & Miura, Current Topics Developmental Biology 2014, Chakrabarti et al., PLoS Genetics (2016)), and we suspect that it may lead to a leakiness of the gut allowing the passage of some bacteria from the gut microbiota that can proliferate in the hemocoel. Hence, we checked axenic and antibiotics-treated MyD88 flies to exclude that the limited sensitivity to trauma was not significantly contributing to the phenotypes we describe. It is also linked to the thickness of the needle and the problem is alleviated by using thinner needles.

The uninjected control is now shown in Fig. EV8_E_.

Please, see also the answer to Reviewer 2 Major comment 1.

Fig 2E: Not sure what would be the best way of presenting the curves - different colors, dotted lines or something? Now if there are too many lines, they are hard to tell apart. because the symbols are not that visible. Like in 2E if you want to compare the light red/orange colored lines.

We agree with the reviewer that the lines are hard to tell apart. This is however not a significant issue since the glip mutants display curves similar to that of the wt A. fumigatus control strain.

For consistency add the caption also to Fig 3D (I assume it is the same as 3C)

The caption was present in our version and is present in the revised version.

For consistency, should you add Verruculogen on top of Fig 3F?

Same reply as for the previous comment.

Chronologically, how it is explained in the text, Figs 4A and B are in the wrong order.

We fully agree with the reviewer. This problem has been addressed in the revised version.

The quality of Fig 4 is not great, the text is hard to read (too small) and becomes blurry upon magnification.

We fully agree with the reviewer. This problem has been addressed in the revised version.

Page 12; "These data then suggest that a process akin to the immune surveillance of core cellular processes first described in C. elegans may also exist in Drosophila" - I think this sentence belongs to the discussion, this is not directly drawn from the results.

We have followed the reviewer suggestion and have now developed our Discussion paragraph now entitled “Induction of the expression of specific Bomanin genes upon mycotoxin challenge”

Referees cross-commenting

I think we share many thoughts among all the reviewers.

The main problem is that the manuscript language is quite strong; from the results many times it is not ok to make such strong statements. Some experiments need further analysis and clarification.

I think in most cases, this could be achieved by softening the statements and adding more discussion, and not by making new experiments (some may be needed).

We respectfully disagree with the reviewer on this point. There were obviously some misunderstandings that might be traced to the short format of the initial version. We have now developed the Discussion to clarify our conclusions as suggested by the reviewer.

Minor things are that experiments are not advancing in a logical order between the text and the figures and there are problems with resolution in some figures.

Statistics in some figures needs to be added.

Please, see above.

Reviewer #1 (Significance):

The nature of the work is conceptual for the field, to understand the role of the Toll pathway and Bomanins in particular, in this fungal infection model. The work is interesting to a somewhat limited audience, mainly immunologists and in particular, people interested in the Drosophila model for immunity. The work may be interesting conceptually in understanding fungal infections.

We are not certain that immunologists represent a limited audience. We agree that work on fungal infections is insufficiently funded with respect to the medical importance of these infections, as highlighted in our introduction and Perspective section of the Discussion.

My expertise: I am a Drosophila immunity researcher with nearly 20 years of experience in working with fly immunity, in particular the Toll and the Imd pathways.

Reviewer #2 (Evidence, reproducibility and clarity):

Summary:

Xu et al. describe how A. fumigatus kills Toll-deficient fruit flies not by hyperproliferation, but more likely by virulence factors. Melanization is important for suppressing fungal spread. The Bomanin genes have an unknown function, and here the data suggest a reasonably convincing role for Toll in resilience. Overall the manuscript is thorough and presents a diversity of approaches that show Toll and the Bomanins in particular contribute to this resilience effect. The idea that Toll effectors are essential for resilience is interesting as other fly stress response pathways like JAK-STAT are better known for helping the fly cope with damages, while Toll is better known as an antifungal response.

I believe the study, with some careful considerations added, would add a valuable series of observations to understanding how the host immune system promotes survival after infection. Overall I am quite positive about the results, and the authors have made a significant effort.

We thank the reviewer for the positive evaluation of our work that actually spans many years of research on the Aspergillus fumigatus Drosophila infection model that is a major topic of our work at the Sino-French Hoffmann Institute of Guangzhou Medical University.

Any experiment suggestions I make are strictly to improve the confidence in the interpretations of the results, but the language could alternately be softened to address those concerns. My major critique is that the authors repeatedly extend beyond what is shown, and occasionally in defiance of what is shown (if I understand the results correctly).

We have chosen to perform additional experiments when needed. We have also clarified points where there were obvious misunderstandings by expanding our text that had been written under a very concise format.

It is not thoroughly clear what the reviewer has in mind when using the word defiance. We suppose it refers to the work of Scott Lindsay with whom we are in contact. He actually attempted to monitor the C. glabrata burden but did not pursue this line of investigations as he already saw a difference after one hour and he thought that the Toll pathway cannot be induced so rapidly. Actually, David Duneau mentions a time of two to three hours for the Toll pathway to control E. faecalis infections (eLife, 2017) and Sandrine Uttenweiler-Joseph already saw by MALDI-TOF MS an induction of Bomanins and other DIMs at the earliest point tested, six hours (PhD thesis). There is absolutely no critique of the work of the Wasserman laboratory who has greatly contributed to our understanding of Bomanin functions. Some of our unpublished data clearly point out to an AMP role for at least one Bomanin gene against E. faecalis and we certainly do not exclude an AMP role for BomS against C. glabrata. This however does not dismiss the possibility that Bomanins may also have other roles in dealing with microbial toxins. We have been studying Candida infections in Drosophila for many years and have documented the host defense against C. glabrata (Quintin et al., JI, 2013). We do suspect that C. glabrata likely secretes virulence factors that have not been identified so far. We mention this as a possibility and certainly not as a truth. One should remember that investigators were unaware for a long period of the role of Candidalysin, a pore-forming toxin, in C. albicans infections.

Finally, a dual role as AMP and protecting from secreted toxins has been clearly shown in the case of alpha-mammalian Defensins that we now are describing in our Revised Discussion (Kudryashova,Immunity, 2014).

Comments below.

Major comments:

1) The language is too strong. Specifically the use of the phrase "anti-toxin" is too generalist, especially as the authors show that their candidate Bomanin does not bind to the toxin directly.

We have checked all of the submitted documents: the term anti-toxin was never used (just found “anti” in antimicrobial, antifungal, antibiotics..), in this manuscript as well as in the companion article. and we have never excluded an indirect effect, quite to the contrary because of the in vitro experiment with restrictocin mentioned by the reviewer and other observations now included (see further below). We use the terms “protection” or “counteract”, which have not such a meaning. It is burdensome for the reader to read each time “counteract or protect from the actions of the toxins or the effects of the toxin.

Instead, Toll mutants seem susceptible to damage/stress caused by injury/toxins. MyD88 even show general susceptibility to vehicle controls in Fig3C-D.

The effects of stress related to the infection conditions and injury are clearly distinct from the much stronger ones exerted by the toxins themselves. As requested by the reviewer further below, we have submitted wild-type and immuno-deficient flies to several stresses such as heat or the injection of hydrogen peroxide or salt solution (Fig. EV8_B-E_). While the latter did not reveal any difference, MyD88 flies succumbed slightly faster to a strong 37°C stress; in contrast, they survived better to a 29°C exposure, the temperature at which we perform most experiments. However, the difference started to be visible only after some 15 days whereas the time frame in which flies succumb to A. fumigatus or toxin challenges is definitely much shorter by some 10 days. We also note that Bom__D__55C mutant flies behave like the isogenized wild-type controls in these assays, further excluding a potential role for general stress sensitivity as a contributor to the effect of toxins.

As regards DMSO, there is indeed a general mild sensitivity of flies to DMSO, but not specifically affecting MyD88 mutant (Rebuttal Fig. 1J). We find that this effect is lessened when using thinner needles. Thus, the problem has become minor as we became more experienced. We had checked axenics- and antibiotics-treated flies to exclude a contribution from the microbiota. Finally, to uncouple the effects of verruculogen from those of DMSO, we have also challenged flies directly by introducing the powder, using a technique similar to that of the septic injury. While it is quantitatively less accurate, it clearly proves that verruculogen produces the reported effects (Fig. 3C) and was useful to measure Bom and Drosomycin expression by digital PCR in the heads of challenged flies, e.g., Fig. EV6_J-K_ and Figs EV_11&12_.

Toll is important for development, so it may be expected that Toll flies could have development defects impacting resilience even if/when Toll flies can survive to adulthood. I don't say this to be too negative on the findings, which are quite convincing. But I am not sure that the phrase "anti-toxin" is right for what is shown.

We fully agree with the reviewer on this point. We have failed to find RNAi lines that are efficient enough to mimic the Toll pathway phenotype when expressed ubiquitously at the adult stage. However, Bom__D__55C mutants do not seem to display a developmental phenotype and display a phenotype similar to that of MyD88 flies. Furthermore, our rescue experiments of the Bom__D__55C sensitivity phenotype to mycotoxin challenge is achieved by the overexpression of specific Boms that are induced only at the adult stage, making it unlikely that this sensitivity phenotype reflects a developmental problem, as had been shown to be the case for 18-wheeler that had initially been proposed to encode the IMD pathway receptor.

A very interesting recent study shows Dif has a role in the synapse of neurons to protect from alcohol sensitivity. Could secreted Bomanins participate? This emphasizes a mechanism through which Toll mutants likely have defective neural development, which could make them stress response defective, especially to things like neurotoxins. See: https://pubmed.ncbi.nlm.nih.gov/35273084/

We are aware of this study first presented at the 2019 Fly Meeting in Dallas and this author did discuss with the authors of the study. However, we have found that Dif (and Dorsal) mutants are not sensitive to A. fumigatus infections nor to injected mycotoxins, as was the case already for C. glabrata (Quintin et al., JI, 2013).

Lin et al. (2019) also showed lack of Bomanin secretion from the fat body in Bombardier mutants causes loss of tolerance (resilience?). So does Bomanin disruption increase susceptibility to stresses more generally, rather than specifically fungal toxins? And is this a development role, rather than an immune response role?

The authors could try to use other stresses (NaCl, oxygen, heat, alcohol) to test the contribution of Bomanins to this resilience, which may reflect defective neural development rather than a role for secreted systemic immune-response peptides.

Please, see replies above.

2) The authors present a paradox. On the one hand, A. fumigatus hardly induces Drs/Bomanins (Fig. S1). Yet on the other, they propose that inducible Bomanins protect the fly from mycotoxins. Why do the authors say Toll is hardly induced by A. fumigatus at the start of the study (Fig S1), but later use the same data to argue that Bomanin induction underlies the resilience phenotype (Fig5).

The reviewer raises an interesting point. Of note, we have added new data in Fig. EV2_B_ that document that all 55C Bomanin genes, BomS4-_excepted, are induced by a systemic infection. There is indeed somewhat of a paradox. The _Bom__D__55C deletion phenotype clearly establishes that Bomanins play a major role in the protection against mycotoxins and A. fumigatus. The rescue experiments rely on ectopic expression and therefore establish that specific Bomanins can mediate the protective effect. Our data on verruculogen suggest that there might be local inductions, e. g., in the head of BomS6 and BomS4. The brain represents a compartment that is separated from the hemocoel by the blood-brain-barrier. We have not been able to generate BomS6 null mutants so far. In this case, the relevant response may not be systemic. We only detect a weak signal for BomS peptides in the hemolymph of unchallenged flies, making it unlikely that a basal expression is important, at least as regards a systemic infection. We cannot however exclude local inductions at the level of tissues. This would not rely on hemocytes as “hemoless” flies are not susceptible to A. fumigatus or toxin challenges. This topic definitely warrants further investigations.

In Fig 5, it looks like DMSO is nearly identical to A. fumigatus, so can the authors really suggest that equal induction to DMSO is relevant?

We had stated that an induction of the Bomanins by the injection of DMSO alone precluded us from analyzing the effects of verruculogen on Bom gene expression. We have now bypassed this difficulty through direct challenges by the undissolved powder (Fig. 6_J-K,_ Fig. EV11).

The authors' discussion of these points would benefit from considering Vaz et al. (2019; Cell Rep) to frame how much PAMP is injected given equal numbers of fungal cells vs. bacterial cells. To me the lower induction by injecting a few fungal cells with much lower surface area to volume ratio means equal microbe mass has exponentially less PAMP in fungal conidia cell walls (2-3um diameter) vs. equal mass of bacteria (0.5-1um diameter).

We fully agree with the reviewer and now mention that C. glabrata also led to a milder induction of the Toll-mediated humoral response (Quintin et al. JI, 2013). In addition, it has been shown previously that ß-(1-3)-glucans, which are sensed by GNBP3 in Drosophila (Gottar et al., Cell, 2006), are concealed by the cell wall (germinating conidia) or hydrophobins (Wheeler et al., PLoS Pathogens, 2006; Aimanianda et al., Nature, 2009) . In the case of yeasts, these glucans are accessible only at the budding scar (Gantner et al., EMBO J., 2003).

Fig S1O is not convincing that Boms alone are present. There is significant noise near Drs in FigS1 infected, which likely saturates the detector before Drs can fly to it. I say this because DIM4 (Daisho) indicates that Toll is strongly induced. The authors should show a larger mass range on the x-axis including peaks of other Toll-induced peptides like the BaramicinA DIM10, DIM12 and DIM13 peptides of their companion paper and DIM14 (Daisho), which are closer in mass to the Bomanins and less likely disrupted by the noise at 4300 m/z. The maldi-tof calibration to correct ranges is critical for arguments of quantification.

We provide the primary data in the Rebuttal figures at the end of this document. These are the results obtained from three single flies (Files A29683PBUG22, A29684PBUG23 and A29684PBUG24). The first three spectra correspond to the full scale based on the major peaks observed (DIM4/BomS5) in two out of three spectra. At this scale, no signal is visible for Drosomycin at 4891 and the “noise” at 4278 is modest. Next, the multi-spectra report allows to put all three samples on the same sheet, this time zooming on the peaks of interests in the region 4300 (“noise”) and 4891 (Drosomycin). Finally, the next two pages zoom in on the BomS peptide signals and the next page keeps the same scale to document the 4300-5000 region. On the last page, it is obvious that the signal around 4300 is very modest and too distant to influence the Drosomycin ion, thereby excluding any effect of suppression. Of note, in the systemic immune response, Drosomycin is the most induced AMP with a concentration estimated to be around 0.3µM, an order of magnitude higher than other AMPs. Finally, these experiments have been performed by PB who initially developed the technique (Uttenweiler-Joseph, PNAS, 1998) and has been using and developing it ever since.

Combined with comments in Major Concern 1, I am not convinced that the -inducible- Bomanin response mediates the resilience phenotype.

Besides our replies above, we do hope that the new data we have included in Fig. 6 that document an induction of only two BomS genes in the heads of Drosophila upon verruculogen and the finding that BomS6 expression in the nervous system protects the fly from the effects of verruculogen will convince this reviewer.

3) The author's language is very strong to disregard a possible antimicrobial activity.

As noted above, this is a misunderstanding that we hope is dispelled in the revised discussion (see also above and replies to Reviewer 1).

Previous studies showed increased Candida growth and decreased hemolymph killing activity in Bom55C flies (Lindsay et al. 2018 and Hanson et al. 2019).

Please, see reply above. Factually, Lindsay et al. did not study the C. glabrata titer in vivo but using collected hemolymph. The killing activity likely requires a cofactor regulated by the Toll pathway. Hanson investigated the burden of the dimorphic C. albicans pathogen that in flies is filamentous and not C. glabrata.

Also see minor concern (i).<br /> I grant that the data are consistent with a resilience role. However the authors found no binding of Bomanin to restrictocin, countering their idea of a -direct- anti-toxin effect.

We are surprised by this comment. We certainly did not favor this idea nor developed it in the original manuscript, even though we cannot formally exclude it at this stage. Future experiments will focus on BomS6 potential interactions with these two mycotoxins.

At present the authors cannot rule out a direct antimicrobial role, or even the possibility of two different roles for the same peptides (ex: one in resilience, one antimicrobial). For instance, it is difficult to explain the loss of killing activity of Bom-deficient hemolymph ex vivo from Lindsay et al. if Bomanins are strictly anti-toxins. Surely they must also do something generalist?

Please, see our replies above and the paragraph dedicated to this topic in the Discussion.

4) In most figures, the authors do not compare flies with shared genetic backgrounds.

The MyD88 allele we are using is a transposon insertion from the Exelixis collection and we are using the wA5001 strain that was used to generate the collection of insertion (Thibault et al., Nat. Genetics 2004). We thank the reviewer for this comment as we realized we had forgotten to mention the Bom__D__55C strain. Lines 603-604 state that the deficiency line has been isogenized in the wA5001 background.

The phenotypes are usually strong so I am not concerned.

However the rescue effect of Bom transgenes in Fig 5C-D is based on smaller differences. Were these genetic backgrounds controlled?

Yes, as much as we reasonably could. The fact that most BomS transgenes did not rescue gives further confidence in the data.

Were transgenes inserted at the same site?

We used the strategy for overexpression developed by the Basler laboratory (Bishof et al., Development 2013, Nat. Protocols 2014) that relies on insertions at the same site.

The authors seemingly used a heat shock to express transgenes.

Heat-shocks are usually a short exposure to higher temperatures, usually 37°C. Here, we have used the inducible Gal4-Gal80ts system developed by McGuire and Davis (Trends in Genetics, 2004). The Gal80 repressor inhibits Gal4 function at the permissive temperature (18°C) and becomes inactive at the restrictive temperature (29°C). Thus, we use a temperature shift and not a bona fide heat shock.

Given a resilience effect is being studied, this heat stress approach is sub-optimal. Earlier experiments showing effect/no effect of Bomanin on heat shock resilience would improve confidence here. I would recommend assaying temperatures that can kill wild-type in order to confirm that Bom do not succumb earlier (ex. up to 37'C).

The results have been discussed above and show that 29°C is not a concern for Bom__D__55C and not much of a significant problem as regards MyD88.

In Fig5C the time resolution is poor, and the effect inconsistent across Bomanins. What are the differences in the Bomanins that the authors suspect could cause this? And how consistent are the experiments?

We provide all the primary survival data in Rebuttal Fig.1 A-H. The partial protection effects of BomBc1, BomS3 and BomS6 against restrictocin are consistent in the three independent experiments (Fig. 5D and Rebuttal Fig. 1 A-B). As regards the seven independent experiments performed with verruculogen, we observed a strong protection conferred by BomS6 expression in six experiments whereas we detected a milder protection conferred by BomS1 in four out of seven experiments and no protection in the three other ones. The effects were always there after 24 hours, in keeping with our novel data showing that BomS6 expression allows a faster recovery, around 10 hours, from verruculogen-induced tremors (Fig. 6E-F).

Since the effect is finished by 24h, perhaps a boxplot of percent survival at this time would better show the consistency across experiments.

Given the argument presented just above and considering that this rebuttal letter will be published alongside the article, this may not be needed.

Minor concerns:

i) The authors say the fungal burden of Bom55C flies remains low in Fig 5B, but they never measure flies that are near death when fungal load is greatest, or FLUD like in other figures. Given low mortality at the following time points, it seems likely that A. fumigatus would grow beyond initial loads in those individuals and kill them. I grant that these loads are less than what is seen in Hayan mutants. I just might suggest a more careful consideration of the time points used and what can be said about the trends shown here.

This is certainly a relevant point. The FLUD data are now presented in Fig. EV8_A_ and do not reveal any additional growth.

ii) Could the authors comment somewhere about the levels of toxin they were required to inject to get a phenotype vs. the level of toxins the authors expect are found in the fly during infection? I appreciate that toxin injection likely requires much higher doses, but it would be good to know just how far the authors have pushed their experimental system beyond its natural range.

This a question that is difficult to answer accurately as we are not sure the techniques exist to measure toxin levels in these small flies. We have tested a range of concentrations. It is clear that we push the system and likely use concentrations that are higher than those actually secreted by A. fumigatus during infection. Indeed, the mutant strains defective for the production of verruculogen or restrictocin display only a mildly reduced virulence in MyD88 flies. This makes it even more remarkable that wild-type flies are able to withstand these high, unphysiological concentrations, an argument for an indirect effect independent of the dose as pointed out now in the Discussion. How fungal pathogens balance the expression of the hundreds of secreted virulence factors, proteins and secondary metabolites, is a major frontier for future investigations be them plant or animal pathogenic fungi/

Again regarding toxins vs. general stresses, one could manage to inject salt into the hemolymph and show a stress-sensitized fly would succumb at lower doses than wild-type, emphasizing the relevance of defining concentrations.

We feel that just monitoring the survival of flies after a challenge that produces an effect is sufficient (Fig. EV8_C_).

The authors could also write toxin concentrations clearly in the figure/legend per experiment.

Corrected.

iii) Throughout the manuscript, the order that figures/panels are cited is inconsistent. Perhaps the text could be re-written so the reader can follow the figures more intuitively while going through the text?

Corrected.

iv) There are a few points where run-on sentences, involving many commas, make it hard to follow the logic. I might suggest a careful reading to break up long sentences into two sentences to ensure clarity.

We hope to have addressed this concern.

v) Line 279-281: this is the first and only mention of the immune surveillance hypothesis in nematodes. This is strange, given the authors are effectively describing an analogous idea exists in flies? Perhaps this could be added somewhere in the introduction or discussion.

We have followed the advice of the reviewers and now discuss this point more fully in the Discussion under its own subheading.

Small points

• What timepoints are the gene expression data from? Could the authors indicate this in figures/legends?

Done

• Line 133-135: "We conclude that MyD88 flies succumb to a low A. fumigatus burden..." - could the authors cite a figure panel here to emphasize what evidence they're referring to.

Done

• Line 151-152: Dudzic et al. (2019- Cell Reports Figure 3) showed that PPO2 was regulated by Hayan, while PPO1 by Sp7. This relevant study should be cited here or in the introduction/discussion.

Excellent suggestion, this was indeed an important study. Done

• Line 179-180: could the authors define the gliotoxin mutant strain here in the text for clarity?

Done

• Line 196: Fig. 4A-B should be Fig. **S4 A-B?

Corrected.

• Fig4A: perhaps the authors could reduce the x-axis to focus on the early time points? If I understand correctly, aspf1 has slightly delayed killing compared to akuB (˜50% difference at 2 days), but both kill 100% by 3 days.

Done

• Fig4G: can the authors define the GFP transgene on pg10? Not clear what this is, or what this means. Brain? Fat body? The legend of Fig4G and the key in the top left... it's not easy to quickly understand what is shown in Fig4G.

Done

• Line 247: I would drop the "at the intracellular level" part. I'm not sure this is robustly shown given the use of an in vitro model where there is no closed extracellular environment. The data are convincing of the effect, this is just a semantic point.

We agree that there is no closed extracellular environment and that therefore any signal emitted by the cells might get too diluted. However, the addition of EGF will activate the Toll intracellular through the chimeric EGFR-Toll receptor. As restrictocin is known to act intracellularly, one might have though that there might be some intracellular effectors mediating the Toll-dependent protection against restrictocin. Our sentence excludes this possibility.

• Line 257-258: Cohen et al. (2020- Front Imm) never used Bomanin mutants. Did the authors mean to cite Hanson et al. (2019) here, which seems to fit their described citation re: Bom55C vs. Toll mutant flies (Fig. 2)? Given Hanson et al. infected Toll mutant and Bom55C flies with many bacteria/fungi including A. fumigatus, it's strange this study is not discussed currently.

The reviewer is correct. Cohen et al. did use A. fumigatus, but on Daisho mutants and MyD88 and not Bom__D__55C as a control. We are now citing Hanson et al., 2019 in lines 443-449 (Discussion).

• Fig5C-D: the labeling is difficult to follow.

This is difficult to address unless multiplying EV figures. We feel this is not needed: the important curves are in color and each such curve is seen on the graphs.

• Line 318: a -possible- AMP role of Bomanins was proposed because of the aforementioned killing activity of wt but not Bom mutant hemolymph, alongside rescue by single Bom genes. To say this was based only on survival experiments is incorrect.

The paragraph has been rewritten and expanded to dispel any misunderstanding.

• Line 324-328: could the authors cite appropriate references after "inhibition of calcium-activated K+ channels" ?

Done

• comment re-Line 334: Toll10b flies have melanotic tumors and are in general in a stressed state. Might their rescue be due to increased stress tolerance by pre-activated stress responses?

This is a developmental effect occurring during larval stages, also observed for Cactus mutants. Here, we use a UAS-Tl10B transgene that is induced only at the adult stage using the Gal4-Gal80ts system. Thus, any stress is minimized as much as possible. Furthermore, we can phenocopy this phenotype to a large extent using a UAS-BomS6 driver, even though the phenotypes are subtly different as regards the protection against verruculogen-induced tremors.

Referees cross-commenting

Yes I agree that the data themselves are not the issue, nor even the direction of the results. But there are many overly-strong statements that go so far as to refute ideas which are supported by other studies, and for which the authors here do not provide any contradictory evidence.

We hope that this revised, extended version has clarified any misunderstanding in the initial version.

As per my review, I would be happy with a re-write that softened the language overall. I genuinely wonder if these Bomanin mutants simply have poor development, and so they are susceptible to neurotoxins/stress because their nervous system/development leaves them less resilient in general. Experiments testing their resilience to different stresses would greatly elevate the ability to make confident insights in the present manuscript. Currently the authors have only investigated one type of phenotype and interpreted it as if that is evidence of the evolved purpose of the peptides. This approach does not account for many other possible (and reasonable) explanations.

We have performed the experiments suggested by the reviewer. While we see a modest effect of heat on MyD88, it is not found in Bom__D55C flies, which display essentially the same phenotype as MyD88 with regards to the sensitivity to A. fumigatus or some of its secreted mycotoxins_._

Reviewer #2 (Significance):

This paper should be of broad interest to the study of immunology, where roles for effectors are typically thought of as cytokines. In fruit flies and other invertebrates that lack adaptive immunity, immune effectors are more thought of as direct actors likely with antimicrobial properties. The finding that Toll might mediate resilience is interesting, and implicating well known Toll effectors provides an important step forward towards a mechanistic basis behind this resilience effect.

We thank the reviewer for his appraisal of the significance of our work.

My expertise is in insect and innate immunity.

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

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Referee #1

Evidence, reproducibility and clarity

Summary

The authors have set out to study the Drosophila immune response against the fungus Aspergillus fumigatus. They found that Aspergillus fumigatus kills Drosophila Toll pathway mutants. The fungus does this without invasion because its dissemination is blocked by melanization. They suggest that there is a role for Toll in host defense distinct from resistance. The findings are interesting, and looks like the mycotoxins play a role. It also seems that there is some role of the Bomanins here, but I find that in particular Figure4 experiments are not convincing enough to provide a mechanistic insight as to what is going on. I think the authors need to think through what their results mean, and also, explain better (especially regarding Fig 4) their ideas and how the data fits them.

Major comments:

Page 5: .."the fungal burden did not increase much in MyD88 flies challenged with 50 conidia (Fig. 1B)" - What do you mean did not increase much? There is a clear increase in Myd88 mutants compared to controls; would you expect a bigger increase (e.g. log scale induction)? Explain.

Page 6: "the SPZ/Toll/MyD88 cassette is required for host defense against A. fumigatus infections, even though this pathogen only mildly stimulates the Toll pathway." - Should you rather say that A. fumigatus only mildly induces the Toll pathway target gene Drosomycin?

Page 6: "...we tested Hayan mutant flies defective for this arm of innate immunity (Nam et al., 2012)." - elaborate this, which arm/which pathway? This has not been introduced in the introduction. Explain. Can you really draw this conclusion: "We conclude that melanization limits the proliferation and the dissemination of A. fumigatus injected into wild-type flies yet does not eradicate it at the injection site, where a melanization plug forms." Maybe you can based on the function/importance of the pathway to melanization, but you need to explain.

Page 10: "The cleavage of the 18S RNA was however much less pronounced in wild-type flies as compared to MyD88" - I am not sure what this means. Do you mean 28S? And that the 28S peak is lower? Is this a quantitative method? Fig. legend: "Arrows show the position of the 28S RNA sarcin fragment" - there are three arrows in both Fig 4E and F; specify which arrows point what.<br /> Based on the results, I am not convinced about the conclusion, that "restrictocin is able to inhibit translation to a detectable degree in vivo, likely through the cleavage of the ribosomal 28S a-sarcin/ricin loop as described in vitro." <- Do you draw this conclusion before doing the actual in vitro experiment, which is described next in the text (The rabbit reticulocute assay, S2 cells)?

4H: Not sure what should be seen here, is it the darkest band at 0 uM that disappears? HI & J need more explanation than what is now included in the text or Figure legend, is the conclusion that there is no difference? Write the stats above the Figs 4I & J (n.s.?).

Minor comments:

It would have helped commenting if the manuscript contained line numbers

Why do you have the title "Hayan" on top of Fig 1F; you don't have this marking system in the other survival curves

Fig 2A: Can you speculate why MyD88 flies die rapidly at day 10 if you inject PBST (your control)? What would happen to uninjected controls in otherwise the same conditions? (you could include an uninjected control here?)

Fig 2E: Not sure what would be the best way of presenting the curves - different colors, dotted lines or something? Now if there are too many lines, they are hard to tell apart. because the symbols are not that visible. Like in 2E if you want to compare the light red/orange colored lines.

For consistency add the caption also to Fig 3D (I assume it is the same as 3C)

For consistency, should you add Verruculogen on top of Fig 3F?

Chronologically, how it is explained in the text, Figs 4A and B are in the wrong order.

The quality of Fig 4 is not great, the text is hard to read (too small) and becomes blurry upon magnification.

Page 12; "These data then suggest that a process akin to the immune surveillance of core cellular processes first described in C. elegans may also exist in Drosophila" - I think this sentence belongs to the discussion, this is not directly drawn from the results.

Referees cross-commenting

I think we share many thoughts among all the reviewers. The main problem is that the manuscript language is quite strong; from the results many times it is not ok to make such strong statements. Some experiments need further analysis and clarification. I think in most cases, this could be achieved by softening the statements and adding more discussion, and not by making new experiments (some may be needed).

Minor things are that experiments are not advancing in a logical order between the text and the figures and there are problems with resolution in some figures. Statistics in some figures needs to be added.

Significance

The nature of the work is conceptual for the field, to understand the role of the Toll pathway and Bomanins in particular, in this fungal infection model. The work is interesting to a somewhat limited audience, mainly immunologists and in particular, people interested in the Drosophila model for immunity. The work may be interesting conceptually in understanding fungal infections.

My expertise: I am a Drosophila immunity researcher with nearly 20 years of experience in working with fly immunity, in particular the Toll and the Imd pathways.

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Reply to the reviewers

We thank the reviewers for their time in evaluating of our manuscript and for the useful feedback. We are grateful that reviewers acknowledged that our study is important because it “sheds much needed light on this less documented early stage of cancer development”. The reviewers were overall positive in their assessment and, as reviewer #3 noted, our study “advances this field conceptually by highlighting the importance of targeting the cell signaling and chromatin regulation together”. The common criticism of all reviewers relates to writing style, some textual interpretation and ensuring that the number of replicates, statistical analysis, and cell culture type were appropriately mentioned. We felt these were valid points and have taken onboard all these comments. A shared concern between two of the reviewers was related to the logic behind the timepoints we chose to analyse cells in the different assays. We are confident that we have addressed this, and all other comments as detailed below.<br /> Please find below a point-by-point reply to the reviewer’s comments.

Reviewer #1 (Evidence, reproducibility and clarity):

This study aimed to identify events that happens early in malignant transformation of breast cancer (BC) cells that are driven by HER2 oncogene. Constructing a 3D inducible model to study impact of HER2 protein level on BC cell and assessment of gross morphological changes, protein phosphorylation and chromatin accessibility at different time points of HER2 activation.

Using a controllable in vitro model is a good approach although it is not novel. Also the method used to assess HER2 protein positivity is not standardized nor clinically relevant. Positivity of HER2 in clinical practice is assessed either through immunohistochemistry (IHC 3+ or 2+ with gene amplification), however the author did not mention any control for positivity except western blot which is not used in clinical practice.

We agree with the reviewer that we should have included our comparison of HER2 protein levels for our cells with a positive control. We have tested this, and the data will be included in the revised version of the manuscript. Briefly, both western blot (WB) and IHC are very useful methods with different benefits: WB is less cost effective but more quantitative, while IHC gives a better overview of tissue heterogeneity. Indeed, due to higher sample processing costs, WB is not used in clinical practice to assess HER2 but it has been shown that there is a high concordance (in 95% of over 300 tumours analysed) between the two methods as both techniques showed prognostic significance R. Molina et al., 1992 (PMID: 1363511). We performed comparison of HER2 protein expression levels of our subpopulations (low, medium, and high HER2 expressing cells) versus two patients’ samples that were already known to be HER2 positive using IHC 3+ or 2+. We were able to demonstrate that HER2 protein levels as measured by western blotting showed that the low HER2 expressing cells expressed less HER2 protein compared to IHC 3+ or 2+ and may be comparable to patients with IHC 1+, which are considered HER2 negative and do not qualify for anti-HER2 therapies such as Trastuzumab.

There is difference between early HER2 positive BC and HER2 low BC. As the earlier is driven by HER2 oncogenic signalling pathway, but the latter is not.<br /> Identification of molecular changes that occur at HER2 low BC seems very important and clinically relevant, however HER 2 low is not fully characterized, yet. And the only definition available is either HER2 1+ or 2+ without gene amplification. The author was not very clear about threshold he followed to call the model HER2 low. Is it positive with lower limit of positivity or just small amount of protein). He also concluded that BC with sub-threshold of HER2 protein behave more aggressive than HER2 positive BC. What is the threshold and was it correlated with IHC or gene amplification level to be reliable?

The HER2 positive population in our in vitro inducible system was determined by flow cytometry, we separated the overall (bulk) HER2 positive cells into three different subpopulations and selected the bottom 20% of HER2 expressing cells as the “low HER2” and the top 20% of HER2 expressing cells as “high HER2”. We show in figure 4C the different thresholds for low, med, high HER2 protein expression by flow cytometry. We have modified the figure and the figure legend (figure 4C) to better indicate the different subpopulations. Through western blotting we compared these population of cells with patients’ samples that had IHC 3+ or 2+ and showed that low HER2 population expressed less protein than IHC 2+, whereas the high HER2 was relatively comparable to IHC 3+ sample.

The status of oestrogen and progesterone receptors were not highlighted. Triple negative breast cancer, for instance, is more aggressive than HER2 positive BC, this may be the reason for the worse behaviour.

We have modified our main text in the manuscript, line 68-69, to better reflect the fact the MCF10A cells are both oestrogen (ER) and progesterone (PR) negative, this has been already characterised by Qu, Y et al., 2015 (PMID: 26147507). However, importantly, we do not think that ER and PR status is the reason these cells are relatively more aggressive, as normal MCF10A cells without HER2 expression did not display any transformative characteristics in our molecular analysis and/or in vitro functional assays, despite being ER and PR negative.

At line 130, "The low levels of HER2 protein activation at early time point may closely mimic at least partially the signalling changes occurring in HER2 positive BC patients". This claim is not quite true, as low levels of HER2 protein activation doesn't activate HER2 oncogenic signalling pathway as HER2 positive does.

We thank you for this insightful comment, we have modified our main text to better reflect our view (line 132-133). However, we were not sure which published data the reviewer was referring to in this case. In particular, if low HER2 levels can still form dimerisation with its family members and induce signalling via its family partners such as HER1, HER3 or HER4.

The author aimed to study the signalling changes accompanying low levels of HER2 induction by lowering significance threshold to log2fold > 0.5. Lowering the threshold for significance will increase the total number of phosphorylated protein (both at low HER2 levels and high levels). So, studying the whole significant proteins at whole time points will not be exclusive for low HER2 levels and this was evident through activation of MAPK cascade which is one of downstream signalling pathway of HER2 positive BC.

We agree that a log2fold change > 0.5 would increase the total number of significantly phosphorylated proteins. We first performed the analysis on a more stringent cut-off value of log2fold change > 1.5 p-value, <0.05 as shown in figure 2B. In the supplementary we also show the reduced stringency of log2fold change > 0.5, p-value <0.05, for the following reasons: when it comes to proteins, it is conceivable that a log2fold change > 0.5 is sufficient to induce molecular changes; secondly, our study investigates changes that occur just half an hour, and up to 7 hours, after HER2 protein induction. At such early time-points, proteins would be beginning to be phosphorylated and the extent of it may not be pronounced (especially in a small subset of the population); finally, we thought it is important to share this supplementary analysis with the scientific community to have access to this data so that they may further interrogate it from different perspectives.

Combining HER2 protein level (both IHC and Western blot) to different time points will give better understanding of events associated with HER2 low, early positive or late positive.

As above, IHC is routinely performed for clinical diagnosis because it is cost effective. Although, western blotting is laborious and expensive, it is more quantitative compared to IHC.

Reviewer #1 (Significance):

This work provides good evidence to changes that happen at early HER2 positive breast cancer transformation and introducing a chromatin opening and accessibility as a new target of treatment of HER2 positive breast cancer patients.

We thank reviewer #1 for their thoughtful feedback and for their appreciation of our work.

Reviewer #2 (Evidence, reproducibility and clarity):

HER2 amplification is associated with poor prognosis of breast cancer. Despite it has been extensively studied, it deserves thorough study how HER2 amplification alters downstream signaling pathways, chromatin structure and gene expression, and how cells overcome the hurdles in order to transform. In this study, Hayat et al used doxycycline-induced HER2 expression in MCF10A cells to recapitulate the very early stage of HER2 expression and HER2-induced mammary epithelial cell transformation. The authors performed global phosphoproteomic, ATAC-seq and single-cell RNA-seq, and propose sub-threshold low level HER2 expression activates signaling pathways and increases chromatin accessibility required for cell transformation, while high HER2 expression level in early stages results in decreased chromatin accessibility.

Major comments:<br /> 1. Although it is not clearly described, it seems that phosphoproteomic and single-cell RNA-seq were performed using 2D-cultured cells, while ATAC-seq was performed using 2D (FACS sorted cells based on HER2 expression levels) or 3D (time course)-cultured cells. Cells cultured on 2D and 3D are significantly different on cell signaling, chromatin structure and gene expression, and therefore cannot be compared.

We agree that there are differences between 2D and 3D cell cultures, which may impact on the multi-omics experiments performed in this study. In an ideal world we would have preferred to be able to conduct all experiments in 3D cell cultures, including the phosphoproteomics experiments. However, this is not feasible because the phosphoproteomics experiment requires 500ug of total protein which corresponds to approximately 10 million cells for each condition and replicates in 3D matrices. 3D structures would have also presented with accessibility issues since doxycycline might not have reached all cells equally at the 30 minutes timepoint. Since we were analysing early timepoints for phosphoproteomics, homogeneity in induction was important. We performed ATAC-seq in 3D cell culture because it was feasible as it only required 25,000-50,000 cells to be grown in small 3D cell cultures and is indeed superior for physiological relevance. We therefore had to compromise and worked with the assumption that immediate signaling events will not be fundamentally different in 2D vs 3D. We have modified the main text to better reflect this and have indicated which experiments were performed in 2D vs 3D in the figure legends and the methods section.

1. Phosphoproteomic (0.5, 4 and 7 hours), ATAC-seq (1, 4, 7, 24 and 48 hours) and single-cell RNA-seq (7, 24, 48 and 72 hours) were performed on cells at different time points after doxycycline treatment. The authors need to clearly explain the rationale why such time points were chosen for each experiment in the text.

There are indeed differences in the time-points analysed between the different multi-omics analysis. However, as mentioned above, the reason for selecting such early time points for the phosphoproteomic experiment was that signalling changes are rapid and we were focused on characterising the early signalling dynamics. With regards to the ATAC-seq and scRNA-seq, there are several shared time-points such as the 7h, 24h, and the 48h. Additionally, as the chromatin changes would be slower acting as compared to signalling changes, two later time-points were selected including the 48h (ATAC-seq) and 72h (scRNA-seq) to capture some late changes during cellular transformation.

1. Change on chromatin accessibility does not necessarily mean change on gene expression levels. RNA-seq needs to be performed and analyzed along with ATAC-seq data.

We agree that chromatin accessibility does not necessarily correlates with gene expression changes and the need to perform RNA-seq to make such a conclusion. This is the reason we performed single cell RNA-seq, which looks at changes in high temporal and cellular resolution. This is particularly useful for the heterogenous cell population that we worked in to better understand the differences between cell types.

1. Analyses on multi-omics data are quite preliminary. Clustering analysis on the time course of phosphoproteomic, ATAC-seq and single-cell RNA-seq will help characterize the dynamics of cell signaling and gene expression. Integrated analyses on multi-omics data and construction of regulatory network are necessary to identify the key signaling node and key epigenetic regulators/machinery that facilitate or prevent cell transformation. Integrated analyses, of course, need to be performed on data obtained from cells cultured in the same conditions.

We think our study is an important work and provides a strong foundation for a comprehensive, integrative multi-omics study using primary human breast cells with parallel analysis performed on the same population of cells using the latest techniques such as scATAC and RNA-seq or scNMT-seq. We are indeed in the process to apply for funding in a larger analysis that involves in vivo work and clinical samples, using this study as a foundation.

1. The authors picked up several genes from the analyses, and discussed the potential importance in cell transformation without functional validation. It is important to show data demonstrating altered expression of certain genes and/or altered activity of certain signaling pathway/epigenetic regulators is indeed important for cell transformation in low HER2-expressing condition or preventing cell transformation in high HER2-expressing condition.

We agree that this is important. The scope of this study is to report on the result that low HER2 was unexpectedly more aggressive compared to high HER2, which was a highly reproducible observation, and identified a molecular explanation for this behaviour (dedifferentiation and predominant chromatin opening). In terms of cross validation, we found the MUC1 protein expression to be low in low HER2 expressing cells, indicating that they are more stem-like (figure 4B). We confirmed and validated this finding in our scRNA-seq data shown in figure 4F. The pathway analysis from phosphoproteomic study shows that MAPK pathway is highly activated upon HER2 protein overexpression. To validate this claim, we performed western blotting analysis that confirm this as the ERK protein was hyperphosphorylated in HER2 expressing cells compared to controls. Thus, our resource study provides many candidates that can be tested to further explore the biology.

1. HER2 expression in MCF10A cells is insufficient in inducing tumor formation in vivo, although HER2 expression results in disrupted acini structure and colony formation in vitro (e.g. Alajati et al. 2013 Cancer Res, 73:5320-5327 cited in the manuscript). It is interesting to investigate whether this is due to the mechanisms identified in this study.

MFC10A cells are generally difficult to transform in vivo. It is possible that mechanisms identified in our study might be responsible for lower tumourigenicity in vivo with WT HER2 compared to HER2 variants, since our study suggests activated checkpoints in high HER2 cells. It would be interesting to compare the differential impact on chromatin for the two HER2 variants too. In our system, we think the reasons why cells form abnormal morphological changes and grow colonies in vitro is a result of HER2 overexpression, which induces aberrant signalling, and this may be leading to loss of cell-to-cell contact and disruption of adhesion molecules. However, the objective of this study was to understand the early signaling to chromatin changes in in vitro cellular transformation, and changes in cell morphology are a consequential part of the process.

1. In Figure 2C, two replicates are completely separated and replicates of each time points are not clustered together.

We agree that the two replicates are separated into two separate groups, this was demonstrated by the PCA analysis (Supplementary Fig 1F). We grouped these samples into “early” (0h, 1h, 4h, and 7h time-points) or “late” (24h and 48h time-points) based on them clustering well into these two groups. The subsequent analysis were performed based on these groups that clustered together. However, we still showed each replicate in figure 2C to appreciate the dynamics of chromatin accessibility between each time-point, which shows clear differences in HER2 versus Control.

Minor comments:<br /> 1. Essential experimental information, e.g. whether cells were cultured in 2D or 3D, needs to be clearly and accurately described in main text, figure legends and experimental procedures.

The figure legends in the manuscript have now been modified to include information on cell culture type.

1. Statistic methods are not provided. In Fig. 4D, HER2-med and HER2-high need to be compared to HER2-low group.

Statistical analyses have been added to figure 4D and HER2-med and HER2-high have been compared to HER2-low group.

Reviewer #2 (Significance):

The authors propose sub-threshold low level HER2 expression activates signaling pathways and increases chromatin accessibility, which facilitates mammary epithelial cell transformation, while high HER2 expression in early stages results in decreased chromatin accessibility via unknown feedback mechanisms. It is interesting to identify which signaling and epigenetic regulators are essential to cell transformation, which feedback mechanisms prevent the transformation of HER2-amplified mammary epithelial cells, whether inactivation of such feedback mechanism indeed occurs in tumorigenesis of HER2-amplified breast cancer, and whether it is a potential therapeutic target for HER2-amplified breast cancer.

Expertise of review: breast cancer, cell signaling, tumor microenvironment.

We thank reviewer #2 for their time and for providing such useful feedback on our work.

Reviewer #3 (Evidence, reproducibility and clarity):

In this paper Hayat et.al study the early transformational events that follow the activation of the oncogenic HER2 signaling pathway and its crosstalk with chromatin opening. Using an inducible in vitro model of HER2+ breast cancer they have identified that the overexpression of HER2 transforms non-tumorigenic breast epithelial cells via chromatin regulation. The study also shows that the transformative potential of the cells is inversely related their HER2 expression where the low HER2 expressing cells obtain a stem-cell like signature and increased chromatin accessibility leading to an increased transformative potential.

Major comments:

While the key conclusions of the paper are convincing, here are the parts of the study that need further clarification or supporting data from the authors.

1. In Figure 1C the authors show that MCF10AHER2 cells formed complex transformed masses when grown in 3 dimensional cultures. From the figure it is evident that that the transformative potential of the HER overexpression is far more pronounced at the Day 6 and Day 9 mark. Therefore, one wonders why these time points weren’t used as the “late timepoint” in any of the sequencing studies moving forward. Can the authors comment on this choice and perform additional experiments to address the molecular changes that lead to the dramatic transformations seen at this timepoint? Since the authors have a well-established protocol in place, looking at an additional time point could be potentially feasible, provided the cells/samples have been frozen down at this stage. If unable to do so, could the authors comment on the molecular changes they would expect to see at this time point.

In our study we primarily focused on the early events upon HER2 overexpression because the changes appear to be much more dynamic, and we hypothesised that these events are the cause of the subsequent, more pronounced featured later on. The rationale behind employing an inducible system and capturing the early changes was to identify aberrant molecular events at the earliest time possible. Indeed, numerous studies have investigated the differences between normal versus cancer cells (many of which are at later time points, that have missed the foremost aberrant molecular changes). Based on our ATAC-seq analysis at late-timepoints, 24h and 48h time-point, the number of changes in chromatin accessibility become relatively more stable as compared to early time points (supplementary figure 2A).

1. Fig 1D the authors conclude that the overexpression of HER2 causes increased cell invasion based on the results seen in a collagen coated plate. How to the authors explain the lack of any such significant change in a Matrigel coated plate?

To test the invasiveness of the HER2 overexpressing cells, collagen is used to increase stiffness to Matrigel. Stiffness is relevant for the type of invasion seen in these 3D cultures because it activates pathways important for invasion. We added the references to the text for clarity (PMID: 15838603 and PMID: 16472698).

1. In Supp Fig 1D the authors use the DAVID Bioinformatics tool to identify the various signaling pathways enriched in the HER2 induced system. In addition to the MAPK pathway this analysis also shows other common cancer-related pathways (eg. The Mtor pathway) being enriched to a similar or higher extent. Can authors address why only the MAPK pathways was pursed in detail?

HER2 is major receptor that can signal through various signalling pathways. We highlighted the MAPK pathway because it has been previously shown that MAPK cascades can modify chromatin through transcription factors and chromatin regulators Clayton and Mahadevan., 2010 (PMID:19948258). We think that when HER2 is overexpressed, it primarily signals down the MAPK pathway, resulting in the activation of transcription factors and chromatin regulators that lead to a highly accessible chromatin and ultimately contributes to transformation. To confirm this result, we did perform western blotting control analysis and found that indeed, HER2 overexpression consistently activates the MAPK pathway that shows phosphorylation of ERK but does not influence AKT phosphorylation. We can include this data in the manuscript.

1. Figure 4B and supplementary figure 3E only show that percentage of the cells have either MUC1-ve or EpCAMlow or CD24low expression. However, Figure 4A and the corresponding text indicates that that breast stem cells are defined by a combination of MUC1-ve, EpCAMlow, and CD24low expression. If this is the case, the authors need to show the percentage of the cells within each population have an overlap of all these expression signatures, to support the claim of low HER2 expressing cells showing a more de-differentiated stem-cell like property.

Our results confirm that upon HER2 overexpression, cells become MUC1-ve, EpCAMlow and CD24-ve, acquiring the breast stem cell signature. We did not show the CD24 expression because all the cells that were MUC1-ve and EpCAMlow were also 100% CD24-ve. We have now modified figure 4B and the figure legend to reflect this change, additionally, we added another figure (supplementary figure 4) that shows how the analysis was performed systematically.

1. The authors also state 'other biological effects being responsible for the lower capacity in anchorage-independent growth of high HER2 expressing cells' that is shown in fig 4d. While an experimental investigation of these effects may be out of the scope of this study, the authors may consider commenting (and referencing additional literature) on the other biological effects they think may result in this phenomenon.

We have modified the manuscript (lines 294-296) and added further explanation as to what other biological effects may be responsible for lack of colony growth in high HER2 expressing cells in lines.

1. The authors do a great job providing details about all statistical analyses performed, however the details regarding the experimental replicates are only provided for some experiments making it difficult to infer if the experiments have been adequately replicated before concluding results. Can the authors please add the n - value for all applicable experiments in the figure legend or the methods section?

The number of replicates has now been added to the respective figure legends.

1. What is the scope for validation of these findings in vivo and in human samples? Could the authors please comment on this in the discussion section of the manuscript.

The primary goal of this study was to understand the early transformational events in a simple in vitro, yet a robust model that is highly accessible. We have analysed some human samples to compare the HER2 protein expression levels. However, the findings from this manuscript could be validated in more precious models such as primary human cells, human tumours samples and in vivo in animals. We have modified the end of discussion to address these points (lines 394-399).

Minor comments:

1. In figure 1B the authors show a western blot analysis for HER2 expression over time while using GAPDH as a loading control. However, GADPH control seems to be unequal, especially in the 1ug/ml Dox lane. This needs to be addressed.

We agree that there is a slight difference in the GAPDH levels in this western blot. We have carried out densitometry analysis which could be added to the supplementary data if required, to show that even though the GAPDH appears to be slightly less in the 1ug/ml of dox (last lane), it shows that HER2 levels are even greater than what appears on the blot, thereby confirming the trend we have observed in the current western blot.

1. In figure 1C, it is unclear if the images shown are representative of the exact same spot over a 9-day period or of different spots.

In figure 1C, the morphological regions are representative of the whole well in which the cells were growing but not the exact same spot. This is because nearly all the cells (>90%) transformed from round, organised acini to the fibroblastic, invasive morphology by day 9. We have captured multiple images of different areas in the well using confocal microscopy, and this can be added in the supplementary data.

1. In Supplementary figure 3E, labeling the y-axis on the figure as opposed to just in the legends would make it easy for the reader.

The figure has now been appropriately labelled.

1. With respect to presentation: In figures involving single cell RNA sequencing and phosphoproteome analyses, highlighting the specific genes that are focused in detail on the manuscript would aid the reading process. The current format makes it difficult for the reader to spot the specific genes that are the points of focus within each heat map.

We modified the figures concerning the phosphoproteomic analysis and scRNA-seq and have highlighted important genes for readers’ ease.

Reviewer #3 (Significance):

I have close to a decade's experience in working on breast cancer. In the past I focused on studying intratumor genetic heterogeneity and cell signaling pathway interactions. I am currently working on identifying novel therapeutic targets for the treatment of ER+ breast cancer. My expertise lies in understanding molecular biology of the disease. While I have worked with and understand most techniques used in this study, I would like to indicate that I do not have sufficient expertise in ATAC seq and am unable to evaluate the intricacies of this technique.

While molecular changes that occur in HER2+ breast cancer have been highly investigated, the changes that occur at an early pre-cancerous stage of the disease aren't as well documented. The work by Hayat et al., sheds much needed light on this less documented early stage of cancer development. The past decade has shown an increased focus on epigenetic therapy with more chromatin targeting drugs entering clinic (Siklos et al., 2022). There has also been increased clinical evidence underlining the efficiency of combining epigenetic therapy and with hormonal and other anticancer therapies in solid tumors (Jin et al., 2021). Phase II clinical trials combining HDAC inhibitors with aromatase inhibitor have shown to improve clinical outcomes in patients (Yardley et al., 2013). Similarly, pre-clinical studies have shown that combination therapy with BET inhibitors improved treatment efficacy and circumvented drug resistance in fulvestrant (Feng et al., 2014) and everolimus (Bihani et al., 2015) treatments. Conclusions from the work by Hayat et.al, although based on in vitro analyses, advances this field conceptually by highlighting the importance of targeting the cell signaling and chromatin regulation together. If validated in in vivo models and clinical samples, this may open up potential possibilities of combining anti-HER2 therapies with epigenetic therapies. Additionally, the study also makes an interesting observation that low HER2 expression could result in increased tumorigenicity of cells which is in contrary to current clinical norm of looking at increased HER2 expression as a sign of aggressive disease. These findings are of interest to the scientific and clinical community working on discovering novel therapeutic targets and biomarkers for treatment of HER2+ breast cancer.

We thank reviewer #3 for his/her overall assessment and for appreciating this work. There is a significant focus regarding low HER2 positive breast cancers in the field. Approximately 50-60% of breast cancers have "low" HER2 expression and in many cases, this low HER2 is seen together with metastatic cancer. The FDA has very recently approved fam-trastuzumab deruxtecan-nxki aka Enhertu, which appears to target these cancers with low HER2 well and is shown to be relatively effective in a phase 3 clinical trial known as Destiny Breast-04. However, it is not yet clear how low HER2 expressing cells drive the metastatic spread of breast cancers or why they are so aggressive. Our work sheds a light that increased chromatin accessibility could be a route of transformation in low HER2 cancers. Therefore, providing an alternative platform to target these cancers and why it is crucial that this work reaches the clinical and scientific community as soon as possible.

Author Response

Reviewer #1 (Public Review):

Kang et al. have performed whole exome sequencing of gall bladder carcinomas and associated metastases, including analysis of rapid autopsy specimens in selected cases. They have also attempted to delineate patterns of clonal and subclonal evolution across this cohort. In cases where BilIN was identified, the authors show that subclones within these precursor lesions can expand and diversify to populate the primary tumor and metastatic sites. They also demonstrate subclonal variation and branching evolution across metastatic sites within the same patient, with the suggestion that multiple subclonal populations may metastasize together to seed different sites. Lastly, they highlight ERBB2 amplification as a recurrent event observed in gall bladder carcinomas.

While these data add to the literature and start to examine important questions related to clonal evolution in a relatively rare malignancy, the authors' findings are very descriptive and it is hard to draw many generalizable conclusions from their data. In addition, the presentation of their figures is somewhat confusing and difficult to interpret. For example, they do not separate their clonal analyses by disease site and by time in a readily interpretable manner, as in some instances of Figure 2 and Figure 3 the clone maps are from different sites collected at the same time point, while others show some samples at different time points. Depicting these hierarchies in a more organized and clearly understandable manner would help readers more easily interpret the authors' findings. In addition, the clinical implications of these clonal hierarchies and their heterogeneity are unclear, as the authors do not relate the observed evolution to intervening therapies and may not be powered to do so with this dataset.

Thank you for the constructive and valuable comments about 1) figures and 2) clinical implications.

1) We agree with your opinion that Figures 2 and 3 are confusing. Reflecting on your comment, Figures 2 and 3 have been modified. Now, the time point at which the tissue was obtained and the anatomical location of the tissue are readily visible in the redesigned figures.

2) From a clinical point of view, we believe that our study highlights the importance of precise genomic analysis of multi-regional and longitudinal samples in individual cancer patients. In the current oncology clinics, cancer panel data of patients are being used to identify druggable mutations usually with a single tumor sample. However, we found that only a part of the mutations was clonal while a substantial proportion was subclonal, which is usually not an effective druggable target. For example, in the GB-S2 patient, after sequencing with GB tissue, ERBB2 targeting treatment would have been performed if a specific clinical trial is available because ERBB2 p.V777L is pathogenic. However, our clonal evolution analysis suggests that ERBB2 targeting strategy may not be effective in subclones without the ERBB2 p.V777L mutation, especially from regional metastasis. We have added the description for this part to the Discussion section (Page 13, Line 12-15).

Additional areas that would require clarification include:

1) There are very few details on how the authors performed their subclone analysis to identify major subclones, and what each of the clusters in Supplemental Figure 1 represents. In addition, they do not describe how they determined that the highlighted mutations in Table 2 were drivers for metastasis and subclonal expansion. Were these the only genes that exhibited increased allele frequencies in metastatic sites, or were other statistical criteria used?

Thank you for the important comment about 1) clone analysis and 2) highlighted mutations in Table 2.

1) Mutations were timed as clonal or subclonal through PyClone (Roth A et al., Nat Methods. 2014) clustering (Figure 1—figure supplement 1). Phylogenetic trees were constructed using the mutation clusters identified with PyClone as an input of CITUP (Malikic S et al., Bioinformatics. 2015) (Figures 2 and 3). We added the sentence "See Supplementary File 1 to check the matching information for the PyClone clusters and the CITUP clones." to the supplementary figure legend.

2) A full list of mutations constituting a CITUP clone can be found in Supplementary File 1. Among the mutations, previously reported cancer-associated genes harboring them were selected manually and listed in Table 2. References for each gene are introduced in the 'Evolutionary trajectories and expansion of subclones during regional and distant metastasis' section.

2) The authors do not discuss the relevance of variation in mutational signatures observed with disease progression/metastasis, e.g., is there any significance that signature 22 (aristolochic acid) and signature 24 (aflatoxin) are increased in metastases? In addition, when comparing their data to previously published reports in Figure 1B and Figure 4A, it would be helpful if the authors discussed possible reasons for some of the large differences in mutational or signature frequencies across datasets. For example, do the authors think the frequency of ERBB2 alterations is so much higher in their cohort than in prior reports due to methodological/data reasons or due to differences in patient population?

Thank you for the constructive and valuable comments about 1) mutational signatures observed with disease progression/metastasis and 2) differences in mutational or signature frequencies across datasets.

1) During the revision process, signatures 22 and 24 highlighted in the metastasis stage were validated by two additional tools, Signal (Degasperi A et al., Nat Cancer. 2020) and MuSiCa (Diaz-Gay M et al., BMC Bioinformatics. 2018) (Figure 4—figure supplement 3). Aristolochic acid is an ingredient of oriental herbal medicine (Debelle FD et al., Kidney Int. 2008, Hoang ML et al., Sci Transl Med. 2013). Given that all the patients in our cohort are Korean, and a recent study found that Korean cancer patients are frequently exposed to herbal medicines (Kwon JH et al., Cancer Res Treat 2019), one possible explanation is that some patients might have been exposed to herbal remedies containing aristolochic acid. On the other hand, aflatoxin is known to be contained in soybean paste and soy sauce, which are widely used in Korean food (Ok HE et al., J Food Prot. 2007). Considering that the signatures 22 and 24 are found not in early carcinogenesis but in late carcinogenesis and metastasis (Figure 4B and Figure 4—figure supplement 3), the two carcinogens appear to have little impact on the early stage of cancer development, but their impacts might be highlighted in overt cancer cells. Further investigation is required because it is difficult to determine the etiology of signatures 22 and 24 with this limited patient data. We updated this part in the Discussion section (Page 13, Line 4-7).

2) In the two previous genomics studies on GBAC, the prevalence of ERBB2 alteration was 7.9% (Narayan RR et al., Cancer. 2019) and 9.4% (Li M et al., Nat Genet. 2014), respectively. Compared with these data, our data is characterized by relatively higher ERBB2 alterations (54.5%: amplification in 27.3% and SNV in 27.3%) (Figure 1B). A higher prevalence of ERBB2 alteration was also reported in other studies on GBAC, with corresponding rates of 28.6% (amplification and overexpression, Nam AR et al., Oncotarget. 2016) and 36.4% (amplification only, Lin J et al., Nat Commun. 2021). The variations in ethnicity and culture might have contributed to the differences. This part is described in the Discussion section (Page 11, Line 19-23). In addition, the discrepancy in Figure 4A might be attributed to the difference in analyzed samples: our study included precancerous and metastatic lesions while the other two studies uniformly analyzed primary tumors.

Reference for reply 1)

• Kwon JH, Lee SC, Lee MA, Kim YJ, Kang JH, Kim JY, et al. Behaviors and Attitudes toward the Use of Complementary and Alternative Medicine among Korean Cancer Patients. Cancer Res Treat. 2019;51(3):851-60.

3) The authors try to describe and draw conclusions about the possibility of metastasis to metastasis spread in p.6, lines 6-10 "In our study, of 7 patients with 2 or more metastatic lesions, evidence of metastasis-to-metastasis spread was found in 2 patients (28.6%). In GB-A1 (Figure 2A), it appears that CBD, omentum 1-2, mesentery, and abdominal wall 2-4 lesions may originate from abdominal wall 1 (old) rather than from primary GBAC considering clone F." The authors conclude here that the spread arose from abdominal wall 1, but this lesion is only separated from the CBD lesion by 1 month. There is no history given about whether this timing difference is significant or if it was simply due to clinically-driven differences in when each lesion was sampled. Given the proximity of the CBD lesion to the original gall bladder cancer, it seems just as likely that all of these distant lesions were seeded from the CBD lesion. If this is the case, the author's conclusion about "metastasis to metastasis" spread does not seem strongly supported. It would be helpful if the authors could clarify this point and/or provide additional data to strengthen this conclusion.

We appreciate your valuable comment. As addressed above, the manuscript has been modified to reflect your comments.

Reviewer #2 (Public Review):

Minsu Kang et al. analyzed 11 patients with gallbladder adenocarcinoma using multi-point sampling. Mutational analysis revealed evolutional patterns during progression where the authors found metastasis-to-metastasis spread and the migration of a cluster of tumor cells are common in gallbladder adenocarcinomas. The signature analysis detected signatures 22 (aristolochic acid) and 24 (aflatoxin) in metastatic tumors. Overall, the analyses are well-performed using established algorithms. However, the manuscript is highly descriptive. Therefore, it is very difficult to understand what the novel findings are.

Major comments

1) The sections "Evolutionary trajectories and expansion of subclones during regional and distant metastasis", "Polyclonal metastasis and intermetastatic heterogeneity", "Mutational signatures during clonal evolution", and "Discussion" are highly descriptive which makes it difficult to understand what the novel and/or important findings are. Those sections would profit from reorganization.

Thank you for the important comment. We have reorganized the manuscript according to your comments.

1) In the "Evolutionary trajectories and expansion of subclones during regional and distant metastasis" section, unnecessary sentences have been removed and Figures 2 and 3 have been changed to make it simpler to understand how subclones spread during metastasis.

2) In the "Polyclonal metastasis and intermetastatic heterogeneity" section, after receiving feedback on statements that were conflicting (Reviewer #1's comment 4), we clarified the statements and removed any other extraneous sentences. Figures 2 and 3 have been changed to make it simpler to understand polyclonal metastasis and intermetastatic heterogeneity.

3) In the "Mutational signatures during clonal evolution" section, after receiving comments that Figures 4B and 4C were confusing (Essential Revisions #6), we moved Figure 4B to Figure 4—figure supplement 2. Unnecessary sentences have been removed. We emphasized signatures 22 and 24 highlighted during metastasis. This result was validated by using two additional tools, Signal (Degasperi A et al., Nat Cancer. 2020) and MuSiCa (Diaz-Gay M et al., BMC Bioinformatics. 2018).

4) In the Discussion section, duplicate descriptions and unnecessary extraneous explanations have been deleted. We emphasized that whereas aflatoxin and aristolochic acid had little impact on early cancer formation, their impacts could be more clearly seen in cancer cells that had already manifested (Page 13 Line 2-7). In addition, the limitations of the NGS test currently used in the clinical field were pointed out, and the clinical significance of this study was described (Page 13 Line 8-16).

2) What would enhance this paper is more of a connection between the bioinformatics analysis and the biology. Although the authors analyzed multi-point sequencing data well, this paper lacks in-depth discussion. I understand that the results in the paper are "computationally" the most likely. However, the impact is lost by an incomplete connection to biology.

As you commented, we analyzed the WES data obtained from patient samples by computational methods. In this study, we did not validate the various results using in vitro or in vivo models. However, we would like to emphasize the significance of our work because it is the first human study, covering the current theory of carcinogenesis from precancerous lesions to metastasis in GBAC. For example, polyclonal seeding has been previously confirmed in animal models (Cheung KJ et al., Science 2016). In humans, there have been reports in breast cancer (Ullah I et al., J Clin Invest. 2018) and colorectal cancer (Wei Q et al., Ann Oncol. 2017), but not in GBAC yet.

3) In addition to the above concern, it is difficult to comprehend the cohort as the detailed information is lacking. I would suggest providing a brief table that contains the number of collected samples, frozen or FFPE, the clinical information, etc. by sample.

Thank you for the constructive comment. Supplementary Table 1 was modified as you mentioned. It is now indicated from which organ, when, and by what method the tissue was obtained, what the tumor purity of the tissue was, and whether the tissue was fresh-frozen or FFPE. In addition, we updated the information about tissue acquisition sites in Figure 1A.

4) The mutations with very low allele frequency (< 1%) are discussed in the manuscript. However, no validation data is provided. Please add a description of the accuracy of the mutation calling considering the following concerns.

• FFPE samples are analyzed using the same method as frozen samples. FFPE contains much more artifacts. Is it adequate to use the same methods for both frozen and FFPE samples?

Thank you for the valuable comment. We also considered the FFPE artifacts. However, we did not remove the possible artifacts. This part has been described above. Please see Essential Revisions #5.

• How were those mutations with low allele frequency validated? Are those variants validated by other methods? Especially in FFPE.

Thank you for the important comment. Firstly, we discarded any low-quality, unreliable reads and variants according to the pre-specified filtering criteria used in previous literature analyzed with the Genomon2 pipeline (Yokoyama A et al., Nature. 2019, Kakiuchi N et al., Nature. 2020, Ochi Y et al., Nat Commun. 2021). In the Method section, we have added an explanation for this part (Page 16 Line 5-12).

As you commented, validation of low VAF mutation is required if the mutation is sample-specific. However, in this study, if a mutation in Supplementary File 1 has a low VAF in one sample, one of the other samples always has a higher VAF, which has passed our pre-specified filter. Therefore, validation is not required for that mutation. In addition, possible sequencing artifacts with low VAFs in FFPE tissues have been discussed above. Please see Essential Revisions #5.

• Is the low variant allele frequency (0.2~1%) significantly higher than the background noise level?

Thank you for the important comment. As you expected, FFPE samples had a higher number of sample-specific mutations than fresh-frozen ones in our study. However, we did not remove these mutations in the analysis of the FFPE samples. For a more detailed description, please see Essential Revisions #5.

5) The authors compared mutational signatures divided by stages or timings. How are the signatures calculated although each sample has a distinct number of somatic mutations? Did the authors correct the difference?

Thank you for the helpful comment. We classified all the mutations according to the specific criteria (Page 9 Line 9-18). For example, in Figure 4B (before revision, Figure 4C), mutations were classified by the timing of development during clonal evolution. After that, we could calculate the relative contributions of mutational signatures in each group using the three tools, Mutalisk (Lee J et al., Nucleic Acids Res. 2018), Signal (Degasperi A et al., Nat Cancer. 2020) and MuSiCa (Diaz-Gay M et al., BMC Bioinformatics. 2018). Although the number of mutations is different for each group, no additional correction was required because we compared the relative contributions among the groups.

6) In distant metastasis tumors, signatures 22 and 24 are increased. Those two signatures are strongly associated with a specific carcinogen. Although the clinical information lacks, do the authors think that those patients were exposed to those chemicals after the diagnosis? Why do the authors think the two signatures increased in the metastatic tumors? Were those signatures validated by other methods?

We appreciate your important and constructive comment.

1) We think that the patients might have been exposed to aristolochic acid or aflatoxin before or after the cancer diagnosis. Aristolochic acid is an ingredient of oriental herbal medicine (Debelle FD et al., Kidney Int. 2008, Hoang ML et al., Sci Transl Med. 2013). Given that all the patients in our cohort are Korean, and a recent study found that Korean cancer patients are frequently exposed to herbal medicines (Kwon JH et al., Cancer Res Treat 2019), one possible explanation is that some patients might have been exposed to herbal remedies containing aristolochic acid. On the other hand, aflatoxin is known to be contained in soybean paste and soy sauce, which are widely used in Korean food (Ok HE et al., J Food Prot. 2007). Nevertheless, we believe that further investigation is required because it is difficult to determine the etiology of signatures 22 and 24 with this limited patient data.

2) Summarizing the mutational signature results using the 3 different tools (Figure 4B and Figure 4—figure supplement 3), the signatures 22 and 24 are relatively rare in early carcinogenesis. However, the two signatures contributed more to late carcinogenesis and metastasis. Therefore, it is speculated that the two carcinogens appear to have little impact on the early stage of cancer development but might be highlighted in overt cancer cells. Further studies on this novel hypothesis are necessary.

3) During the revision process, signatures 22 and 24 highlighted in the metastasis stage were validated by two additional tools, Signal (Degasperi A et al., Nat Cancer. 2020) and MuSiCa (Diaz-Gay M et al., BMC Bioinformatics. 2018) (Figure 4—figure supplement 3). We updated this part in the Result (Page 9 Line 18-21) and Discussion (Page 13 Line 2-7) sections.

Reference for reply 1)

• Kwon JH, Lee SC, Lee MA, Kim YJ, Kang JH, Kim JY, et al. Behaviors and Attitudes toward the Use of Complementary and Alternative Medicine among Korean Cancer Patients. Cancer Res Treat. 2019;51(3):851-60.

7) Figures 2 are well-described. However, they are difficult for readers to fully understand. The colors for each clone are sometimes similar. The results of multi-time point and regional analyses in the cases with multiple sampling are not integrated. Driver mutations are separately described in the small phylogenetic trees. Evolutional patterns (linear or branching) are not described in the figures. Modifying the above concerns would improve the manuscript.

We appreciate your important comment.

1) In GB-S1, clones of similar colors were modified to be different colors.

2) Figures 2 and 3 have been modified to make them easier to understand by separating time and space more clearly.

3) Driver mutations are now indicated in both the phylogenetic tree and TimeScape result (Figures 2 and 3).

4) Evolutional patterns (linear or branching) can be discovered by examining the phylogenetic tree in Figures 2 and 3. In addition, we described each patient's evolutionary pattern more clearly in the manuscript.

8)"Among 6 patients having concurrent BilIN tissues, two patients were excluded from the further analysis because of low tumor purity in one patient and different mutational profiles between BilIN and primary GBAC in the other patient, suggesting different origins of the two tumors (Figure 1-figure supplement 2)." This seems cherry-picking. More explanation is necessary.

• How is the tumor purity? Although the authors use 0.2% variant allele frequency as true mutation (for example Table 2), is the tumor purity lower than 0,2%?

Thank you for the important comment. The calculated tumor purity of BilIN in the GB-S8 patient was 0.03 based on the WES data. We added this value to the manuscript (Page 6 Line 9) and Supplementary Table 1. Although variants were called in this case, the tumor purity was too low to estimate the allele-specific copy number, and thus sophisticated analysis as in other patients was not possible. In addition, the value of 0.2% in Table 2 is not the VAF, but cellular prevalence calculated by PyClone and CITUP. Although the value is low in the primary tumor, it is mentioned because it is high in metastatic lesions.

• BilIN and GBAC of GB-S7 have some shared mutations. Why do the authors conclude that BilIN and GBAC have distinct origins? Do the authors think that those shared mutations are germline mosaic mutations?

Thank you for the important comment.

1) We think that the BilIN and GBAC of the GB-S7 patient are tumors of different origins because BilIN and GBAC of the GB-S7 patient have different truncal mutations (Figure 1—figure supplement 2C). This is a markedly different feature compared to BilIN and GBAC samples of other patients. We have added an explanation for this part to the Results section (Page 6 Line 9-11).

2) We do not think that mosaicism occurred at the developmental stage. In addition, although some mutations were identified from both BilIN and GBAC, we cannot determine their importance because either one of the lesions had a very low VAF ranging from 0.001 to 0.04. If the mosaicism occurred only in the GB at the developmental stage, the VAF values of the shared mutations should be much higher than the current values, and the VAF values of the two BilIN and GBAC lesions should be similar.

• Was the copy number profile compared between BilIN and GBAC?

Thank you for the constructive comment. In this study, we obtained allele-specific copy numbers using Control-FREEC version 11.5 (Boeva V et al., Bioinformatics. 2012). The copy number of the mutations in the GB-S8 patient's BilIN could not be estimated by Control-FREEC due to low tumor purity (0.03). In the case of GB-S7, BilIN and GBAC were determined to be of a different tumor origin and thus disregarded from the analysis.

Author Response

Reviewer #1 (Public Review):

It's here where my very mild (I truly liked this article - it is well done, well written, and creative) comments arise. The implications for stochastic strategies immediately emerge in the early results - bimodal strategies come about from the introduction of two variables. There is not enough credence given to the field of stochastic behavior in the introduction - the introduction focuses too much on previous models of predator-prey interaction, and in fact, Figure 1, which should set up the main arguments of the article, shows a model that is only slightly different (slight predator adjustment) that is eventually only addressed in the Appendix (see below). The question of "how and when do stochastic strategies emerge?" is a big deal. Figure 1 should set up a dichotomy: optimal strategies are available (i.e., those that minimize Tdiff) which would predict a single unimodal strategy. Many studies often advocate for Bayesian optimal behavior, but multimodal strategies are the reality in this study - why? Because if you consider the finite attack distance and inability of fish to evoke maximum velocity escapes while turning, it actually IS optimal. That's the main point I think of the article and why it's a broadly important piece of work. Further framing within the field of stochastic strategies (i.e., stochastic resonance) could be done in the introduction.

We appreciate the comment provided by the reviewer. We changed the second paragraph of the introduction so as to focus more on the protean tactic (stochasticity). We added a new figure (Figure 1 in the new version) to conceptually show the escape trajectories (ETs) of a pure optimal tactic, a pure protean tactic, a combination of optimal and protean tactics, and an empirically observed multimodal pattern. We explained each tactic and described that the combination of the optimal and protean tactics still cannot explain the empirically observed multiple preferred ETs.

The revised paragraph (L49-66) is as follows: Two different escape tactics (and their combination) have been proposed to enhance the success of predator evasion [16, 17]: the optimal tactic (deterministic), which maximizes the distance between the prey and the predator (Figure 1A) [4, 14, 15, 18], and the protean tactic (stochastic), which maximizes unpredictability to prevent predators from adjusting their strike trajectories accordingly (Figure 1B) [19-22]. Previous geometric models, which formulate optimal tactics, predict a single ET that depends on the relative speeds of the predator and the prey [4, 14, 15, 18], and additionally, predator’s turning radii and sensory-motor delay in situations where the predator can adjust its strike path [23-25]. The combination of the optimal tactic (formulated by previous geometric models), which predicts a specific single ET, and the protean tactic, which predicts variability, can explain the ET variability within a limited angular sector that includes the optimal ET (Figure 1C). However, the combination of the two tactics cannot explain the complex ET distributions reported in empirical studies on various taxa of invertebrates and lower vertebrates (reviewed in [26]). Whereas some animals exhibit unimodal ET patterns that satisfy the prediction of the combined tactics or optimal tactic with behavioral imprecision (e.g., [27]), many animal species show multimodal ETs within a limited angular sector (esp., 90–180°) (Figure 1D) (e.g., [4, 5, 28]). To explore the discrepancy between the predictions of the models and empirical data, some researchers have hypothesized mechanical/sensory constraints [17, 29]; however, the reasons why certain animal species prefer specific multiple ETs remain unclear.

All experiments are well controlled (I especially liked the control where you varied the cutoff distance given that it is so critical to the model). Some of the figures require more labeling and the main marquee Figure 1 needs an overhaul because (1) the predator adjustment model that is only addressed in the Appendix shouldn't be central to the main introductory figure - it's the equivalent of the models/situations in Figure 6, and probably shouldn't take up too much space in the introductory text either (2) the drawing containing the model variables could be more clear and illustrative.

(1) According to this comment and comment #11 from reviewer #2, we moved the two panels in the figure (Figure 1B and D in the original version) to Appendix-figure 1, and accordingly, we changed the first paragraph of the Model section so as to clearly describe that we focus on Domenici’s model in this study (L103-108).

As for Figure 6 (Figure 7 in the new version) and related parts, we tempered our claims to clearly describe that our model has only the potential to explain the different patterns of escape trajectories observed in previous works. We would like to keep this figure in the main text because it is fundamental to explain the potential applicability of our model to other predator-prey systems.

(2) To alleviate the burden for readers, we added the model variables to the figure and made them colored (Figure 2B in the new version).

Finally, I think a major question could be posed in the article's future recommendations: Is there some threshold for predator learning that the fish's specific distribution of optimal vs. suboptimal choice prevents from happening? That is, the suboptimal choice is performed in proportion to its ability to differentiate Tdiff. This is "bimodal" in a sense, but a probabilistic description of the distribution (e.g., a bernoulli with p proportional to beta) would be really beneficial. Because prey capture is a zero-sum game, the predator will develop new strategies that sometimes allow it to win. It would be interesting if eventually the bernoulli description could be run via a sampler to an actual predator using a prey dummy; one could show that the predator eventually learns the pattern if the bernoulli for choosing optimal escape is set too high, and the prey has balanced its choice of optimal vs. suboptimal to circumvent predator learning.

We thank the reviewer for this constructive comment. Actually, we are now developing a dummy prey system. We added the following sentence in the Discussion to mention future research.

The added sentence (L496-499): Further research using a real predator and dummy prey (e.g., [48]) controlled to escape toward an optimal or suboptimal ET with specific probabilities would be beneficial to understand how the prey balances the optimal and suboptimal ETs to circumvent predator learning.

Reviewer #2 (Public Review):

First, it is unclear how the dummy predator is actuated. The description in the Methods section does not clearly address how rubber bands are used for this purpose.

To clearly mention how the dummy predator was actuated by rubber bands, we added a figure (Figure 3-figure supplement 3B) and the following sentences.

The added sentences (L608-611): The dummy predator was held in place by a metal pipe anchored to a four-wheel dolly, which is connected to a fixed metal frame via two plastic rubber bands (Figure 3—figure supplement 3B). The wheel dolly was drawn back to provide power for the dummy predator to strike toward the prey.

Second, the predator's speed, which previous research has identified as a critical factor during predator-prey interactions, is not measured from the motion of the dummy predator in the experiments. Instead, it is estimated using an optimization algorithm that utilizes the mathematical model and the prey-specific parameters. It is unclear why the authors chose this method over measuring velocity from their experiments. Since the prey fish are responding to a dummy predator moving toward them at a particular speed during the interaction, it is important to measure the speed of the predator or clearly explain why estimating it using an optimization procedure is more appropriate.

We chose this method (optimizing predator speed from the prey’s viewpoint) because there was no significant effect of predator speed on the escape trajectory in our experiment (L203-208). In other words, we considered that, at least in our case, the prey did not change the escape trajectory in response to the predator speed, and thus it would be more appropriate to use a specific predator speed estimated through an optimization algorithm from the prey’s point of view. It may be appropriate to use measured predator speed in other cases where the prey adjusts the escape trajectory in response to the change in predator speed. Therefore, we conducted a further analysis using actual predator speeds (both the predator speed at the onset of escape response, and the mean speed for the predator to cover the distance between the predator and prey). The results show that the model fit became worse when using measured predator speed per trial compared to the model using the fixed predator speed estimated through the optimization procedure (Table 3—source data 1; Figure 5—figure supplement 1). We added the above explanation in L219-226.

One of the major claims of this article is that the model can explain escape trajectories observed in other predator-prey systems (presented in Figure 6). Figure 6 panels A-C show the escape responses of different prey in response to some threatening stimuli. Further, panels D-F suggest that the empirical data can be predicted with the model. But the modeling parameters used to produce the escape trajectories in D-F are derived from the authors' experiments with fish, instead of the experiments with the species shown in panels A-C.

We thank the reviewer for this comment. We agree that this part in the previous version was an over-interpretation. Therefore, we tempered our statements to simply suggest that our approach has the potential to explain multiple ETs observed in other taxa. The revised sentences are as follows.

Abstract (L27-30): By changing the parameters of the same model within a realistic range, we were able to produce various patterns of ETs empirically observed in other species (e.g., insects and frogs): a single preferred ET and multiple preferred ETs at small (20–50°) and large (150–180°) angles from the predator.

Results (L395-407): Potential application of the model to other ET patterns. ...(sip)... To investigate whether our geometric model has the potential to explain these different ET patterns, we changed the values of model parameters (e.g., Upred, Dattack) within a realistic range, and explored whether such adjustments can produce the ET patterns observed in the original work. ...(sip)... These results indicate that our model has the potential to explain various patterns of observed animal escape trajectories.

Discussion (L538-548): We show that our model has the potential to explain other empirically observed ET patterns (Figure 7). ...(sip)... Further research measuring the escape response in various species and applying the data to our geometric model is required to verify the applicability of our geometric model to various predator-prey systems.

David Spivak discusses how category theory may appeal to different political ideologies for a variety of reasons.

This is a post I made on the Slack public channel asking about whether or not Hypothes.is indexes replies. A tech support membered confirmed this is true.

However, Obsidian's Hypothes.is plugin does pull replies. It should be noted that default settings don't capture updates to the annotations or tags.

This made me think about the meaning of hidden curriculum. How are we ensuring as educators that we are addressing state standards while also addressing the needs of our students social and emotionally. This also makes me think about how we can intertwine transformative healing practices into our everyday curriculum

Author Response

Reviewer #2 (Public Review):

Grasses develop morphologically unique stomata for efficient gas exchange. A key feature of stomata is the subsidiary cell (SC), which laterally flanks the guard cell (GC). Although it has been shown that the lateral SC contributes to rapid stomatal opening and closing, little is known about how the SC is generated from the subsidiary mother cell (SMC) and how the SMC acquires its intracellular polarity. The authors identified BdPOLAR as a polarity factor that forms a polarity domain in the SMC in a BdPAN1-dependent manner. They concluded that BdPAN1 and BdPOLAR exhibit mutually exclusive localization patterns within SMCs and that formative SC division requires both. Further mutant analysis showed that BdPAN1 and BdPOLAR act in SMC nuclear migration and the proper placement of the cortical division site marker BdTANGLED1, respectively. This study reveals a unique developmental process of grass stomata, where two opposing polarity factors form domains in the SMC and ensure asymmetric cell division and SC generation.

The findings of this study, if further validated, are novel and interesting. However, I feel that the data presented in the current manuscript do not fully support some crucial conclusions. The lack of dual-color images is the weakest point of this study. If it is technically impossible to add them, alternative analyses are needed to validate the main conclusions.

1) Is BdPOLAR-mVenus functional? Although the authors interpret that weak BdPOLAR-mVenus expression partially rescued the bdpolar mutant phenotype in Fig. S4D, the localization pattern visualized by BdPOLAR-mVenus may not be completely reliable with this partial rescue activity.

This is indeed a valid point. The partial complementation of weakly expressing translational reporters (Figure 3–figure supplement 1D) and the weak effect of BdPOLAR-mVenus overexpression lines (Figure 3–figure supplement 1J) at least suggest partial functionality which is strongly dependent on dosage. Yet the localization pattern and the temporal dynamics might indeed not fully reflect the spatiotemporal dynamics of the endogenous BdPOLAR. This criticism is, however, true for any transgenic reporter line–even when fully complementing–as the requirement for dosage, stability, and turnover likely varies strongly between different protein classes and functions.

Nonetheless, we have added a sentence on p. 7, which mentions this potential caveat.

2) Regardless of the functionality of the tagged protein, the authors need to provide more information on their localization. For example, is there a difference in polarity pattern depending on expression level? Does overexpressed BdPOLAR-mVenus invade the BdPAN1 zone? In such cases, might the loss of BdPOLAR polarity in the bdpan1 mutant be a side effect of overexpression, not PAN1 exclusion? Does BdPOLAR expression (no tag) show a dose-dependent effect, similar to the mVenus-tagged protein?

The difference in polarity patterns in bdpan1 mutants and wild-type does not depend on expression level. BdPOLAR-mVenus was crossed into bdpan1 and mutant and wild-type siblings in the F2 generation were analyzed. This means that the data presented in Fig. 3E and F show exactly the same transgene insertion line in wt and bdpan1 and were imaged with the same setting for comparability. Therefore, the difference in localization is not due to different expression levels but indeed reflects a PAN1-dependent effect.

To address if BdPOLAR without a tag is also sensitive to dosage, we have generated an untagged complementation line that includes the untagged, genomic locus of BdPOLAR including promoter (-3.1kb) and terminator (+1.1kb). Yet, even though this construct is much better at rescuing the mutant, we still see remaining defects in T0 lines (Figure 3–figure supplement 1K) suggesting that even without a tag we cannot fully recapitulate wild-type functionality. Yet, to actually measure protein levels of untagged BdPOLAR, we would need to raise an antibody against BdPOLAR, which we think is clearly out of the scope of this study.

3) A major conclusion of this study was that the polarity domains of BdPOLAR and BdPAN1 are mutually exclusive. However, not all the cells in the figures were consistent with this statement. For example, the BdPOLAR signals at the GMC/SMC interphase appear to match BdPAN1 localization (compare 0:03 s in Video 1 and 0:20 s in Video 2 [top cell]). The 3D rendered image in Fig. 2F shows that BdPOLAR is excluded near the GMC on the front side of the SMC, where BdPAN1 is not localized. Some cells did not exhibit polarization (Fig. 3A, bottom left; Fig. 3E, bottom left). The most convincing data are the dual-color images of these two proteins. Otherwise, a sophisticated image analysis is required to support this conclusion.

We agree that dual-color image analysis would have provided the most convincing data. As mentioned in our answers to the reviewing editor and reviewer 1, we have generated a dual marker line (BdPAN1p:BdPAN1-CFP; BdPOLARp:BdPOLAR-mCitrine), yet the BdPAN1-CFP signal (compared to mCitrine signal) was too weak to visualize the proximal BdPAN1 domain.

This issue was also raised by reviewer 1 and deemed an essential revision. To determine how BdPOLAR and BdPAN1 relate spatially to each other, we have added data in Figure 2E where we manually traced mature SMC outlines to determine BdPOLAR-mVenus and BdPAN1-mCitrine occupancy along the SMC’s circumference. This confirmed that the polarization is indeed opposite yet not perfectly reciprocal (see details above, Essential Revisions #1).

Finally, we realized that the 3D image renderings were more confusing than helpful and we removed them from the revised version.

4) Another central conclusion was that BdPOLAR was excluded at the future SC division site, marked with BdTANGLED1. However, these data are also not very convincing, as such specific exclusion cannot be seen in some figure panels (e.g., Fig. 3A, bottom left; Fig. 3E, all three cells on the left). If dual-color imaging is not feasible, a quantitative image analysis is needed to support this conclusion.

As for point 3, this was also criticized by reviewer 1 and deemed an essential revision by the reviewing editor.

To determine whether the absence of BdPOLAR signal and the presence of BdTAN1 signal colocalize, we again manually traced mature SMC outlines to determine BdPOLAR-mVenus and BdTAN1-mCitrine occupancy along the SMC’s circumference. We plotted the relative average fluorescence intensity in Figure 4G-I nicely showing that BdTAN1 indeed resides in the BdPOLAR gaps above and below the GMC (again, details above, Essential Revisions #2).

5) I could not find detailed imaging conditions and data processing methods. Are Figs. 2B and 2E max-projection or single-plane images? If they are single-plane images, which planes of the SMC are observed? In addition, how were Figs. 2C and 2F rendered? (e.g., number of images, distance intervals, processing procedures). This information is important for data interpretations.

We agree that we might not have provided sufficient imaging condition details and have added more details regarding image acquisition in the method part (p. 20). We always use a consistent depth and show the midplane of SMCs. As mentioned above, we removed Figs. 2C and 2F and the supplemental movies as these data did not seem to be helpful.

6) [Minor point] The authors should clearly describe where BdPAN1 is expressed and localized. Is it expressed in the GMC and localized at the GMC/SMC interface? Alternatively, is it expressed and localized in the SMC?

BdPAN1 is expressed throughout the epidermis but starts to strongly accumulate at the GMC/SMC interface. According to the literature (Cartwright et al 2009 with immunostainings against ZmPAN1 and Sutimantanapi et al. 2014 with PAN1 and PAN2 reporter) and our own observations (Fig. S3), this accumulation occurs in the SMC rather than in the GMC. In Fig. S3A, third panel, second GMC from the top, for example, one can see that the early PAN1 polarity domain expands beyond the GMC/SMC interface suggesting that it is indeed forming in SMCs rather than in GMCs. We have specified this in the text more clearly now (p. 5).

Author Response

Reviewer #1 (Public Review):

The research investigates the genetic basis for resistance to high CO2 levels in the human pathogenic fungus Cryptococcus neoformans. Screening collections of over 5,000 gene deletion strains revealed 96 with impaired growth, including a set of genes all related to the same RAM signaling pathway. Further genetic dissection was able compellingly to place where this pathway lies relative to upstream inputs and through the isolation of suppressor mutants as potential downstream targets of the pathway. Given the high levels of CO2 encountered by fungi in the human host, this work may provide new directions for the control of disseminated fungal disease.

The research presents both strengths and weaknesses.

Strengths include:

(1) One of the largest scale analyses of genes involved in growth under high CO2 concentrations in a fungus, revealing a set of just under 100 mutants with impaired growth.

(2) Elegant genetic epistasis analysis to show where different components fit within a pathway of transmission of CO2 exposure. For example, over expression of one of the kinases, Cbk1, can overcome the CO2-sensitivity of mutations in the CDC24 or CNA1 genes (but not in the reciprocal overexpression direction).

(3) Isolation of suppressor mutations in the cbk1 background, now able to grow at high CO2 levels, was able to lead to the identification of two genes. Follow up characterization, which included examining in vitro phenotypes, gene expression analysis, and impact during mouse infection was able to reveal that the two suppressors restore a subset of the phenotypes impacted by mutation of CBK1. Indeed, one conclusion from this careful work is that the reduced virulence of the cbk1 mutant is not due to its sensitivity to high levels of CO2, perhaps an unexpected finding given the original goals of the study towards linking CO2 sensitivity with decreased virulence.

Weaknesses include:

(1) What is the rationale for examining gene expression using the NanoString technology of 118 genes rather than a more genome-wide approach such as RNA-sequencing?

(2) Without additional species examined, some of the conclusions about differences in impact between ascomycetes and basidiomycetes might instead reflect differences between species. For example, RAM mutants in other strains of C. neoformans do not exhibit so strong a temperature sensitive phenotype. Or to extend the comparison further, one might assume given the use of CO2 for Drosophila manipulations that the RAM pathway components in an insect would not be required for surviving high CO2.

(3) Given the relative ease of generate progeny of this species, it would have been informative to explore if the suppressors of cbk1 also suppressed the loss of genes like CDC24, CNA1, etc, equivalent to the experiment performed of overexpression of CBK1 in those backgrounds.

We thank the reviewer for the kind summary of our work and the highlights of the major findings. We chose NanoString because we have already generated a probe set of 118 genes that are differentially expressed in response to CO2 based on RNA-seq profiles of multiple natural cryptococcal isolates in a separate study. Nanostring allowed us to focus on CO2 relevant transcripts and do multiple replicates and conditions in a way that is not practical using RNA-Seq.

Although the RAM pathway has not been extensively characterized in different species of Cryptococcus, we do know that RAM pathway mutants lead to pseudohyphal growth in multiple strain backgrounds including two different species of Cryptococcus (Magditch, Liu, Xue, & Idnurm, 2012; Walton, Heitman, & Idnurm, 2006). We have added corresponding references and discussed this point on lines 167-169.

We agree with the reviewer that it would be interesting to test the effects of the cbk1Δ suppressor mutations in the backgrounds of other CO2-sensitive gene knockout strains. This is part of our plan for future investigation in characterizing the signaling pathways involved in CO2 tolerance.

Reviewer #2 (Public Review):

In the paper by Chadwick et al., the authors identify the molecular determinants of CO2 tolerance in the human fungal pathogen Cryptococcus neoformans. The authors have screened a collection of deletion mutants to identify the genes that are sensitive at 37oC (host temperature) and elevated CO2 levels. The authors identified that the genes responsible for CO2 sensitivity are involved in the pathways responsible for thermotolerance mechanisms such as Calcineurin, Ras1-Cdc24, cell wall integrity, and the Regulator of Ace2 and Morphogenesis (RAM) pathways. Moreover, they identified that the mutants of the RAM pathway effector kinase Cbk1 were most sensitive to elevated temperature and CO2 levels. This study uncovers the previously unknown role of the RAM pathway in CO2 tolerance. Transcriptome data indicates that the deletion of CBK1 results in an alteration in the expression of CO2-related genes. To identify the potential downstream targets of Cbk1, the authors performed a suppressor screen and obtained the spontaneous suppressor mutants that rescued the sensitivity of cbk1 mutants to elevated temperature and CO2. Through this screen, the authors identified two suppressor groups that showed a modest improvement in growth at 37˚C and in presence of CO2.

Interestingly, from the suppressor screen, the authors identified a previously known interactor of Cbk1 which is SSD1, and an uncharacterized gene containing a putative Poly(A)-specific ribonuclease (PARN) domain named PSC1 (Partial Suppressor of cbk1Δ) which acts downstream of Cbk1. Deletion of these two genes in cbk1 null mutants rescued the sensitivity to elevated CO2 levels and temperature but did not fully rescue the ability to cause disease in mice.

This study highlights the underappreciated role of the host CO2 tolerance and its importance in the ability of a fungal pathogen to survive and cause disease in host conditions. The authors claim to gain insight into the genetic components associated with carbon dioxide tolerance. The experimental results including the data presented, and conclusions drawn do justice to this claim. Overall, it is a well-written manuscript. However, some sections need improvement in terms of clarity and experimental design.

• One major drawback of the study is the virulence assay performed to test the ability of cbk1 mutants to cause the disease in the mouse model. The cbk1 null mutants are thermosensitive in nature. Using these mutants, establishing the virulence attributes in mice would undermine the mutants' ability to infect mice as they won't be able to survive at the host body temperature.

• The rationale for choosing the genes to test further is not clear in two instances in the study. a) From a list of 96 genes, how do the authors infer the pathways involved? Was any pathway analysis performed that helped them in shortlisting the pathways that they subsequently tested? A GO term analysis of the list of genes identified through the genetic screen would be more helpful to get an overview of the pathways involved in CO2 tolerance. b) The authors do not clearly mention why they chose only four genes to test for the CO2 sensitivity out of 16 downregulated genes identified from the nano string analysis.

• It would be more useful to the readers if the authors could also include a thorough analysis of the presence of the putative PARN domain-containing protein across various fungal species rather than mentioning that it is only observed in C. neoformans and S. pombe. Also, the authors may want to discuss the known role(s) of SSD1, if any, in pathogenic ascomycetous yeasts so that the proposed functional divergence is supported further.

We are glad that the reviewer appreciated the approach, the findings, and the significance of this research, and we are grateful for the helpful suggestions to improve the manuscript.

To remove temperature sensitivity as a variable when testing virulence, we have added a new infection model in the revised manuscript to test the cbk1Δ mutant and its suppressors. This infection model uses the Galleria mellonella larvae as a host. G. mellonella larvae are commonly used to test virulence for temperature sensitive strains as the body temperature of the larvae is similar to that of the environment. We performed cryptococcal infection in this model and the larvae were kept at 30°C rather than at 37°C. The results of these experiments are now described in results section 5 and shown in Figure 6 of the manuscript. The data using the larva-infection model supports our original conclusion about the virulence of these strains observed in mouse models.

We performed a GO term analysis of the hits from our screening, but did not find any significant or outstanding pathways. From our list of 96 genes, we chose to focus on the RAM pathway because the mutants were among the most sensitive to CO2. We have added an explanation for the genes we decided to test for host CO2 level sensitivity from the 16 downregulated genes on lines 139-141.

Through Blast searching, we have found that the PARN domain-containing protein has homologs in other basidiomycetes. There might be some homologs in a few zygomycetes and ascomycetes but the confidence scores were so low that we deemed unlikely. We now report this in the manuscript on lines 210-213, “This domain was previously reported to be found in S. pombe (Marasovic, Zocco, & Halic, 2013). Interestingly, through a Blast search of the PARN domain, we did not identify this domain in the genomes of S. cerevisiae, C. albicans or other ascomycetes, but found it in Basidiomycetes and higher eukaryotes”.

Ssd1 has been studied in the pathogenic yeast Candida albicans and is also regulated by Cbk1 in this organism. We have added a discussion about possible functions of Ssd1 in C. neoformans based on references to studies in C. albicans in the discussion section on lines 401-408. “In C. albicans, Ssd1 plays an important role in polarized growth and hyphal initiation by negatively regulating the transcription factor Nrg1 (H. J. Lee, Kim, Kang, Yang, & Kim, 2015). The observation that cbk1Δpsc1Δ and cbk1Δssd1Δ suppressor mutants partially rescue cell separation defects or depolarized growth suggests that C. neoformans may primarily utilize Ssd1/Psc1 rather than a potential Ace2 homolog to regulate cell separation or polarization. Differential regulation of target mRNA transcripts by Ssd1 and Psc1 may explain the functional divergence of the RAM pathway we observed here between basidiomycete Cryptococcus and the ascomycete yeasts.”

Reviewer #3 (Public Review):

In this work the authors identify genes and pathways important for CO2 and thermotolerance in Cryptococcus neoformans. They additionally rule out the contribution of the bicarbonate or cAMPdependent activation of adenylyl cyclase to this pathway, which is important for CO2 sensing in other fungi, further solidifying the need to characterize CO2 sensing in basidiomycetes. The authors establish the importance of focusing on CO2 tolerance by testing the impact of CO2 on fluconazole susceptibility with varied pH, suggesting the ability of CO2 to sensitize cryptococcal cells to fluconazole. Furthermore, the authors compared the CO2 tolerance of clinical reference strains to environmental isolates. The characterization of the RAM pathway Cbk1 kinase illustrated the integration of multiple stress signaling pathways. By using a series of CBK1OE insertions in strains with deletions in other pathways, the ability of Cbk1 over-expression to rescue several strains from CO2 sensitivity was apparent. Additionally, NanoString expression analysis comparing cbk1∆ to H99 validated the author's screen of CO2-sensitive mutants as 16/57 downregulated genes were found in their screen, further confirming the interconnected nature of these pathways. The importance of the RAM pathway in maintaining CO2 and thermotolerance was also incredibly clear.

Perhaps most interestingly, the authors identify suppressor colonies with distinctive phenotypes that allowed for the characterization of downstream effectors of the RAM pathway. These suppressor colonies were found to have mutations in SSD1 and PSC1 which somewhat restore growth at 37oC with CO2 exposure. Further confirming the importance of the RAM pathway, the cbk1∆ strain had markedly attenuated virulence during infection. Interestingly, the generated suppressor strains had varying impacts on fungal infection in vivo. While the sup1 suppressor was completely cleared from the lungs during both intranasal and IV infection, the sup2 strain, containing mutations in SSD1, maintained a high fungal load in the lungs and was able to disseminate into host tissues during IV infection but not intranasal infection.

The authors make a strong case for the exploration of thermotolerance and CO2 tolerance as contributors to virulence. Through screening and characterization of RAM pathway kinase CBK1's ability to rescue other mutants from CO2 sensitivity, the overlapping contributions of several signaling pathways and the importance of this kinase were revealed. This work is important and will be valuable to the field. However, the cbk1∆ strain does show reduced melanization, urease secretion, and higher sensitivity to cell wall stressor Congo Red in SI Appendix, Figure S4. While the authors make a strong argument that these well-established virulence factors are not perfect predictors of virulence in vivo, the cbk1∆ strain is not an example of such a case as it does have defects in these important factors in addition to thermotolerance and CO2 tolerance. Not acknowledging the changes in these virulence factors in the cbk1∆ and their potential contribution to phenotypes observed is a weakness of the manuscript. Interestingly, the sup1 and sup2 strains also rescue these virulence factors compared to cbk1∆. Additionally, the assertion that "the observation that only sup2 can survive, amplify, and persist in animals stresses the importance of CO2 tolerance in cryptococcal pathogens" due to the sup2's slightly higher CO2 tolerance compared to sup1, could be better supported by the data. These suppressors did not restore transcript abundances of the differentially expressed genes to WT levels, suggesting post-transcriptional regulation. However, there may be differences in the ability of sup2 to resist stress better than sup1 especially given the known Ssd1 repression of transcript translation in S. cerevisiae. Finally, pH appears to impact the sup1 and sup2 strain's sensitivity to CO2 in SI Appendix Figure 4. This could be better explained and interrogated in the manuscript. Finally, this work includes a variety of genes in several signaling pathways. The paper would be greatly clarified by a graphical abstract indicating how CBK1 may be integrating these pathways or by indicating which genes belong to which pathways in the Figure 1 legend to make this figure easier to follow.

We thank the reviewer for the thorough summary of the study. We appreciate the reviewer’s enthusiasm about this study as well as constructive critiques on the manuscript. Indeed, the suppressor mutations in the cbk1Δ mutant rescue more phenotypes of cbk1Δ in vitro than just thermotolerance and CO2 tolerance (Supplemental Figure 5), which could benefit the survival of these suppressor strains in vivo compared to the original the cbk1Δ mutant. However, between the sup1 and the sup2 mutants, the only clear difference in growth we observed was in host levels of CO2 and temperature. There was no obvious difference in their resistance to Congo red (cell wall stress), melanization, susceptibility to FK506 (calcineurin pathway inhibitor), sensitivity to H2O2 (ROS), or urease (Supplemental Figure 5). Nonetheless, we agree with the reviewer that there could be other reasons which may influence the outcome in vivo, given that the host environment is more complex than we know. We have changed our wording in the manuscript to make it clear that contribution of better tolerance of CO2 to better survival of the sup2 mutant is only our hypothesis and there could be other unrecognized contributing factors. “The only in vitro difference observed between sup1 and sup2 was better growth of sup2 at host CO2 levels which may explain the difference in their ability to propagate and persist in the mouse lungs. However, due to the complexity of the host environment, there could be other unrecognized factors contributing to their growth difference in vivo.” (Lines 276279).

About growth at different pH levels, C. neoformans tends to grow better at lower pH, closer to pH 5. This fungus can grow at pH 3, the lowest pH that our lab had tested (it may be able to sustain viability even at pH 2 based on others’ conference presentations). The high temperature/CO2 combined with neutral or high pH likely causes worse growth of both H99 and the mutants tested.

We tried making a model to integrate all the pathways and factors identified in this work as the reviewer suggested. However, in this process, we found it difficult to propose a model. Although the current findings clearly demonstrate the importance of Cbk1 in thermotolerance and CO2 tolerance (overexpression of CBK1 can partially restore thermotolerance and/or CO2 tolerance in the mutants defective in the cell wall integrity pathway, the calcineurin pathway or the Cdc24-Ras1 pathway, and that the reciprocal overexpression of these genes in the cbk1∆ mutant does not rescue any of the cbk1∆ mutant’s defects), we do not know the exact mechanisms underlying this phenomenon. Do these pathways directly interact with Cbk1, affect its phosphorylation status, or alter its subcellular localization? Or do these pathways act through some other massagers to indirectly activate Cbk1 or maybe Cbk1’s downstream targets? These are the questions that warrant further investigations in the future. To be prudent, we think it is better not to propose a model at this point given the uncertainty of the mechanism. The mutants belonging to each of the pathways are clearly specified in the texts in this revised manuscript to help orient the readers. For example “As the RAM pathway effector kinase mutant cbk1Δ showed the most severe defect in thermotolerance and CO2 tolerance compared to the mutants of the other pathways, we first overexpressed the gene CBK1 in the following mutants, cdc24∆ (Ras1-Cdc24), mpk1∆ (CWI), cna1∆ (Calcineurin), and the cbk1Δ mutant itself, and observed their growth at host temperature and host CO2 (Figure 2B)...”

Author Response

Public Evaluation Summary:

The authors re-analyzed a previously published dataset and identify patterns suggestive of increased bacterial biodiversity in the gut may creating new niches that lead to gene loss in a focal species and promote generation of more diversity. Two limitations are (i) that sequencing depth may not be sufficient to analyze strain-level diversity and (ii) that the evidence is exclusively based on correlations, and the observed patterns could also be explained by other eco-evolutionary processes. The claims should be supported by a more detailed analysis, and alternative hypotheses that the results do not fully exclude should be discussed. Understanding drivers of diversity in natural microbial communities is an important question that is of central interest to biomedically oriented microbiome scientists, microbial ecologists and evolutionary biologists.

We agree that understanding the drivers of diversity in natural communities is an important and challenging question to address. We believe that our analysis of metagenomes from the gut microbiomes is complementary to controlled laboratory experiments and modeling studies. While these other studies are better able to establish causal relationships, we rely on correlations – a caveat which we make clear, and offer different mechanistic explanations for the patterns we observe.

We also mention the caveat that we are only able to measure sub-species genetic diversity in relatively abundant species with high sequencing depth in metagenomes. These relatively abundant species include dozens of species in two metagenomic datasets, and we see no reason why they would not generalize to other members of the microbiome. Nonetheless, further work will be required to extend our results to rarer species.

Our revised manuscript includes two major new analyses. First, we extend the analysis of within-species nucleotide diversity to non-synonymous sites, with generally similar results. This suggests that evolutionarily older, less selectively constrained synonymous mutations and more recent non-synonymous mutations that affect protein structure both track similarly with measures of community diversity – with some subtle differences described in the manuscript.

Second, we extend our analysis of dense time series data from one individual stool donor and one deeply covered species (B. vulgatus) to four donors and 15 species. This allowed us to reinforce the pattern of gene loss in more diverse communities with greater statistical support. Our correlational results are broadly consistent with the predictions of DBD from modeling and experimental studies, and they open up new lines of inquiry for microbiome scientists, ecologists, and evolutionary biologists.

Reviewer #1 (Public Review):

This paper makes an important contribution to the current debate on whether the diversity of a microbial community has a positive or negative effect on its own diversity at a later time point. In my view, the main contribution is linking the diversity-begets-diversity patterns, already observed by the same authors and others, to genomic signatures of gene loss that would be expected from the Black Queen Hypothesis, establishing an eco-evolutionary link. In addition, they test this hypothesis at a more fine-grained scale (strain-level variation and SNP) and do so in human microbiome data, which adds relevance from the biomedical standpoint. The paper is a well-written and rigorous analysis using state-of-the-art methods, and the results suggest multiple new experiments and testable hypotheses (see below), which is a very valuable contribution.

We thank the reviewer for their generous comments.

That being said, I do have some concerns that I believe should be addressed. First of all, I am wondering whether gene loss could also occur because of environmental selection that is independent of other organisms or the diversity of the community. An alternative hypothesis to the Black Queen is that there might have been a migration of new species from outside and then loss of genes could have occurred because of the nature of the abiotic environment in the new host, without relationship to the community diversity. Telling the difference between these two hypotheses is hard and would require extensive additional experiments, which I don't think is necessary. But I do think the authors should acknowledge and discuss this alternative possibility and adjust the wording of their claims accordingly.

We concur with the reviewer that the drivers of the correlation between community diversity and gene loss are unclear. Therefore, we have now added the following text to the Discussion:

“Here we report that genome reduction in the gut is higher in more diverse gut communities. This could be due to de novo gene loss, preferential establishment of migrant strains encoding fewer genes, or a combination of the two. The mechanisms underlying this correlation remain unclear and could be due to biotic interactions – including metabolic cross-feeding as posited by some models (Estrela et al., 2022; San Roman and Wagner, 2021, 2018) but not others (Good and Rosenfeld, 2022) – or due to unknown abiotic drivers of both community diversity and gene loss.”

Additionally, we have revised Figure 1 to show that strain invasions/replacements, in addition to evolutionary change, could be an important driver of changes in intra-species diversity in the microbiome.

Another issue is that gene loss is happening in some of the most abundant species in the gut. Under Black Queen though, we would expect these species to be most likely "donors" in cross-feeding interactions. Authors should also discuss the implications, limitations, and possible alternative hypotheses of this result, which I think also stimulates future work and experiments.

We thank the reviewer for raising this point. It is unclear to us whether the more abundant species would be donors in cross-feeding interactions. If we understand correctly, the reviewer is suggesting that more abundant donors will contribute more total biomass of shared metabolites to the community. This idea makes sense under the assumption that the abundant species are involved in cross-feeding interactions in the first place, which may or may not be the case. As our work heavily relies on a dataset that we previously analyzed (HMP), we wish to cite Figure S20 in Garud, Good et al. 2019 PLoS Biology in which we found there are comparable rates of gene changes across the ~30 most abundant species analyzed in the HMP. This suggests that among the most abundant species analyzed, there is no relationship between their abundance and gene change rate.

That being said, we acknowledge that our study is limited to the relatively abundant focal species and state now in the Discussion: “Deeper or more targeted sequencing may permit us to determine whether the same patterns hold for rarer members of the microbiome.”

Regarding Figure 5B, there is a couple of questions I believe the authors should clarify. First, How is it possible that many species have close to 0 pathways? Second, besides the overall negative correlation, the data shows some very conspicuous regularities, e.g. many different "lines" of points with identical linear negative slope but different intercept. My guess is that this is due to some constraints in the pathway detection methods, but I struggle to understand it. I think the authors should discuss these patterns more in detail.

We sincerely thank the reviewer for raising this issue, as it prompted us to investigate more deeply the patterns observed at the pathway level. In short, we decided to remove this analysis from the paper because of a number of bioinformatics issues that we realized were contributing to the signal. However, in support of BQH-like mechanisms at play, we do find evidence for gene loss in more diverse communities across multiple species in both the HMP and Poyet datasets. Below we detail our investigation into Figure 5b and how we arrived at the conclusion that is should be removed:

(1) Regarding data points in Figure 5B where many focal species have “zero pathways”,we firstly clarify how we compute pathway presence and richness. Pathway abundance data per species were downloaded from the HMP1-2 database, and these pathway abundances were computed using HUMAnN (HMP Unified Metabolic Analysis Network). According to HUMAnN documentation, pathway abundance is proportional to the number of complete copies of the pathway in the community; this means that if at least one component reaction in a certain pathway is missing coverage (for a sample-species pair), the pathway abundance may be zero (note that HUMAnN also employs “gap filling” to allow no more than one required reaction to have zero abundance). As such, it is likely that insufficient coverage, especially for low-abundance species, causes many pathways to report zero abundance in many species in many samples. Indeed, 556 of the 649 species considered had zero “present” pathways (i.e. having nonzero abundance) in at least 400 of the 469 samples (see figure below).

(2) We thank the reviewer for pointing out the “conspicuous regularities” in Figure 5B,particularly “parallel lines” of data points that we discovered are an artifact of the flawed way in which we computed “community pathway richness [excluding the focal species].” Each diagonal line of points corresponds to different species in the same sample, and because community pathway richness is computed as the total number of pathways [across all species in the sample] minus the number of pathways in the focal species, the current Figure 5B is really plotting y against X-y for each sample (where X is a sample’s total community pathway richness, and y is the pathway richness of an individual species in that sample). This computation fails to account for the possibility that a pathway in an excluded focal species will still be present in the community due to redundancy, and indeed BQH tests for whether this redundancy is kept low in diverse communities due to mechanisms such as gene loss.

We attempted to instead plot community pathway richness defined as the number of unique pathways covered by all species other than the focal species. This is equivalent to [number of unique pathways across all species in a sample] minus the [number of pathways that are ONLY present in the focal species and not any other species in the sample]. However, when we recomputed community pathway richness this way, it is rare that a pathway is present in only one species in a sample. Moreover, we find that with the exception of E. coli, focal species pathway richness tended to be very similar across the 469 samples, often reaching an upper limit of focal species pathway richness observed. (It is unclear to what extent lower pathway richnesses are due to low species abundance/low sample coverage versus gene loss). This new plot reveals even more regularities and is difficult to interpret with respect to BQH. (Note that points are colored by species; the cluster of black dots with outlying high focal pathway richness corresponds to the “unclassified” stratum which can be considered a group of many different species.)

Overall, because community pathway richness (excluding a focal species) seems to primarily vary with sample rather than focal species in this dataset when using the most simple/strict definition of community pathway richness as described above, it is difficult to probe the Black Queen Hypothesis using a plot like Figure 5B. As pointed out by reviewers, lack of sequencing depth to analyze strain-level diversity and accurately quantify pathway abundance, irrespective of species abundance, seems to be a major barrier to this analysis. As such, we have decided to remove Figure 5B from the paper and rewrite some of our conclusions accordingly.

Finally, I also have some conceptual concerns regarding the genomic analysis. Namely, genes can be used for biosynthesis of e.g. building blocks, but also for consumption of nutrients. Under the Black Queen Hypothesis, we would expect the adaptive loss of biosynthetic genes, as those nutrients become provided by the community. However, for catabolic genes or pathways, I would expect the opposite pattern, i.e. the gain of catabolic genes that would allow taking advantage of a more rich environment resulting from a more diverse community (or at least, the absence of pathway loss). These two opposing forces for catabolic and biosynthetic genes/pathways might obscure the trends if all genes are pooled together for the analysis. I believe this can be easily checked with the data the authors already have, and could allow the authors to discuss more in detail the functional implications of the trends they see and possibly even make a stronger case for their claims.

We thank the reviewer for their suggestion. As explained above, we have removed the pathway analysis from the paper due to technical reasons. However, we did investigate catabolic and biosynthetic pathways separately as suggested by the reviewer as we describe below:

We obtained subsets of biosynthetic pathways and catabolic pathways by searching for keywords (such as “degradation” for catabolic) in the MetaCyc pathway database. After excluding the “unclassified” species stratum, we observe a total of 279 biosynthetic and 167 catabolic pathways present in the HMP1-2 pathway abundance dataset. Using the corrected definition of community pathway richness excluding a focal species, for each pathway type—either biosynthetic or catabolic—we plotted focal species pathway richness against community pathway richness including all pathways regardless of type:

We observe the same problem where, within a sample, community pathway richness excluding the focal species hardly varies no matter which focal species it is, due to nearly all of its detected pathways being present in at least one other species; this makes the plots difficult to interpret.

Reviewer #2 (Public Review):

The authors re-analysed two previously published metagenomic datasets to test how diversity at the community level is associated with diversity at the strain level in the human gut microbiota. The overall idea was to test if the observed patterns would be in agreement with the "diversity begets diversity" (DBD) model, which states that more diversity creates more niches and thereby promotes further increase of diversity (here measured at the strain-level). The authors have previously shown evidence for DBD in microbiomes using a similar approach but focusing on 16S rRNA level diversity (which does not provide strain-level insights) and on microbiomes from diverse environments.

One of the datasets analysed here is a subset of a cross-sectional cohort from the Human Microbiome Project. The other dataset comes from a single individual sampled longitudinally over 18 months. This second dataset allowed the authors to not only assess the links between different levels of diversity at single timepoints, but test if high diversity at a given timepoint is associated with increased strain-level diversity at future timepoints.

Understanding eco-evolutionary dynamics of diversity in natural microbial communities is an important question that remains challenging to address. The paper is well-written and the detailed description of the methodological approaches and statistical analyses is exemplary. Most of the analyses carried out in this study seem to be technically sound.

We thank the reviewer for their kind words, comments, and suggestions.

The major limitation of this study comes with the fact that only correlations are presented, some of which are rather weak, contrast each other, or are based on a small number of data points. In addition, finding that diversity at a given taxonomic rank is associated with diversity within a given taxon is a pattern that can be explained by many different underlying processes, e.g. species-area relationships, nutrient (diet) diversity, stressor diversity, immigration rate, and niche creation by other microbes (i.e. DBD). Without experiments, it remains vague if DBD is the underlying process that acts in these communities based on the observed patterns.

We thank the reviewer for their comments. First, regarding the issue of this being a correlative study, we now more clearly acknowledge that mechanistic studies (perhaps in experimental settings) are required to fully elucidate DBD and BQH dynamics. However, we note that our correlational study from natural communities is complementary to experimental and modeling studies, to test the extent to which their predictions hold in more complex, realistic settings. This is now mentioned throughout the manuscript, most explicitly at the end of the Introduction:

“Although such analyses of natural diversity cannot fully control for unmeasured confounding environmental factors, they are an important complement to controlled experimental and theoretical studies which lack real-world complexity.”

Second, to increase the number of data points analyzed in the Poyet study, we now include 15 species and four different hosts (new Figure 5). The association between community diversity and gene loss is now much more statistically robust, and consistent across the Poyet and HMP time series.

Third, we acknowledge more clearly in the Discussion that other processes, including diet and other environmental factors can generate the DBD pattern. We also now stress more prominently the possibility that strain migration across hosts may be responsible for the patterns observed. For example, in Figure 1, we illustrate the possibility of strain migration generating the patterns we observe.

Below we quote a paragraph that we have now added in the Discussion:

"Second, we cannot establish causal relationships without controlled experiments. We are therefore careful to conclude that positive diversity slopes are consistent with the predictions of DBD, and negative slopes with EC, but unmeasured environmental drivers could be at play. For example, increased dietary diversity could simultaneously select for higher community diversity and also higher intra-species diversity. In our previous study, we found that positive diversity slopes persisted even after controlling for potential abiotic drivers such as pH and temperature (Madi et al., 2020), but a similar analysis was not possible here due to a lack of metadata. Neutral processes can account for several ecological patterns such as species-area relationships (Hubbell, 2001), and must be rejected in favor of niche-centric models like DBD or EC. Using neutral models without DBD or EC, we found generally flat or negative diversity slopes due to sampling processes alone and that positive slopes were hard to explain with a neutral model (Madi et al., 2020). These models were intended mainly for 16S rRNA gene sequence data, but we expect the general conclusions to extend to metagenomic data. Nevertheless, further modeling and experimental work will be required to fully exclude a neutral explanation for the diversity slopes we report in the human gut microbiome.”

Finally, we now put more emphasis on the importance of migration (strain invasion) as a non-exclusive alternative to de novo mutation and gene gain/loss. This is mentioned in the Abstract and is also illustrated in the revised Figure 1.

Another limitation is that the total number of reads (5 mio for the longitudinal dataset and 20 mio for the cross-sectional dataset) is low for assessing strain-level diversity in complex communities such as the human gut microbiota. This is probably the reason why the authors only looked at one species with sufficient coverage in the longitudinal dataset.

Indeed, this is a caveat which means we can only consider sub-species diversity in relatively abundant species. Nevertheless, this allows us to study dozens of species in the HMP and 15 in the more frequent Poyet time series. As more deeply sequenced metagenomes become available, future studies will be able to access the rarer species to test whether the same patterns hold or not. This is now mentioned prominently as a caveat our study in the second Discussion paragraph:

“First, using metagenomic data from human microbiomes allowed us to study genetic diversity, but limited us to considering only relatively abundant species with genomes that were well-covered by short sequence reads. Deeper or more targeted sequencing may permit us to determine whether the same patterns hold for rarer members of the microbiome. However, it is notable that the majority of the dozens of species across the two datasets analyzed support DBD, suggesting that the phenomenon may generalize.”

We also note that rarefaction was only applied to calculate community richness, not to estimate sub-species diversity. We apologize for this confusion, which is now clarified in the Methods as follows:

“SNV and gene content variation within a focal species were ascertained only from the full dataset and not the rarefied dataset.”

Analyzing the effect of diversity at a given timepoint on strain-level diversity at a later timepoint adds an important new dimension to this study which was not assessed in the previous study about the DBD in microbiomes by some of the authors. However, only a single species was analysed in the longitudinal dataset and comparisons of diversity were only done between two consecutive timepoints. This dataset could be further exploited to provide more insights into the prevailing patterns of diversity.

We thank the reviewer for raising this point. We now have considered all 15 species for which there was sufficient coverage from the Poyet dataset, which included four different stool donors. Additionally, in the HMP dataset, we analyze 54 species across 154 hosts, with both datasets showing the same correlation between community diversity and gene loss.

Additionally, we followed the suggestion of the reviewer of examining additional time lags, and in Figure 5 we do observe a dependency on time. This is now described in the Results as follows:

“Using the Poyet dataset, we asked whether community diversity in the gut microbiome at one time point could predict polymorphism change at a future time point by fitting GAMs with the change in polymorphism rate as a function of the interaction between community diversity at the first time point and the number of days between the two time points. Shannon diversity at the earlier time point was correlated with increases in polymorphism (consistent with DBD) up to ~150 days (~4.5 months) into the future (Figure S4), but this relationship became weaker and then inverted (consistent with EC) at longer time lags (Fig 5A, Table S8, GAM, P=0.023, Chi-square test). The diversity slope is approximately flat for time lags between four and six months, which could explain why no significant relationship was found in HMP, where samples were collected every ~6 months. No relationship was observed between community richness and changes in polymorphism (Table S8, GAM, P>0.05).”

Finally, the evidence that gene loss follows increase in diversity is weak, as very few genes were found to be lost between two consecutive timepoints, and the analysis is based on only a single species. Moreover, while positive correlation were found between overall community diversity and gene family diversity in single species, the opposite trend was observed when focusing on pathway diversity. A more detailed analysis (of e.g. the functions of the genes and pathways lost/gained) to explain these seemingly contrasting results and a more critical discussion of the limitations of this study would be desirable.

We agree that our previous analysis of one species in one host provided weak support for gene loss following increases in diversity. As described in the response above, we have now expanded this analysis to 15 focal species and 4 independent hosts with extensive time series. We now analyze this larger dataset and report the more statistically robust results as follows:

“We found that community Shannon diversity predicted future gene loss in a focal species, and this effect became stronger with longer time lags (Fig 5B, Table S9, GLMM, P=0.006, LRT for the effect of the interaction between the initial Shannon diversity and time lag on the number of genes lost). The model predicts that increasing Shannon diversity from its minimum to its maximum would result in the loss of 0.075 genes from a focal species after 250 days. In other words, about one of the 15 focal species considered would be expected to lose a gene in this time frame.

Higher Shannon diversity was also associated with fewer gene gains, and this relationship also became stronger over time (Fig 5C, Table S9, GLMM, P=1.11e-09, LRT). We found a similar relationship between community species richness and gene gains, although the relationship was slightly positive at shorter time lags (Fig 5D, Table S9, GLMM, P=3.41e-04, LRT). No significant relationship was observed between richness and gene loss (Table S9, GLMM, P>0.05). Taken together with the HMP results (Fig 4), these longer time series reveal how the sign of the diversity slope can vary over time and how community diversity is generally predictive of reduced focal species gene content.”

As described in detail in the response to Reviewer 1 above, we found that the HUMAnN2 pathway analyses previously described suffered from technical challenges and we deemed them inconclusive. We have therefore removed the pathway results from the manuscript.

Reviewer #3 (Public Review):

This work provides a series of tests of hypothesis, which are not mutually exclusive, on how genomic diversity is structured within human microbiomes and how community diversity may influence the evolution of a focal species.

Strengths:

The paper leverages on existing metagenomic data to look at many focal species at the same time to test for the importance of broad eco-evolutionary hypothesis, which is a novelty in the field.

Thank you for the succinct summary and recognition of the strengths of our work.

Weaknesses:

It is not very clear if the existing metagenomic data has sufficient power to test these models.

It is not clear, neither in the introduction nor in the analysis what precise mechanisms are expected to lead to DBD.

The conclusion that data support DBD appears to depend on which statistics to measure of community diversity are used. Also, performing a test to reject a null neutral model would have been welcome either in the results or in the discussion.

In our revised manuscript, we emphasize several caveats – including that we only have power to test these hypotheses in focal species with sufficient metagenomic coverage to measure sub-species diversity. We also describe more in the Introduction how the processes of competition and niche construction can lead to DBD. We also acknowledge that unmeasured abiotic drivers of both community diversity and sub-species diversity could also lead to the observed patterns. Throughout the manuscript, we attempt to describe the results and acknowledge multiple possible interpretations, including DBD and EC acting with different strengths on different species and time scales. Our previous manuscript assessing the evidence for DBD using 16S rRNA gene amplicon data from the Earth Microbiome Project (Madi et al., eLife 2020) assessed null models based on neutral ecological theory, and found it difficult to explain the observation of generally positive diversity slopes without invoking a non-neutral mechanism like DBD. While a new null model tailored to metagenomic data might provide additional nuance, we think developing one is beyond the scope of the manuscript – which is in the format of a short ‘Research Advance’ to expand on our previous eLife paper, and we expect that the general results of our previously reported null model provide a reasonable intuition for our new metagenomic analysis. This is now mentioned in the Discussion as follows:

“In our previous study, we found that positive diversity slopes persisted even after controlling for potential abiotic drivers such as pH and temperature (Madi et al., 2020), but a similar analysis was not possible here due to a lack of metadata. Neutral processes can account for several ecological patterns such as species-area relationships (Hubbell, 2001), and must be rejected in favor of niche-centric models like DBD or EC. Using neutral models without DBD or EC, we found generally flat or negative diversity slopes due to sampling processes alone and that positive slopes were hard to explain with a neutral model (Madi et al., 2020). These models were intended mainly for 16S rRNA gene sequence data, but we expect the general conclusions to extend to metagenomic data. Nevertheless, further modeling and experimental work will be required to fully exclude a neutral explanation for the diversity slopes we report in the human gut microbiome.”

Reviewer #3 (Public Review):

To motivate the proposal, Karageorgiou et al. first identify a problem in applying current multivariable MR (MVMR) methods with many correlated exposures. I believe this problem can really be broken into two pieces. The first is that MVMR suffers from weak instrument bias. The second is that some traits may have nearly co-linear genetic associations, making it hard to disentangle which trait is causal. These problems connect in that inclusion of co-linear traits amplifies the problem of weak instrument bias - traits that are nearly co-linear with another trait in the study will have no or very few conditionally strong instruments.<br /> The authors then propose a solution: Apply a dimension reduction technique (PCA or sparse PCA) to the matrix of GWAS effect estimates for the exposures. The identified new components can then be used in MVMR in place of the directly measured exposures.

I think that the identified problem is timely and important. I also like the idea of applying dimension reduction techniques to GWAS effect estimates. However, I don't think that the manuscript in its current form achieves the goals that it has set out. Specifically, I will outline the weaknesses of the work in three categories:<br /> 1. The causal effects measured using this method are poorly defined.<br /> 2. The description of the method lacks important details.<br /> 3. Applied and simulation results are unconvincing.<br /> I will describe each of these in more detail below.

1. To me, the largest weakness of this paper is that it is not clear how to interpret the putatively causal effects being measured. The authors describe the method as measuring "the causal effect of the PC on outcome" but it is not obvious what this means.

One possible implication of this statement is that the PC is a real biological variable (say some hidden regulator) that can be directly intervened on. If this is the intention it should be discussed. However, this situation would imply that there is one correct factorization and there is no guarantee that PCs (or sparse PCs) come close to capturing that.

The counterfactual implied by estimating the effects of PCs in MVMR is that it is possible to intervene on and alter one PC while holding all other PCs constant.<br /> In the introduction, the authors note (and I agree) that one weakness of MR applied to correlated traits is that "MVMR models investigate causal effects for each individual exposure, under the assumption that it is possible to intervene and change each one whilst holding the others fixed." However, it is not obvious that altering one PC while holding the others constant is more reasonable.

2. This section combines a few items that I found unclear in the methods section. The most critical one is the lack of specification on how to select instruments.<br /> For the lipids application, the authors state that instruments were selected from the GLGC results, however, these only include instruments for LDL, HDL, and TG, so 1) it would not be possible to include variants that were independently instruments for one of the component traits alone and 2) there would be no instruments for the amino acids. There is no discussion of how instruments should be selected in general.<br /> This choice could also have a dramatic impact on the PCs estimated. The first PC is optimized to explain the largest amount of variance o of the input data which, in this case, is GWAS effect estimates. This means that the number of instruments for each trait included will drive the resulting PCs. It also means that differences in scaling across traits could influence the resulting PCs.

The other detail that is either missing or which I missed is what is used as the variant-PC association in the MVMR analysis. Specifically, is it the PC loadings or is it a different value? Based on the computation of the F-statistic I suspect the former but it is not clear. If this is the case, what is the effect of using loadings that have been shrunk via one of the sparse methods? It would be nice to see a demonstration of the bias and variance of the resulting method, though it is not clear to me what the "truth" would be.

3. In the lipids application, the fact that M.LDL.PL changes sign in MVMR analysis are offered as evidence of multicollinearity. I would generally associate multicollinearity with large variance and not bias. Perhaps the authors could offer some more insight on how multicollinearity would cause the observation.<br /> A minor point of confusion: I was unable to interpret this pair of sentences "Although the method did not identify any of the exposures as significant at Bonferroni-adjusted significance level, the estimate for M.LDL.PL is still negative but closer to zero and not statistically significant. The only trait that retains statistical significance is ApoB." The first sentence says that none of the exposures were significant while the second sentence says that Apo B is significant. The GRAPPLE results don't seem clearly bad, indeed if only Apo B is significant, wouldn't we conclude that of the 118 exposures, only Apo B is causal for heart disease? It would help to discuss more how the conclusions from the PC-based MVMR analysis compare to the conclusions from GRAPPLE.

It is a bit hard to interpret Table 4. I wasn't able to fully determine what "VLD, LDL significance in MR" means here. From the text, it seems that it means that any PC with a non-zero lodaing on VLDL or LDL traits was significant, however, this seems like a trivial criterion for the PCA method, since all PCs will be dense. This would mean this indicator only tells us whether and PCs were found to "cause" heart disease.

In simulations, I may be missing something about the definition of a true and false positive here. I think this is similar to my confusion in the previous paragraph. Wouldn't the true and false positive rates as computed using these metrics depend strongly on the sparsity of the components? It is not clear to me what ideal behavior would be here. However, it seems from the description that if the truth was as in Fig 7 and two methods each yielded one dense component that was found to be causal for Y, these two methods would get the same "score" for true positive and false positive rate regardless of the distribution of factor loadings. One method could produce a factor that loaded equally on all exposures while the other produced a factor that loaded mostly on X1 and X2 but this difference would not be captured in the results.

key passage from As We May Think

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Reply to the reviewers

Response to Reviewers:

1. General Statements

We thank the reviewers for the comments and the suggestions. We hope that we have addressed all the queries raised by the reviewers in the revised manuscript. We provide a point-by-point response below. Please note that the line numbers indicated in parentheses correspond to the pdf file without the track changes display.

2. Point-by-point description of the revisions

---

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

Summary: Srinivasan and co-workers developed an alternative screening method for defining the ability of FtsZ inhibitor to affect FtsZ polymerization. This alternative assay was defined considering the expertise of the authors on the topic, and they use Schizosaccharomyces pombe as a model for studying the effect of PC190723, sanguinarine and berberine on FtsZ assembly. The use of a heterologous expression system is useful for the evaluation of FtsZ coming from different strains, both Gram - and Gram +. The same model could gain insights also on the capability of FtsZ inhibitors to affect eukaryotic cell physiology. Finally, authors resulted also in suggesting a possible cause to suspected resistance to PC190723 from Gram - strains as E. coli.

Major comments: • The conclusions are included in the discussion section and are quite convincing, for a general audience.

We thank the reviewer for the positive comments.

In my opinion, the authors should define which could be the limits of their method, since no data on the possible weaknesses are reported.

RESPONSE: We have discussed the limitations of the methods as well. The discussion has been modified and the following sentences have been now included in the revised manuscript.

“However, one of the major disadvantages of using fission yeast could be the need to use much higher concentrations of drugs than normally used for mammalian cell cultures to achieve an inhibitory effect. This could probably be due to the poor permeability of certain drugs in fission yeast because of its thick cell wall (Benko et al. 2017; Pérez and Ribas 2004). A similar effect of toxicity might arise at much lower concentrations in other eukaryotic cells, such as human cells. Consistently, while sanguinarine and berberine are known to affect the eukaryotic microtubules at 10 μΜ – 20 μM concentrations (Lopus and Panda 2006; Wang et al. 2016; Raghav et al. 2017), morphological effects on yeast cells were observed only at concentrations > 100 μM. However, yeast microtubules were not affected by berberine and sanguinarine. Differences in membrane lipid profiles and MDR efflux pumps between yeasts and mammalian cells might also contribute to differential resistance to the drugs being tested (Balzi and Goffeau 1991). Conversely, an inhibitory effect in yeast cells may not necessarily translate into toxicity in a human cell. These and the permeability of drugs in yeast cells represent an important caveat in using such heterologous expression systems for the screening of compounds against target molecules.”

[Lines 498-513]

As suggested in the later sections, we have also elaborated on the pros and cons of various methods including the yeast-based screening methods. [Lines 462-523]

• No additional experiments are required to support the claims.

• The suggested experiments could be quite easy to be realized for authors working in the microbiological field, and familiar with protein expression and purification, as well as bacteria and yeast growth.

• From my side, even if I am not so expert in microbiology and plasmid/protein purification, the methods presented could be reproduced with no significant doubt.

• Statistical analysis was done and seems to be adequate.

RESPONSE: We thank the reviewer for these encouraging comments.

Minor comments: • Prior studies should be deepened, especially for the state of art authors referred to. Additional paper, both reviews on the possible methods for evaluating FtsZ inhibition, as well as research papers on FtsZ inhibitors targeting E. coli and other Gram negative strains should be mentioned, since, in my opinion, these could move authors in changing a little bit the overall text of the manuscript.

RESPONSE: We have now elaborated the state-of-art methods used for evaluation of FtsZ inhibition and cited the relevant papers and reviews. We have also included papers on development of FtsZ inhibitors, especially the ones similar to PC190723, targeting Gram-negative bacteria. The following sentences have been included in the revised manuscript.

“Several approaches have been used to screen small molecules targeting bacterial cell division and FtsZ. While in vitro methods such as NMR (Domadia et al. 2007; Sun et al. 2014; Araújo‑Bazán et al. 2019) and crystallography (Läppchen et al. 2008; Fujita et al. 2017) are valuable and offer information on distinct binding sites, these are not efficient for screening. Electron microscopic examination can distinguish the effects of the compounds being tested on the FtsZ protofilament assembly and lateral associations (Nova et al. 2007; Kaul et al. 2012; Anderson et al. 2012; Sun et al. 2014; Huecas et al. 2017; Kumar et al. 2011; Park et al. 2014). Other techniques that are routinely used include fluorescence anisotropy (Ruiz‑Avila et al. 2013; Park et al. 2014), 90º light-scattering assay (Mukherjee and Lutkenhaus 1999) and dynamic light scattering (Hou et al. 2012; Di Somma et al. 2020) for assessing inhibition of FtsZ assembly (Kaul et al. 2012; Nova et al. 2007; Lui et al. 2019; Anderson et al. 2012, (Irwin et al. 2015). Other easily scalable high-throughput assays include FCS/FCCS and FRET-based methods (Hernández‑Rocamora et al. 2015; Mikuni et al. 2015; Reija et al. 2011).

In vivo assays relying on cell filamentation phenotype coupled with the localization of Z-ring might be a good indicator of FtsZ being the direct target. However, since bacteria can undergo cell filamentation and not assemble FtsZ rings in response to a variety of conditions, including DNA damage (Mukherjee et al. 1998) and disruption of membrane potential (Strahl and Hamoen 2010), the in vivo assay is not so useful unless combined with the in vitro assays mentioned above. Finally, the isolation of resistance mutants in FtsZ to the drug can provide strong evidence of FtsZ being the direct target.

Reconstitution systems are powerful and provide excellent control over the system, but they are emerging technologies and are technically challenging. Reconstitution systems include a variety of methods, such as the use of membrane nanodiscs, microbeads of different materials, supported bi-layer membranes (SLBs) and biomimetic systems that provide cell-like environments (Monterroso et al. 2013; Rivas et al. 2014).”

[Lines 462-487]

“Several compounds have been evaluated for their activity against FtsZ from both Gram-positive bacteria and Gram-negative bacteria. Although many exhibited only weak activity in vivo against Gram-negative bacteria, derivatives could be promising. These include benzamides (Haydon et al. 2008; Adams et al. 2011; Straniero et al. 2017, 2020a), trisubstituted benzimidazoles (Kumar et al. 2011), 4-bromo-1H-indazole derivatives (Wang et al. 2015), cinnamaldehyde and its derivatives (Domadia et al. 2007; Li et al. 2015), curcumin (Rai et al. 2008), heterocyclic molecules like guanidinomethyl biaryl compounds (Kaul et al. 2012), pyrimidine-quinuclidine scaffolds (Chan et al. 2013), 3-phenyl substituted 6,7-dimethoxyisoquinoline (Kelley et al. 2012), thiazole orange derivatives (Sun et al. 2017), viriditoxin (Wang et al. 2003), N-heterocycles such as zantrins and derivatives (Margalit et al. 2004; Nepomuceno et al. 2015).”

[Lines 69-80]

“Several efforts have been made to target Gram-negative bacteria with derivatives of benzamide. Examples include difluorobenzamides, substituted benzodioxanes, heterocyclic and non-heterocyclic derivatives (Straniero et al. 2017; Chai et al. 2020; Straniero et al. 2020a, 2020b). Although many exhibited promising activity in vitro, most were substrates for the AcrAB class of efflux pumps (Chai et al. 2020; Kaul et al. 2014; Straniero et al. 2020a, 2020b; Casiraghi et al. 2020). Thus, the poor membrane permeability, signature outer membrane, particularly lipopolysaccharide (LPS) structure (Wang et al. 2021), the presence of multiple efflux pumps in species such as E. coli, Klebsiella pneumonia and Pseudomonas aeruginosa (Piddock 2006), and differences in FtsZ sequences in the binding-site (Kaul et al. 2013b; Miguel et al. 2015) have been cited as reasons for lack of susceptibility of Gram-negative bacteria to benzamide derivatives (Casiraghi et al. 2020). More recently, two molecules, TXA6101 and TXY6129, with substituted 2,6-difluorobenzamide scaffold, have been shown to inhibit the polymerization of both E. coli and Klebsiella pneumoniae FtsZ. Moreover, despite being substrates for efflux pumps, TXA6101 induced morphological changes in K. pneumoniae (Rosado‑Lugo et al. 2022). Studies in the past on the effects of PC190723 on E. coli have been confusing, with a few reports suggesting an effect on FtsZ polymerization resulting in cell filamentation (Kaul et al. 2014), while others did not find any effect on EcFtsZ (Andreu et al. 2010; Anderson et al. 2012; Khare et al. 2019)⁠. The outer membrane has been shown to be a permeability barrier for PC190723 in E. coli (Khare et al. 2019; Chai et al. 2020). In addition, the Resistance-Nodulation-Division (RND) family of efflux pumps has been attributed to resistance against 2,6-difluorobenzamide derivatives, including TX436 (a prodrug of PC190723) in Gram-negative bacteria (Kaul et al. 2014).”

[Lines 527-550]

The whole text requires a deep check for grammar and word choice. Some sentences should be re-written since it is not so easy to understand their meaning. Figures are clear, even if I am not so convinced on the need of including Figure 1.

RESPONSE: We have now deleted Figure 1 and 2 (as also suggested by Reviewer #2), revised the manuscript and have re-written certain long sentences. We have used Grammarly to check for grammatical errors. We hope the manuscript is easier to follow with these changes.

Reviewer #1 (Significance (Required)):

• In my opinion, the outcome coming from this work could move researchers in evaluating an alternative method for assessing FtsZ inhibition. Nevertheless, the actual state of art, a few reviews of the last years confirm this, already underlined a huge number of possible assays, both microbiological, biochemical, biophysical, physiological, or other. As a result, the authors did not result in convincing me about the importance of their methods, when compared to others. They may include some other possible assays and comment of the differences, pros and cons.

RESPONSE: Several alternative methods have been evaluated and several excellent reviews published in the recent past have underlined the importance of these multiple methods to screen and validate small molecules targeting FtsZ. As suggested by the reviewer here and above, we have now discussed these methods including the yeast-based assay we describe, their advantages and limitations in the revised manuscript.

The following lines have now been included in Introduction.

“Several methods have been used to ascertain FtsZ as the target of the drug, and the various approaches have been reviewed in detail by many (Kusuma et al. 2019; Silber et al. 2020; Zorrilla et al. 2021; Andreu et al. 2022). Andreu et al. (2022) have recently proposed a streamlined experimental protocol for the screening and characterization of FtsZ inhibitors.”

Introduction – [Lines 113-117]

The following paragraphs, including ones as mentioned above have included in the discussion sections of the revised manuscript.

“Several approaches have been used to screen small molecules targeting bacterial cell division and FtsZ. While in vitro methods such as NMR (Domadia et al. 2007; Sun et al. 2014; Araújo‑Bazán et al. 2019) and crystallography (Läppchen et al. 2008; Fujita et al. 2017) are valuable and offer information on distinct binding sites, these are not efficient for screening. Electron microscopic examination can distinguish the effects of the compounds being tested on the FtsZ protofilament assembly and lateral associations (Nova et al. 2007; Kaul et al. 2012; Anderson et al. 2012; Sun et al. 2014; Huecas et al. 2017; Kumar et al. 2011; Park et al. 2014). Other techniques that are routinely used include fluorescence anisotropy (Ruiz‑Avila et al. 2013; Park et al. 2014), 90º light-scattering assay (Mukherjee and Lutkenhaus 1999) and dynamic light scattering (Hou et al. 2012; Di Somma et al. 2020) for assessing inhibition of FtsZ assembly (Kaul et al. 2012; Nova et al. 2007; Lui et al. 2019; Anderson et al. 2012, (Irwin et al. 2015). Other easily scalable high-throughput assays include FCS/FCCS and FRET-based methods (Hernández‑Rocamora et al. 2015; Mikuni et al. 2015; Reija et al. 2011).

In vivo assays relying on cell filamentation phenotype coupled with the localization of Z-ring might be a good indicator of FtsZ being the direct target. However, since bacteria can undergo cell filamentation and not assemble FtsZ rings in response to a variety of conditions, including DNA damage (Mukherjee et al. 1998) and disruption of membrane potential (Strahl and Hamoen 2010), the in vivo assay is not so useful unless combined with the in vitro assays mentioned above. Finally, the isolation of resistance mutants in FtsZ to the drug can provide strong evidence of FtsZ being the direct target.

Reconstitution systems are powerful and provide excellent control over the system, but they are emerging technologies and are technically challenging. Reconstitution systems include a variety of methods, such as the use of membrane nanodiscs, microbeads of different materials, supported bi-layer membranes (SLBs) and biomimetic systems that provide cell-like environments (Monterroso et al. 2013; Rivas et al. 2014). While in vitro biochemical assays and reconstitution systems are useful to find molecules that directly target FtsZ, they are cumbersome and need to be performed at optimal physiological pH and ionic conditions, which can be considerably variable among FtsZ from different species.

Our results on the ability of sanguinarine and berberine to specifically affect the assembly of FtsZ and not MreB in fission yeast highlight the utility of the heterologous expression system as a platform to identify molecules that specifically affect FtsZ polymerization. The yeast platform offers a cellular context mimicking the cytoplasm for cytoskeletal assembly. The system is simple to replicate in any laboratory, including those focused on chemical synthesis with minimum microbiological expertise and can be easily reproduced and scaled up as well. However, one of the major disadvantages of using fission yeast could be the need to use much higher concentrations of drugs than normally used for mammalian cell cultures to achieve an inhibitory effect. This could probably be due to the poor permeability of certain drugs in fission yeast because of its thick cell wall (Benko et al. 2017; Pérez and Ribas 2004). A similar effect of toxicity might arise at much lower concentrations in other eukaryotic cells, such as human cells. Consistently, while sanguinarine and berberine are known to affect the eukaryotic microtubules at 10 μΜ – 20 μM concentrations (Lopus and Panda 2006; Wang et al. 2016; Raghav et al. 2017), morphological effects on yeast cells were observed only at concentrations > 100 μM. However, yeast microtubules were not affected by berberine and sanguinarine. Differences in membrane lipid profiles and MDR efflux pumps between yeasts and mammalian cells might also contribute to differential resistance to the drugs being tested (Balzi and Goffeau 1991). Conversely, an inhibitory effect in yeast cells may not necessarily translate into toxicity in a human cell. These and the permeability of drugs in yeast cells represent an important caveat in using such heterologous expression systems for the screening of compounds against target molecules. However, notwithstanding this caveat, the heterologous system provides significant advantages in assessing the direct effects of the drug on FtsZ assembly. Moreover, fission yeast-based high-throughput platform screening methods using imaging have been successfully adapted to the screening of drugs against HIV-1 proteases by large-scale screening facilities such as the NIH Molecular Libraries Probe Production Centers Network in the Molecular Libraries Program, leading to several candidate drugs (Benko et al. 2017, 2019).”

Discussion - [Lines 462-519]

“A powerful emerging technique based on cytological profiling has been successfully used to identify the cellular pathways targeted by the inhibitors (Nonejuie et al. 2013; Martin et al. 2020), including cell division inhibition by FtsZ (Araújo‑Bazán et al. 2016). The recent advances in computational image analysis and deep learning approaches (von Chamier et al. 2021; Spahn et al. 2022) could further advance image-based screening for FtsZ inhibitors (Andreu et al. 2022).”

Discussion – [Lines 581-586]

As I mentioned before, there are a lot of reviews including the possible tests to perform for assessing FtsZ inhibition. A recent one was not cited, but, from my side, it should be mentioned (10.3390/antibiotics10030254).

The suggested article is an excellent review that in addition to providing an overview of the state-of-art methods currently in practice for screening drugs targeting FtsZ, also suggests other emerging technologies suitable for assay development. We had cited this article (Zorrilla et al., 2021; doi: 10.3390/antibiotics10030254) in other contexts in our original manuscript but inadvertently missed in the text while mentioning the methods for screening.

We have now cited Zorrilla et al., 2021 at all appropriate places in the revised manuscript. In addition, we have also cited (Monterroso 2013; https://doi.org/10.1016/j.ymeth.2012.12.014); (Rivas 2014; https://doi.org/10.1016/j.cbpa.2014.07.018); Kusuma 2019 (doi: 10.1021/acsinfecdis.9b00055); Schaffner-Barbero 2012 (doi: 10.1021/cb2003626); Silber et al 2020 (doi: 10.2217/fmb-2019-0348); Li et al., 2015 (doi: 10.1016/j.ejmech.2015.03.026); Casiraghi et al 2020 (doi: 10.3390/antibiotics9020069); Andreu et al., 2022 (10.3390/biomedicines10081825)

Moreover, I think authors should reconsidered novel research papers, in which researchers evaluated the reason behind the apparent inactivity of benzamide derivatives, similar to PC190723, towards Gram negative strains.

RESPONSE: Several novel papers that have reported reason for the inactivity of benzamide derivatives towards Gram-negative bacteria, including PC190723 have now been cited. The following sentences have been now included in the revised manuscript.

“Several efforts have been made to target Gram-negative bacteria with derivatives of benzamide. Examples include difluorobenzamides, substituted benzodioxanes, heterocyclic and non-heterocyclic derivatives (Straniero et al. 2017; Chai et al. 2020; Straniero et al. 2020a, 2020b). Although many exhibited promising activity in vitro, most were substrates for the AcrAB class of efflux pumps (Chai et al. 2020; Kaul et al. 2014; Straniero et al. 2020a, 2020b; Casiraghi et al. 2020). Thus, the poor membrane permeability, signature outer membrane, particularly lipopolysaccharide (LPS) structure (Wang et al. 2021), the presence of multiple efflux pumps in species such as E. coli, Klebsiella pneumonia and Pseudomonas aeruginosa (Piddock 2006), and differences in FtsZ sequences in the binding-site (Kaul et al. 2013b; Miguel et al. 2015) have been cited as reasons for lack of susceptibility of Gram-negative bacteria to benzamide derivatives (Casiraghi et al. 2020). More recently, two molecules, TXA6101 and TXY6129, with substituted 2,6-difluorobenzamide scaffold, have been shown to inhibit the polymerization of both E. coli and Klebsiella pneumoniae FtsZ. Moreover, despite being substrates for efflux pumps, TXA6101 induced morphological changes in K. pneumoniae (Rosado‑Lugo et al. 2022). Studies in the past on the effects of PC190723 on E. coli have been confusing, with a few reports suggesting an effect on FtsZ polymerization resulting in cell filamentation (Kaul et al. 2014), while others did not find any effect on EcFtsZ (Andreu et al. 2010; Anderson et al. 2012; Khare et al. 2019)⁠. The outer membrane has been shown to be a permeability barrier for PC190723 in E. coli (Khare et al. 2019; Chai et al. 2020). In addition, the Resistance-Nodulation-Division (RND) family of efflux pumps has been attributed to resistance against 2,6-difluorobenzamide derivatives, including TX436 (a prodrug of PC190723) in Gram-negative bacteria (Kaul et al. 2014).”

[Lines 527-550]

Researchers working on FtsZ inhibitors could be interested in this paper, especially microbiologists.

I specifically work on the design, synthesis and evaluation of the microbiological assays performed by others on my compounds.

========================================================================

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

Dr. Srinivasin and colleagues previously developed a system where they expressed bacterial FtsZ in yeast and showed that it could assemble into polymers related to the Z rings. Here they develop this system further as a way to assay for drugs that may poison FtsZ, which would be candidates for new antibiotics. They test three drugs against three species of FtsZ. The results suggest that this system should be useful in screening new drugs that may target FtsZ. I would recommend publication after addressing a number of concerns and apparent contradictions.

Fig. 1 showing chemical formulas of the drugs, and Fig. 2 showing a schematic of the yeast expression system, are probably not needed.

RESPONSE: Reviewer #1 had also made a similar suggestion and we have now deleted these two figures (Fig. 1 and Fig. 2 in the older version).

The authors make a point that sanguinarine and berberine inhibit eukaryote cell morphology. In fact, what they show is that they affect yeast cell morphology. This may or may not extend to other eukaryotes. Also, other eukaryotic cells may be more sensitive to drugs than yeast. They should me more conservative in this claim that the system also screens for drugs effects on eukaryotes.

RESPONSE: We agree with the reviewer’s suggestions here that other eukaryotic cells may be more sensitive to drugs than yeast. We have modified the statements pertaining to these claims in the revised manuscript.

We have made the following changes in the revised version.

The title of the manuscript has been now modified as “A salt bridge-mediated resistance mechanism to FtsZ inhibitor PC190723 revealed by a cell-based screen”.

Lines 23-24 in the abstract has been modified to read as “The strategy also allows for simultaneous assessment of the toxicity of the drugs to eukaryotic yeast cells.”

Other sentences modified in the revised version are:

“We find that although sanguinarine and berberine affected FtsZ polymerization, they also affected yeast cell physiology”. [Lines 146-147]

“In this study, we have attempted to develop a cell-based assay using fission yeast (S. pombe) as a heterologous expression host, which would enable the screening of compounds that could directly affect FtsZ polymerization as well as identify potential toxicity to yeast (or eukaryotic) cells simultaneously”. [Lines 444-447]

“However, one of the major disadvantages of using fission yeast could be the need to use much higher concentrations of drugs than normally used for mammalian cell cultures to achieve an inhibitory effect. This could probably be due to the poor permeability of certain drugs in fission yeast because of its thick cell wall (Benko et al. 2017; Pérez and Ribas 2004). A similar effect of toxicity might arise at much lower concentrations in other eukaryotic cells, such as human cells”. [Lines 498-503]

“Conversely, an inhibitory effect in yeast cells may not necessarily translate into toxicity in a human cell. These and the permeability of drugs in yeast cells represent an important caveat in using such heterologous expression systems for the screening of compounds against target molecules”. [Lines 510-513]

Fig. 3 has some new structural data that should be explored more quantitatively. My quick measurement gave 0.5 and 0.8 µm for the outside diameters of Ec and Sa rings. The spirals of Hp seem to be 0.8 µm outside diameter, similar to SA rings. These spirals may be related to those reported by Popp and by Andreu under certain buffer conditions. This should be explored and referenced.

RESPONSE: We have now quantitatively measured the diameters of the rings formed by EcFtsZ and SaFtsZ and the diameter and pitch of the spiral polymers of HpFtsZ. These have been now included in the results section and presented as a graph in a new figure (Supplementary Fig. S2). Please also note that the scale bar in Figure 1 (previously Figure 3) was erroneously marked as 5 µm. This has been corrected in the revised version to 2.5 µm.

Also, the possibility that these spiral polymers may be related to those described by Popp and Andreu have been discussed. We included the following sentences in the discussion.

“Previous studies have shown that various factors such as molecular crowding, variable C-terminal regions and bound nucleotide state lead to the formation of supramolecular structures like twisted helical structures, toroids and rings similar to those that have been observed in vivo (Popp et al. 2009; Huecas et al. 2017). Thus, the molecular crowding due to the dense cytoplasm of the yeast cells could have possibly induced the spiral and ring-like assembly of FtsZ polymers (Erickson et al. 2010).”

[Lines 456-461]

But Fig. 4 presents a contradiction. Here the Hp control cells show long smooth polymers, not helical. This seems an important difference and needs to be addressed. Are the polymers sometimes straight and sometimes helical? After finishing the paper I see that in some experiments the HP is helical, and in others the polymers are straight and smooth. I think it would be important to determine what favors the two forms. If this remains a mystery, at least address it openly.

RESPONSE: This was definitely an oversight from the authors. We should have clearly mentioned this in the manuscript but completely missed the description of different polymers assembled by HpFtsZ.

We have now described this clearly in the results and added a new Figure (Supplementary Fig. S1) showing a time course for the appearance of spiral and linear polymers. We have also replaced the images in Figure 5E.

We have modified the results to read as:

“Interestingly, HpFtsZ assembled into linear cable-like structures as well as twisted polymers that were curled and spiral in appearance (Fig. 1D). The spiral filaments were more clearly visualized by deconvolution of the images (Fig. 1D iii and 1E). Further, super-resolution imaging using 3D-SIM clearly revealed that HpFtsZ assembles into spiral filaments in fission yeast (Fig. 1F).”

[Lines 171-175]

We have also added the following lines in the results section:

“Spiral polymers appeared early, at 16 – 18 hours after induction of expression (absence of thiamine), and linear cables appeared later at 20 – 22 hours (Fig. S1). The smooth linear polymers possibly arise from lateral association and bundling of FtsZ filaments (Monahan et al. 2009), but the factors determining the two forms in yeast cells remain unclear.”

[Lines 175-179]

I am concerned that the quantitation of drug inhibition in Fig 4, 5 is flawed. Visually from 4A it looks like ~90-100% of control cells have polymers, and sang reduces polymers by 70% for Sa and Ec and 100% for Hp: this is based on the number of spots and filaments I see in Fig. 4 Aii. But the quantitation in D shows only 17-23% reduction for all three. These numbers were based on determining the fraction of cells that showed polymer (spots or lines) vs diffuse. It seems that cells are counted as containing polymer even if they had a great reduction in spots or lines, but still had a few. E.g., 4Aii Sa has 4 cells, two of them with no spots, one with only 2, and one with ~7, which totals ~1/3 the spots in control cells. Categorizing cells with only a couple of spots as polymerized, seems to be a poor way to quantitate. Would it not be better to count all spots in all cells, or measure the total length of line polymers, as a measure of inhibition.

RESPONSE: We agree with the reviewer here that number of spots or the length of the polymers would be a better quantitative measure of the effect of the drugs than the percentage of cells presented. In the revised manuscript, we now present quantified data as suggested.

We have quantitated the number of spots per cell for SaFtsZ and total polymer length per cell for HpFtsZ to elucidate the effect of drugs on FtsZ polymers. The number of spots per cell were counted using built-in ImageJ macro OPS threshold IJ1 script which combines the otsu thresholding method and analyse particles plugin. The total polymer length per cell in the case HpFtsZ, was measured using used the lpx-plugins as described by Higaki (Higaki et al., 2017).

In addition, using the lpx-plugins, we also quantify density, a measure of the amount cytoskeleton per unit area in a given cell (Henty-Ridilla et al., 2014; Higaki et al., 2017). We had previously used this measure successfully to quantify assembly of Spiroplasma citri MreB in fission yeast (Pande et al., 2022).

The methodology has been described in detail in the Materials and Methods section under the heading – “Quantitation of the number of spots, polymer length and density”

Lines [665-689]

The new data has been included in the results (lines 207-231 and 275-284) and new Figures (Fig. 2 E, G and Fig. 3 G, H) have been added.

Fig. 5 makes a convincing case that PC19 accelerates or enhances the polymerization of Sa and Hp. Fig. S2 shows that the structures of polymers are not changed when PC19 is added at 20 hrs, after polymers have already formed. It would have been nice to see for both 5A and S2A that the round spots had holes in the center, when imaged by SIM. Again the quantitation of cells as polymer vs diffuse seems ill suited, because it misses cells with a reduced number of spots.

RESPONSE: We have imaged the FtsZ polymers of Sa and Hp in the presence of PC190723 using SIM and included these images as new panels in the figures. Figure 3C, 3F and Figure S4 in the revised manuscript.

Again, for Figure 5 (Fig. 3 in the revised version), we have provided the quantitation as number of spots per cell, polymer length per cell and density (amount of cytoskeleton per unit area) as described above (new Figures - Fig. 3 G, H) in the revised manuscript.

[Lines 275-284]

Fig. 6 uses FRAP to show that PC reduces the dynamic exchange of Sa polymers by a factor of 3. It is remarkable to me that rapid exchange is not completely eliminated by PC. Regardless, it would be very important to reference the previous study of Adams..Errington 2011, where they showed the same thing for Foci in Bacillus. PC19 reduced the exchange from 3 to 10 s, but the foci were still very dynamic.

RESPONSE: We had referenced this work in the original submission in the discussion section – “These results are also consistent with the earlier findings that PC190723 acts to induce FtsZ polymerization and stabilize FtsZ filaments (Andreu et al. 2010; Elsen et al. 2012; Miguel et al. 2015; Fujita et al. 2017) and its derivative compound, 8j acting to slow down FtsZ-ring turnover by 3-fold in B. subtilis (Adams et al. 2011).”

[Lines 563-567] in revised manuscript

We have now added the following statement and referenced Adams et al., 2011 in the results section as well.

“Interestingly, compound 8j, a related benzamide derivative, has been shown to slow down FtsZ-ring turnover by 3-fold in B. subtilis (Adams et al. 2011).”

[Lines 324-326]

The analysis of the salt bridge as opposed to a single Arg or His being the cause of resistance to PC19 is an interesting addition to the study. In Fig. 8D some numbers do not agree between the caption and figure (R309/7; S226/7). The whole figure should be carefully checked.

RESPONSE: We thank the reviewer for pointing to these. We have corrected these errors now in the revised version (Fig. 6).

I am not familiar with the Gram -ve and Gram +ve nomenclature. Why not simply gram- and gram+?

RESPONSE: We agree that Gram -ve / +ve are not standard notations and inappropriate.

We have now written them as Gram-negative and Gram-positive throughout the text.

The Discussion is quite long largely because it repeats items from Results and Introduction. It is also redundant to hype the value of this system in both Introduction and Discussion; The Introduction should be sufficient. The Discussion should be pared down by eliminating repetition and focusing on relating results to previous literature, in particular items that have not been referenced previously in the paper. Also, I think we don't need the final "In summary" paragraph. That is already nicely presented in the Abstract.

RESPONSE: We have omitted the repetitive statements from the discussion. We have also deleted the final summary paragraph. We had added new paragraphs [lines 462-519] pertaining to previous literature (also suggested by Reviewer #1) to the discussion section in the revised manuscript.

The authors should probably provide references to other studies that have used yeast expression to study assembly of FtsZ. I am thinking in particular of papers from the Osteryoung lab looking at chloroplast FtsZ.

RESPONSE: We have now referenced other papers that have used yeast expression to study assembly of FtsZ.

The following statement has been added to the introduction:

“Moreover, the dynamics of chloroplast FtsZs have also been successfully studied using the heterologous fission yeast expression system (TerBush and Osteryoung 2012; Yoshida et al. 2016; TerBush et al. 2018).”

Lines [132-134]

NO PAGE NUMBERS. Authors should be penalized a week delay for submitting a mss without page numbers.

RESPONSE: We sincerely apologise for this gross error and oversight and thank the reviewer for patiently reading through and reviewing a manuscript with no page numbers and line numbers. We are truly sorry for having submitted a manuscript as such and have now included page numbers and line numbers in the manuscript.

Reviewer #2 (Significance (Required)):

This work should be of interest to the broad field of research on FtsZ. The authors present it as a new platform for assaying drugs targeting FtsZ, and researchers in this area will certainly be interested. It will also be of broader interest for the novel assay of assembly and exchange dynamics and how they may be modulated by small molecules.

========================================================================

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

Summary: The authors established a proof-of-concept assay to investigate the bacterial cytoskeletal protein FtsZ in fission yeast, and this heterologous yeast system is useful for compounds identification targeting FtsZ. The authors used this system to understand the mechanism of FtsZ's resistance to drug PC190723. Major comments: 1. From the study, the pombe seems to be a good system for investigating the bacterial cytoskeleton proteins and testing the drugs for them. However, to my knowledge it is not convincing that this is the proper system can be used to assessing the eukaryotic toxicity, since no toxicity to pombe does not mean no toxicity to human cells and vice versa.

RESPONSE: We agree with the reviewer that toxicity to S. pombe cannot be directly extended to assessing toxicity to other eukaryotic cells such as human cells. As suggested by Reviewer#2 as well, we have modified these claims in the revised manuscript, discussed the possibilities and limited the scope of this work to assessing toxicity in yeast cells.

We have made the following changes in the revised version.

The title of the manuscript has been now modified as “A salt bridge-mediated resistance mechanism to FtsZ inhibitor PC190723 revealed by a cell-based screen”.

Lines 23-24 in the abstract has been modified to read as “The strategy also allows for simultaneous assessment of the toxicity of the drugs to eukaryotic yeast cells.”

Other sentences modified in the revised version are:

“We find that although sanguinarine and berberine affected FtsZ polymerization, they also affected yeast cell physiology”. [Lines 146-147]

“In this study, we have attempted to develop a cell-based assay using fission yeast (S. pombe) as a heterologous expression host, which would enable the screening of compounds that could directly affect FtsZ polymerization as well as identify potential toxicity to yeast (or eukaryotic) cells simultaneously”. [Lines 444-447]

“However, one of the major disadvantages of using fission yeast could be the need to use much higher concentrations of drugs than normally used for mammalian cell cultures to achieve an inhibitory effect. This could probably be due to the poor permeability of certain drugs in fission yeast because of its thick cell wall (Benko et al. 2017; Pérez and Ribas 2004). A similar effect of toxicity might arise at much lower concentrations in other eukaryotic cells, such as human cells”. [Lines 498-503]

“Conversely, an inhibitory effect in yeast cells may not necessarily translate into toxicity in a human cell. These and the permeability of drugs in yeast cells represent an important caveat in using such heterologous expression systems for the screening of compounds against target molecules”. [Lines 510-513]

From figure 4A to 4C, there seems no big difference of cell morphology between control and drug treatment, except for Berberine treatment of SaFtsZ-GFP. Under the low concentration of Sanguinarine (20 µM) and Berberine (53.791 µm), the FtsZ polymerization was disrupted and seems no effect on cell morphology. Why would the authors use much higher Sanguinarine (135.95 µM) and Berberine (134.45 µM) to prove there two drugs are toxic to pombe cells?

RESPONSE: Earlier reports had shown that sanguinarine and berberine affect mammalian microtubules (Lopus and Panda 2006 - DOI: 10.1111/j.1742-4658.2006.05227.x; Raghav et al., 2017 - DOI: 10.1021/acs.biochem.7b00101). While, we did not observe any growth defect in yeast cells, earlier studies have suggested that yeasts possibly require higher concentrations of certain drugs than used for mammalian cells due to the presence of the cell wall, particularly S. pombe (Perez and Ribas 2004 - https://doi.org/10.1016/j.ymeth.2003.11.020; Benko et al., 2017 - DOI: 10.1186/s13578-016-0131-5). We had thus explored the possibility of cell toxicity to yeast cells at higher concentrations of the drugs.

The following lines have thus been added to the results section in the revised manuscript.

“Although we did not observe any growth defect in yeast cells at lower concentrations of the drugs, earlier studies have suggested that yeast cells possibly require higher concentrations of drugs than used for mammalian cells due to the presence of the cell wall, which is particularly thick in S. pombe (Benko et al. 2017; Pérez and Ribas 2004). We thus explored the possibility of cell toxicity to yeast cells at higher concentrations of the drugs.”

Lines [234-239]

Sanguinarine and Berberine are FtsZ disruption drugs, do these drugs have effect on microtubule?

RESPONSE: We have now examined the effect of Sanguinarine and Berberine on yeast microtubules as well and did not find any visible differences between the control and inhibitor (either low or high concentrations) treated cells. This data has been added as a new figure (Supplementary Fig. S3 A and B) in the revised manuscript and the following line added to the results.

“However, even at higher concentrations, neither of the drugs showed any visible effect on yeast microtubules (Fig. S3 A and B).”

[Lines 241-242]

The discussion has been modified as follows:

“However, one of the major disadvantages of using fission yeast could be the need to use much higher concentrations of drugs than normally used for mammalian cell cultures to achieve an inhibitory effect. This could probably be due to the poor permeability of certain drugs in fission yeast because of its thick cell wall (Benko et al. 2017; Pérez and Ribas 2004). A similar effect of toxicity might arise at much lower concentrations in other eukaryotic cells, such as human cells. Consistently, while sanguinarine and berberine are known to affect the eukaryotic microtubules at 10 μΜ – 20 μM concentrations (Lopus and Panda 2006; Wang et al. 2016; Raghav et al. 2017), morphological effects on yeast cells were observed only at concentrations > 100 μM. However, yeast microtubules were not affected by berberine and sanguinarine. Differences in membrane lipid profiles and MDR efflux pumps between yeasts and mammalian cells might also contribute to differential resistance to the drugs being tested (Balzi and Goffeau 1991). Conversely, an inhibitory effect in yeast cells may not necessarily translate into toxicity in a human cell. These and the permeability of drugs in yeast cells represent an important caveat in using such heterologous expression systems for the screening of compounds against target molecules.”

[Lines 498-513]

There are very few SaFtsZ-GFP dot structure in fig 5B, and this is inconsistent with the SaFtsZ-GFP dot structure in fig 4A. Fig 5D has the same issue compare to Fig 4Ci

RESPONSE: We had probably not made it very clear the experimental differences between Figure 4 and 5 (Figure 2 and 3 in the revised manuscript), which has led to this apparent inconsistency.

The strong nmt1 promoter (thiamine repressible) takes about 18 hours for full-induction in the absence of thiamine (Forsburg 1993 - https://doi.org/10.1093/nar/21.12.2955). We have utilised the medium strength nmt41 promoter in our studies and hence, in Figure 2, expression of FtsZ-GFP fusions were allowed for longer periods of time (22 – 24 hours) in the experiments concerning sanguinarine and berberine treatments.

This has been now clearly mentioned in the revised version of the manuscript in the results section (lines 196-199) as well as in figure legends.

In contrast the very few dot structures or polymers in Figure 3 (revised manuscript) is because of a shorter period of expression of FtsZ-GFP (12 – 14 hours in the absence of thiamine). The shorter period of expression time in these experiments allowed us to test if PC190723 indeed induced the polymerisation of FtsZ, at a stage when the control cells still exhibited diffuse fluorescence and had minimal FtsZ assembly. Thus, the cultures were allowed to express FtsZ for a shorter period of time and imaged in the case of experiments presented in Figure 3.

This has been now clearly mentioned in the results (lines 259-263) as well as in figure legends in the revised manuscript.

We hope that we have now made these experimental differences clear and provide more clarity. We have also included this information (hours of induction) in the figure panel.

The concentration of PC190723 the author used is 20 µg/ml, which is enough for disrupting FtsZ function, however according to the Sanguinarine and Berberine experiments, the author may use higher concentration of PC190723 to assess its toxicity to pombe cells. Same as Sanguinarine and Berberine, does PC190723 has effect on microtubule?

RESPONSE: As suggested by the reviewer, we have tested the effect of PC190723 at a higher concentration (140.6 µM) similar to that of Sanguinarine and Berberine. We did not find any morphological changes in yeast upon treatment with higher concentrations of PC190723. Also, the drug did not seem to affect the yeast microtubules. These have been now included in the results section and new images have been added in the figure (Supplementary Fig. S3).

The following lines have been added in the revised manuscript to the results section:

“Earlier studies had reported that PC190723 was non-toxic to eukaryotic cells, including budding yeast (Haydon et al. 2008). We further tested if PC190723 resulted in morphological defects in S. pombe, like sanguinarine and berberine, at higher concentrations. However, consistent with the earlier reports, PC190723 was inactive against S. pombe at both 56.2 μM and 140.6 μM and did not cause any morphological changes (Fig. 2H iv). Further, PC190723 did not disrupt the yeast microtubules at either of the concentrations (Fig. S3 A iv and B iv).”

[Lines 294-300]

The authors mentioned much higher concentrations of drugs than normally used for mammalian cell cultures have to be used for fission yeast. Is there any criterion for this?

RESPONSE: In the discussion section, we had mentioned that “Much higher concentrations of drugs than normally used for mammalian cell cultures have to be used for fission yeast probably due to permeability issues because of the presence of a thick cell wall (Benko 2017 - DOI: 10.1186/s13578-016-0131-5).

This has now been mentioned in the results as well in the revised manuscript.

“Although we did not observe any growth defect in yeast cells at lower concentrations of the drugs, earlier studies have suggested that yeast cells possibly require higher concentrations of drugs than used for mammalian cells due to the presence of the cell wall, which is particularly thick in S. pombe (Benko et al. 2017; Pérez and Ribas 2004). We thus explored the possibility of cell toxicity to yeast cells at higher concentrations of the drugs.”

[Lines 234-239]

The following lines in the discussion have been modified in the revised manuscript to read as – “However, one of the major disadvantages of using fission yeast could be the need to use much higher concentrations of drugs than normally used for mammalian cell cultures to achieve an inhibitory effect. This could probably be due to the poor permeability of certain drugs in fission yeast because of its thick cell wall (Benko et al. 2017; Pérez and Ribas 2004). A similar effect of toxicity might arise at much lower concentrations in other eukaryotic cells, such as human cells.”

[Lines 498-503]

Minor comments: 1. There are two units used for drug concentration µM for Sanguinarine and Berberine and µg/ml for PC190723, I think they should be consistent.

We have now used µM for all drugs.

Check the units (µM and µg/ml) italic in text and figure legend.

We have now used µM for all drugs and corrected the italics. We apologise for the erroneous usage of italics in the text for µM.

Reviewer #3 (Significance (Required)):

The authors provided a proof-of-concept assay for studying bacterial cytoskeleton proteins in yeast cells. This idea will facilitate people to investigate the bacterial cytoskeleton proteins and also find compounds targeting them without affecting the yeast cells. This study will provide different perspectives to people who study cell biology and secondary metabolites discovery.

We hope that we have satisfactorily addressed all the concerns raised by the reviewers in the revised manuscript.

Thanking you,

With Regards

Dr. Ramanujam Srinivasan

Dr. Pananghat Gayathri

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Referee #2

Evidence, reproducibility and clarity

Dr. Srinivasin and colleagues previously developed a system where they expressed bacterial FtsZ in yeast and showed that it could assemble into polymers related to the Z rings. Here they develop this system further as a way to assay for drugs that may poison FtsZ, which would be candidates for new antibiotics. They test three drugs against three species of FtsZ. The results suggest that this system should be useful in screening new drugs that may target FtsZ. I would recommend publication after addressing a number of concerns and apparent contradictions.

Fig. 1 showing chemical formulas of the drugs, and Fig. 2 showing a schematic of the yeast expression system, are probably not needed.

The authors make a point that sanguinarine and berberine inhibit eukaryote cell morphology. In fact, what they show is that they affect yeast cell morphology. This may or may not extend to other eukaryotes. Also, other eukaryotic cells may be more sensitive to drugs than yeast. They should me more conservative in this claim that the system also screens for drugs effects on eukaryotes.

Fig. 3 has some new structural data that should be explored more quantitatively. My quick measurement gave 0.5 and 0.8 µm for the outside diameters of Ec and Sa rings. The spirals of Hp seem to be 0.8 µm outside diameter, similar to SA rings. These spirals may be related to those reported by Popp and by Andreu under certain buffer conditions. This should be explored and referenced.

But Fig. 4 presents a contradiction. Here the Hp control cells show long smooth polymers, not helical. This seems an important difference and needs to be addressed. Are the polymers sometimes straight and sometimes helical? After finishing the paper I see that in some experiments the HP is helical, and in others the polymers are straight and smooth. I think it would be important to determine what favors the two forms. If this remains a mystery, at least address it openly.

I am concerned that the quantitation of drug inhibition in Fig 4, 5 is flawed. Visually from 4A it looks like ~90-100% of control cells have polymers, and sang reduces polymers by 70% for Sa and Ec and 100% for Hp: this is based on the number of spots and filaments I see in Fig. 4 Aii. But the quantitation in D shows only 17-23% reduction for all three. These numbers were based on determining the fraction of cells that showed polymer (spots or lines) vs diffuse. It seems that cells are counted as containing polymer even if they had a great reduction in spots or lines, but still had a few. E.g., 4Aii Sa has 4 cells, two of them with no spots, one with only 2, and one with ~7, which totals ~1/3 the spots in control cells. Categorizing cells with only a couple of spots as polymerized, seems to be a poor way to quantitate. Would it not be better to count all spots in all cells, or measure the total length of line polymers, as a measure of inhibition.

Fig. 5 makes a convincing case that PC19 accelerates or enhances the polymerization of Sa and Hp. Fig. S2 shows that the structures of polymers are not changed when PC19 is added at 20 hrs, after polymers have already formed. It would have been nice to see for both 5A and S2A that the round spots had holes in the center, when imaged by SIM. Again the quantitation of cells as polymer vs diffuse seems ill suited, because it misses cells with a reduced number of spots.

Fig. 6 uses FRAP to show that PC reduces the dynamic exchange of Sa polymers by a factor of 3. It is remarkable to me that rapid exchange is not completely eliminated by PC. Regardless, it would be very important to reference the previous study of Adams..Errington 2011, where they showed the same thing for Foci in Bacillus. PC19 reduced the exchange from 3 to 10 s, but the foci were still very dynamic.

The analysis of the salt bridge as opposed to a single Arg or His being the cause of resistance to PC19 is an interesting addition to the study. In Fig. 8D some numbers do not agree between the caption and figure (R309/7; S226/7). The whole figure should be carefully checked.

I am not familiar with the Gram -ve and Gram +ve nomenclature. Why not simply gram- and gram+?

The Discussion is quite long largely because it repeats items from Results and Introduction. It is also redundant to hype the value of this system in both Introduction and Discussion; The Introduction should be sufficient. The Discussion should be pared down by eliminating repetition and focusing on relating results to previous literature, in particular items that have not been referenced previously in the paper. Also, I think we don't need the final "In summary" paragraph. That is already nicely presented in the Abstract.

The authors should probably provide references to other studies that have used yeast expression to study assembly of FtsZ. I am thinking in particular of papers from the Osteryoung lab looking at chloroplast FtsZ.

NO PAGE NUMBERS. Authors should be penalized a week delay for submitting a mss without page numbers.

Significance

This work should be of interest to the broad field of research on FtsZ. The authors present it as a new platform for assaying drugs targeting FtsZ, and researchers in this area will certainly be interested. It will also be of broader interest for the novel assay of assembly and exchange dynamics and how they may be modulated by small molecules.

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Reply to the reviewers

Manuscript number: RC-2022-01680

Corresponding author(s): Woo Jae, Kim

1. General Statements The goal of this study is to provide the groundwork for future studies of genetically controlled neuronal regulation of ‘interval timing’ through the provision of a behavioral paradigm. Interval timing, or the sense of time in the seconds to hours range, is important in foraging, decision making, and learning in humans via activation of cortico-striatal circuits. Interval timing requires completely distinct brain processes from millisecond or circadian timing. In summary, interval timing allows us to subjectively sense the passage of physical time, allowing us to integrate action sequences, thoughts, and behavior, detect developing trends, and predict future consequences.

Many researchers have tried to figure out how animals, including humans, can estimate time intervals with such precision. However, most investigations have been conducted in the realm of psychology rather than biology thus far. Because the study of interval timing was limited in its ability to intervene in the human brain, many psychologists concentrated on developing convincing theoretical models to explain the known occurrence of interval timing.

To overcome the limits of studying interval timing in terms of genetic control, we have reported that the time investment strategy for mating in Drosophila males can be a suitable behavioral platform to genetically dissect the principle of brain circuit mechanism for interval timing. For example, we previously reported that males prolong their mating when they have previously been exposed to rivals (Kim, Jan & Jan, "Contribution of visual and circadian neural circuits to memory for prolonged mating induced by rivals" Nature Neuroscience, 2012), and this behavior is regulated by visual stimuli, clock genes, and neuropeptide signaling in a subset of neurons (Kim, Jan & Jan, “A PDF/NPF Neuropeptide Signaling Circuitry of Male Drosophila melanogaster Controls Rival-Induced Prolonged Mating” Neuron, 2013).

Throughout their lives, all animals must make decisions in order to optimize their utility function. Male reproductive success is determined by how many sperms successfully fertilize an egg with a restricted number of investment resources. To optimize male reproductive fitness, a time investment strategy has been devised. As a consequence, we believe that the flexible responses of mating duration to different environmental contexts in Drosophila males might be an excellent model to investigate neural circuits for interval timing.

One of the most well-known features of human interval timing is the association of different sensory inputs with perception of time intervals, which influences our estimate of time intervals. Therefore, the first step toward comprehending the neural regulation of interval timing is to dissect the role that numerous sensory inputs play in determining the time duration. In this article, we discuss a different time-investment strategy adopted by males, called "Shorter-Mating-Duration" (SMD). According to our findings, male Drosophila with more sexual experience had shorter mating duration. During our investigation into the sensory inputs for SMD behavior, we found a small number of cells that express sugar receptors and pheromone receptors (ppk25 and ppk29) and thus transmit the multisensory information from females in order to generate memories of sexual experiences, which will determine the final decision of mating duration.

Our discovery of sensory integration mechanisms associated with complex behavioral trait in male Drosophila at the brain circuit and genetic network levels will be a huge step forward in our knowledge of interval timing behavior.

Description of the planned revisions

REVIEWER #1

1. • Overall I think this would be difficult for a general audience as the rationale and explanation of experiments needs to be clearer. * Answer: During the revision process, we will make our text more legible for wide audiences.

REVIEWER #2

1. • 'The knockdown of LUSH, an odorant-binding protein' Lush is expressed in trichoid sensilla in olfactory organs , from the beginning, they exclude the role of olfaction and later one they said 'suggesting that the expression of the pheromone sensing proteins LUSH and Snmp1 in Gr5a-positive gustatory neurons is critical for generating SMD behavior.' ? Therefore, I recommend If available, please provide a reference for the statement in the Methods section that the Orco1 line was "validated via electrophysiology", or include the electrophysiology data itself in this manuscript as supplementary figure. Ideally, positive behavioral controls for this line would also be included in the manuscript. * Answer: We value the reviewer's concern. LUSH has been discovered as an odorant-binding protein; nevertheless, current research suggests that LUSH may be involved in the sensing of additional pheromones to cVA, implying the presence of a lush-independent cVA detection mechanism [1]. Billeter et al. demonstrated in their paper that LUSH detects a female stimulatory chemical and modifies male mating latency (Fig. 2 of Billeter at al.). As Billeter et al. stated, our present understanding of pheromonal recognition in Drosophila is insufficient, and we concur. As a result, we attempted to validate the expression of Snmp1 in the male leg by experiments (Fig. 7I-J) performing sncRNA seq analysis on the Fly SCope dataset, as shown in Fig. 12. As demonstrated in Fig.12, Snmp1 and LUSH is higly expressed fly leg and wing system. Future study will look at the roles of Snmp1 and LUSH in female pheromone sensing, as well as PPK receptors.

Following the reviewer's advice, we will repeat the electrophysiologically validated Orco2 mutant phenotype with proper control and attach it when we submit the complete revision to the journal.

• What is this (GustDx6)? I suggest using Poxn mutant line. *

Answer: We value the reviewer's recommendation. We believe we have previously demonstrated that the Gr5a-mediated gustatory pathway is essential for the generation of sensory input for SMD behavior, but we will test the Poxn mutant and Poxn-RNAi to replace the GustDx6 mutant result.

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

REVIEWER #1

2. My copy of this ms does not have page numbers or line numbers, this makes it extremely difficult to identify where I am making queries/ suggestions. I don't know whether this is a decision of the journal or authors, but please change this in the future.* Answer: We put page numbers and line numbers.

3. A general point, there is simply too much in this ms. It covers too much ground and so doesn't give proper descriptions, discuss the consequences of the data fully or integrate properly with existing literature. Quantity does not equal impact. *

Answer: We appreciate the reviewer's insight. We have previously separated this document from our original preprint [2] in response to a prior reviewer's advice; we believe we have included too much data, which may confuse readers. As a result, we will delete all of the mechanosensory/thermosensory receptor screening data from our present paper and write a second manuscript on sensory integration for the production of SMD behavior. We also removed the most of sncRNA seq data analysis except Fig.12 which confirms our finding in a single diagram.

• Results paragraph 1 says that white mutant background had no effect "unlike that of LMD behavior as reported previously", ignoring that there has been a contrary report that extension of mating duration after exposure to a rival does not involve visual cues and so is not affected by the white mutation (Bretman et al 2011 Curr Biol). *

Answer: We recognize that there is a conflicting report concerning white mutation on LMD behavior, however because we are now reporting SMD rather than LMD behavior, we deleted the statement comparing white mutant results to earlier reports, as shown below;

“thus suggesting that the effect of the white mutant genetic background was not evident.” (line 97)

• A general point in the methodology, it's not very helpful just to say "as in a previous study" without giving at least a brief idea of what that was (e.g. the explanation of egg counting procedures).

A "sperm depletion" assay is described in the results that I cannot find any methodology for. *

Answer: We thank the reviewer for allowing us to clarify our lacking methodologies for a better comprehension of our manuscript.

We included the egg counting procedure to the EXPERIMENTAL PROCEDURES section to further illustrate our approach of egg laying assay as below;

“In short, wild type females mated with naïve or experienced males were transferred to a fresh new vial and allowed to lay eggs for 24 hr at 25°C. After 24 hr of egg laying, number of eggs were counted under the stereomicroscope. After we count the number of eggs, we kept vials in 25°C incubator and counted the total number of progenies ecolsed from them.” (line 956-960)

We included “Sperm Depletion from Males” section in EXPERIMENTAL PROCEDURES as below;

“To deplete sperm from males, 40 virgin Defexel6234 females which lacks SPR and shows multiple mating with males (Yang 2009) were placed in a vial containing four CS males for indicated time (2 h, 4 h, 8 h, and 24 h).” (line 880)

• Was the "excessive mating" with SPR females actually observed, or inferred from previous work? Needs to be clear. In what way do virgins expressing fruitless behave like mated females? It is so unclear how all the evidence in this paragraph leads to the conclusion that both cues from females and successful copulation. Especially as in the next paragraph experience with feminized females (with which the focal males cannot copulate) elicits the response.

It might be helpful to combine the results into a table, so it is easy to see under which conditions males reduce mating duration. *

Answer: We modified the sentence describing SPR mutant female experiment and added references as below;

“Sexual experiences with sex peptide receptor (SPR) mutant females which exhibit a delayed post-mating response and multiple mating with males [3] had no additional effect on SMD (Fig. 2I).” (line 135)

We clarify in which extent, fru>UAS-mSP virgin females behave like mated females as below;

“Virgin females behave like mated females by expressing a membrane-bound version of male sex-peptide in fruitless-positive neurons, hence rejecting the male's copulation attempt.” (line 136)

In the instance of feminized males, we assume that these feminine males can give adequate signals for inducing SMD and eliminated the term "successful copulation" since we are unsure if males can copulate these feminized males or not, despite the fact that males can mount and mate with them (Fig. 2O-P).

Tables S1 and S2 describe the conditions, genotypes, and descriptions of an experiments illustrated in Fig. 2. We believe that these tables may assist general audiences in comprehending our experimental design.

• Why are no statistics reported in the results? Identifying sig diffs on figures is not sufficient. I'm very sceptical that "mating duration of males showed normal distribution" for all comparisons, but then it's also difficult to identify which were analysed in this way (if statistics were properly reported this would not be an issue). *

Answer: We described our statistical analysis with mating duration previously [4–7] and followed the statistical analysis of copulation duration assay reported by Crickmore et al., published in CELL (2013) and NEURON (2020) [8,9]. To further validate our statistical analysis, we added estimation statistics which focuses on the effect size of one's experiment/intervention, as opposed to significance testing [10]. We already described our statistical analysis in EXPERIMENTAL PROCEDURES section in details. We also described our statistical analysis for mating duration will be same in all other figures in the Fig.1 legend.

We appreciate the reviewer's recommendation that the normal distribution of our mating duration data be validated. As a consequence, we performed the normailty test with Graphpad prism and added the histogram and QQ plot results to Fig. S1M and N. Table S3 also contains the results of the normality and lognormality tests.

• Gr5a/ Gr66a mediate acceptance/ avoidance of what? Why would you hypothesise these in particular to be involved? *

Answer: We accidentally left out the citation for that phrase and updated it with Wang et al.'s CELL (2004) paper. Wang et al. wrote in their article about taste representations in the Drosophila brain, “Our behavioral studies reveal that Gr5a cells recognize sugars and mediate acceptance/attractive behaviors whereas Gr66a cells recognize bitter compounds and mediate avoidance…. This suggests that Gr5a cells may be “acceptance” cells rather than “sweet” cells…. Our expression and behavioral studies reveal that Gr5a marks cells that recognize sugars and mediate taste acceptance, whereas Gr66a marks cells that recognize bitter compounds and mediate avoidance.” [11]

As a result, we hypothesize that Gr5a and Gr66a-positive cells influence acceptance or avoidance of "taste." We also changed certain sentences to make them clearer, as seen below;

“Of the various gustatory receptors, Gr5a marks cells that recognize sugars and mediate taste acceptance, whereas Gr66a marks cells that recognizes bitter compounds and mediates avoidance.” (line 173)

• As Orco was not found to affect the behaviour, why test Or67d? *

Answer: We appreciate the reviewer bringing this to our attention. We omitted the Or67d result from the present manuscript to simplify it and make it easier for readers to grasp.

• "Mate guarding" suddenly appears in the modelling section. Can a difference of a couple of minutes in a mating duration of 15-20min really be considered mate guarding? A similar variation in response to rival males is not considered mate guarding, but is linked to adjustments in ejaculate expenditure (admittedly not in a very straight forward way). Surely in a system like this the benefits arise more from how many females the male can mate with in a given time? How does this model relate to any of the previous models of mate guarding?

In this section the work of Linklater et al 2007 is important, they showed progeny declined over successive matings, and related this to exhaustion of Acps rather than sperm. I would urge the authors to consider that what they observe does not necessarily have an adaptive explanation. *

Answer: We have defined “mate guarding” in the text now. The costs and benefits of mate guarding have been extensively studied in insects and demonstrated to shape the optimal mating duration of males. In our experiment, we cannot specify whether the shortened mating duration was caused by the adjustments in ejaculate expenditure or a shorted stay after the ejaculation. Instead, our model has a general assumption that the costs of mate guarding increase linearly at the same rate in both pre- and post-ejaculation periods, which is highlighted in the model text.

There exist many models for the optimal mating duration (earlier models include Grafen and Ridley, 1983. A model of mate guarding. J. Theor. Biol. 102: 549 – 567 [12]). While our model was not built upon a novel theoretical approach (it was built based on the classical Charnov’s marginal value theorem equation), our model was developed specifically for generating testable predictions for the observed SMD behaviors.

We have rephrased the text as follow;

“This model assumes that (i) the shortened (or prolonged) mating duration is controlled by males and shaped by a trade-off between the benefit of mate guarding (remaining with the female both before and after the sperm ejaculation) and opportunistic costs (e.g. searching for another mate).” (line 970)”

• I can't find a data accessibility statement. *

Answer: We added it in the manuscript.

• That said, a current grand challenge in understanding behaviour is discovering the mechanisms that enable individuals to respond plastically to changing environments. This speaks directly to that challenge. However, this behavioural observation is not novel, as claimed. Generally the idea of refractoriness is widely known, and specifically the reduction in mating duration over successive matings in D. melanogaster was shown by Linklater et al 2007 Evolution. Moreover, the time between exposure to females has been shown to be important. Linklater et al 2007 gave males mating attempts in quick succession and observed the decrease in mating duration, whereas given recovery time of 3 days, males either mate equally as long, or even longer across their life course (Bretman et al 2011 Proc B, Bretman et al 2013 Evolution). These papers should be discussed, and more broadly the work understood in the light of previous knowledge. The behaviour does not need to be novel for this manuscript to make a significant contribution to the field. *

Answer: We believe the reviewer highlighted relevant past research that examined the influence of female experiences on mating duration. We agree with the reviewer that SMD behavior does not have to be original in order to contribute significantly to the field. As a result, we examined past reports and updated the introduction as follows;

“It has been reported that previous sexual experience with females influences the mating duration of male D. melanogaster [15,16,34]; however, the neural circuits and physiology underlying this behavior have not been deeply investigated. Here, we report the sensory integration mechanisms by which sexually experienced males exhibit plastic behavior by limiting their investment in copulation time; we refer to this behavior as "shorter mating duration (SMD)."” (line 85)

• Both in the introduction and discussion the extended mating duration in response to rivals is raised. A great deal of work has been done on this plasticity and yet the way this is written implies just two papers from these authors (whilst referencing others elsewhere). *

Answer: We agree with the reviewer. In the introductory and discussion sections, we cited as many key publications explaining the plastic responses of male mating duration as we could.

__REVIEWER #2

__

1. • Summary: The submitted manuscript reports that Drosophila melanogaster males use information derived from their previous sexual experiences from multiple sensory inputs to optimize their investment in mating. They refer to this plasticity as 'shorter-mating duration (SMD)'. SMD requires sexually dimorphic taste neurons. They identified several neurons in the male foreleg and midleg that express specific sugar, pheromone and mechanosensory receptors. Unfortunately, several aspects of the study design and methods used are inappropriate. Although the statistical approaches used are appropriate, the results are questionable. The discussion and conclusions are therefore too speculative in my view and overstretch the implications of the results as presented. Below I explain each one of these concerns about the study design, methods and results in detail as follows.* Answer: We appreciate the reviewer's assessment, especially the statement that our statistical approaches were appropriate. We will revise our manuscript in response to the reviewer's suggestions.

2. The conclusions (as the authors point out) hinge on small (often extremely small) effect sizes. This is not an insurmountable problem, so long as the assays are robust across trials. Unfortunately, they are not-the variation in the baseline for control replicates is often as large as, or larger than, the effects from which the conclusions are derived. Given the extreme experimental challenges of small effect size combined with large intertrial variability, it is notable that the authors do not report any likely false negative or false positive data, as would be frequently expected under these conditions. One explanation for the reproducibility of statistical effect seen across many experiments despite these experimental hurdles is manipulation of sample size. The authors acknowledge the extreme variability in sample size offer seemingly harmless explanations, but a closer look shows how problematic this practice is. For example, see Figure 1 (I, J, L) there is a big different between naive and experience males? *

Answer: We value the reviewer's feedback. Several research have been conducted to investigate the mating duration of male fruit fly. For example, our lab [2,13–15] and others [13–30] have regularly reported that previous rival exposure increases male fruit fly mating duration. Bretman A et al. utilized 49-59 males in their studies to compare the variations in mating duration between circumstances. Crickmore et al. also reported the effect of mating duration differences caused by genetic or experimental modification [8]. They utilized 10-18 male flies in their study to compare the variations in mating duration across circumstances, as shown in Figs. 1G (n=15-18) and 2A (n=10-27). All of these findings indicate that our mating duration sample size is sufficient to examine the effect size variations between the naive and experienced conditions. To confirm our statistical analysis further, we incorporated estimate statistics, which focus on the effect size of one's experiment/intervention rather than significance tests [10]. We have already detailed our statistical analyses under the EXPERIMENTAL PROCEDURES section. We conducted hundreds of mating duration assays using this configuration and confirmed that all of our results are reproducible in a blind test. As a result, we believe our mating duration assay has been validated by other groups' findings, several analytic tools, and numerous blind tests conducted by us. We appreciate the reviewers' concerns, but our data meets the reproducibility requirements.

• I am not sure if you keep using the same control with different experiments (that is okay if those exp is done in the same time) as in figure 1 B, I,J,K,L.But I don't think you did Fig 1B in the same time with Fig 1I, J, K,L. *

Answer: We appreciate the reviewer's feedback. Yes, all of our tests comparing the differences in mating duration between naive and experienced conditions were conducted under the same conditions and at the same time. We replaced Fig.1B with new data (n=49-51) obtained lately in a new lab in China. As previously stated, SMD behavior could be reproduced by the same Canton S genotype in different locations by different experimenters.

• It will be clear if you mention in the text how much reduction in percent happened in copulation duration when the males had previous sexual experience? *

Answer: We appreciate the reviewer’s suggestion and added in the manuscript as follow;

“We found that the mating duration of various wild-type and w1118 naïve males are significantly longer (wild type 15.7~15.8%, w1118 12.4%) than that of sexually experienced males (Fig. 1B-D, Fig. S1A)” (line 99)

• 'Drosophila simulans, the sibling species of D. melanogaster also exhibits SMD, thus suggesting that SMD is conserved between close species of D. melanogaster (Fig. S1B).'. If you want come with this conclusion, you need to test D. erecta, D. sechelia and D. yakuba. *

Answer: We appreciate the reviewer's feedback. We removed the D. simulans data because it is not required for the conclusion of this manuscript. In future research, we will look on the conservation of SMD behavior between species.

• The authors mention that Gr66a is salt. This is not 100% correct. GR66a is expressed in many bitter sensing neurons and is required for the physiological and behavioral responses to many bitter compounds. check this reference DOI:https://doi.org/10.1016/j.cub.2019.11.005. *

Answer: We made the following changes and cited the article reviewer's suggestion.

“Of the various gustatory receptors, Gr5a marks cells that recognize sugars and mediate taste acceptance, whereas Gr66a marks cells that recognizes bitter compounds and mediates avoidance (Wang et al, 2004; Dweck & Carlson, 2020).” (line 180)

• Drosophila melanogaster mating duration is between 21- 23 mins. I never saw copulation duration in normal condition (control) 10-15 mins as in figure fig 2E, Fig 7 C,E,F, Fig 8 E and fig 12 G . To the best of my knowledge, of all of the papers on copulation duration, the only one that ascribes a shortened duration to manipulations of the female is Rideout...Goodwin Nature Neuroscience 2010, who argue that this shortening results from markedly increased female activity/agitation during mating, leading the male to terminate early. *

Answer: We appreciate the reviewer's feedback. Copulation duration in Drosophila melanogaster male is extremely variable and has been reported to be approximately 20 minutes. However, as other groups documented, male copulation duration can range from 10-15 minutes depending on sperm completion (Fig. 1a-c of Bretman A et al.) [30] and genetic background (Fig. 1C, Fig. 2E, Fig. 5D, and Fig. 7A and E of Crickmore et al) [8]. And, as previously stated, males dominate copulation duration [8,30], not females, and we always utilized the same genotype of females for mating duration experiment. As a result, we believe that these rather short mating duration outcomes are the product of a distinct genetic background. Because we employed the same genotype of males while altering the female experience condition, we believe our mating duration results are all equivalent and comparable.

• In some experiments, the authors test very few number of replicates which is not convinced me to their conclusion as example Fig 2F and Fig 12 E. Why you test 100, 103 replicates in this exp fig 10 F? How you compare 47 replicates against 9 replicates in fig S10 I? *

Answer: We appreciate the reviewer's input. As we previously stated in response to Reviewer Question 2, the n number of males exhibited in Figs. 2F and 12E is statistically significant. To corroborate findings with replication, we examined 100, 103 duplicates of Fig. 10F, which represents pyx-RNAi screening results. The results of Fig. S10I are screening data, and we cannot rule out the possibility that TrpA1 knockdown in Gr5a neurons affects the mating success of sexually experienced males. We only placed it there because it was screening results and the differences between naive and experienced conditions were substantial despite the small sample size. However, we deleted Fig. 10F and Fig. S10I data from the current paper in response to Reviewer #1's advice, thus it will not be an issue for the manuscript's conclusion.

• 'Next, to decipher whether DEG/NaC channel-expressing pheromone sensing neurons require the function of OBP, we expressed lush-RNAi using ppk23-, ppk25- and ppk29-GAL4 drivers to knockdown LUSH in each channel-expressing neuron. The knockdown of LUSH in ppk25- and ppk29-GAL4 labeled cells, but not in ppk23-GAL4 labeled cells, led to a disturbance in SMD behavior, thus suggesting that LUSH functions in ppk25- and ppk29-positive neurons to detect pheromones and elicit SMD behavior (Fig. 9G-I). The knockdown of SNMP1 in ppk29-GAL4- labeled neurons also inhibited SMD behavior (Fig. 9J), thus suggesting that SNMP1 also functions in ppk29-positive neurons to induce SMD behavior.' What about ppk25? **

*

Answer: As indicated by the reviewer, we included ppk25-GAL4/snmp1-RNAi data in Fig. S9I, indicating that snmp1 expression in ppk25-positive cells is similarly implicated in SMD behavior.

• There are no page or line numbers throughout the ms! *

Answer: We included page and line numbers.

• The use of subheadings in the results section makes reading much easier.*

Answer: We added subheadings in the results section.

• 'We found that the mating duration of various wild-type and w 1118 naïve males are significantly longer than that of sexually experienced males (Fig. 1B-D, Fig. S1A)' . I think you should change various wild type to CS and WT Berlin as in legend and figure 1B,C .*

Answer: The revised sentence is as follows:

“We found that the mating duration of Canton S, WT-Berlin, Oregon-R, and w1118 naïve males are significantly longer (wild type 15.7~15.8%, w1118 12.4%) than that of sexually experienced males (Fig. 1B-D, Fig. S1A)” (line 102)

• Suggested exp , Fig S1E-H , they might test 2,6, 12 hours males separation from females to test exactly when this behavior change over time. *

Answer: We value the reviewer's recommendation. As seen in Fig. S4B of Kim et al., we have previously conducted experiments for examining the memory circuit of SMD [6]. Briefly, the male with a shorter mating duration recovers completely after 12 to 24 hours of isolation from females. As we are currently preparing the memory section of the SMD study, this information will be included in a future manuscript.

• General comment in figures, you could remove the common y axis as example in figure 1 B,C,D , difference between means and mating duration. *

Answer: We welcome the reviewer's idea, however in this situation we believe that the y axis of each data set is independent from one another and will thus retain the originals. We feel this would be more useful for the general audiences.

• You might move the number of replicates to the legend. *

Answer: We appreciate the reviewer's idea, however we feel that adding more information to the graphic will aid the general audience in comprehending our statistics.

• Latin name should be italic as example Drosophila simulans.*

Answer: We fixed it.

Description of analyses that authors prefer not to carry out

N/A

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28. Fowler EK, Leigh S, Rostant WG, Thomas A, Bretman A, Chapman T. Memory of social experience affects female fecundity via perception of fly deposits. Bmc Biol. 2022;20: 244. doi:10.1186/s12915-022-01438-5
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30. Bretman A, Fricke C, Chapman T. Plastic responses of male Drosophila melanogaster to the level of sperm competition increase male reproductive fitness. Proc Royal Soc B Biological Sci. 2009;276: 1705–1711. doi:10.1098/rspb.2008.1878

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Reply to the reviewers

Reviewer #1:

Minor edits

1. Line 91. Is a bit misleading to say "many other vibrios" possess T3SS. This conveys that this is perhaps the majority, but T3SS in vibrios is at best 50/50. I think best just to delete this sentence.

We deleted this comment, as suggested.

1. Revised to "Thus, in this study, we set out to..." Since the entire paragraph starts with "recent study" I missed that this was summary of new data rather than preview of new results.

The sentence was revised as suggested.

1. Line 503. Correct "xxx-584" or more detail on what this means.

We Thank the reviewer for pointing out this typo._ This refers to the deletion made in tie1, in the region corresponding to nucleotides 485-584 of this gene. The text was corrected accordingly.

1. Line 603. Salmonella should be italicized.

Corrected.

1. The labelling of the figures is pretty complicated with the long genetic designations. Is it reasonable to for example name the ∆vprh/∆hns1 strain with an abbreviation (such as ∆VH)? Or instead create a strain name, common used approaches would be HC## (for Hadar Cohen) or TAU# for Tel Aviv University. If you go this route, be sure to update the strain list. The current method can be followed, the figures are just complicated.

We thank the reviewer for raising this concern. We acknowledge the difficulty in following the many different strains and mutations. Nevertheless, after considering the proposed modifications to the strain names, we believe that they will not add much clarity, and may even cause some confusion. Therefore, we respectfully decided to keep the current nomenclature in place.

Reviewer #2:

Minor edits

1. The authors used a hyperactive T6SS (HNS mutant) to investigate its toxicity. Would the authors be able to use a wild type strain to reproduce the function of T6SS?

We have yet to reveal the external cues that lead to full activation of T6SS3 in vitro. Therefore, in the current study we used genetic tools, such as hns deletion or Ats3 over-expression, to monitor the effect of this system on immune cells. We will dissect the activating conditions in future studies, but we believe that the use of genetic tools should not affect the validity of the results in the current study, nor their timely publication.

1. The authors showed that Tie1 and Tie2 are secreted by T6SS3. It is important to show if they are actually delivered into the host cells during infection. Otherwise it is hard to conclude that they are truly effectors. The primary concern is the lack of in vivo studies to show that Tie1 and Tie2 are actually effectors that play a role in activation of NLRP3 inflammasome._

We present 3 pieces of evidence that, when taken together, support the conclusion that Tie1 and Tie2 are T6SS3 effectors: 1) the proteins are secreted in a T6SS3-dependent manner; 2) their deletion does not hamper overall T6SS3 activity; and 3) their deletion causes the same loss of NLRP3-mediated inflammasome activation and pyroptosis as does inactivation of T6SS3 by deletion of its structural component, tssL3. Although we agree with the reviewer that directly showing delivery of Tie1 and Tie2 into host cells will further strengthen our conclusion, such experiments are quite challenging and difficult to interpret, especially with T6SS effectors that can use diverse mechanisms for secretion through the system. This point was also noted by reviewer #3: “…I believe they were suggesting to demonstrate secretion in host cells. Although this would be nice, it is non-standard and technically not feasible. These types of experiments require genetically fusing the effector with either an enzymatic moiety (e.g. Beta lactamase) or fragment of split GFP. Although such approaches have been previously performed, they often result in either blocked or aberrant secretion due to the presence of the added fragment."

Regarding the reviewer’s comment on the lack of in vivo studies: we agree that these are extremely important, yet they are beyond the scope of the current work, as concurred by reviewers #1 and #3:

Reviewer#1 with regard to Reviewer#2: "I don't think mouse (or aquatic animal) studies are essential for this study. The work contributes nicely to our understanding molecular mechanisms of this T6SS system. As noted in my review, there are many additional lines of study that can be pursued from this work, including animal studies, but this should not preclude publication of this work that is itself an intact unit."

Reviewer#3 regarding reviewer #1's comment on Reviewer#2: "I don't believe that reviewer #2 was suggesting to perform mouse or aquatic animal studies by suggesting in vivo demonstration of secretion…”

Reviewer #3:

Major comments:

1. If the authors believe that GSDME partially compensates in the absence of GSDMD, have they infected a GSDME/GSDMD double knockouts to see if there is an additive effect?

Indeed, this is a very interesting and specific question for the cell death field. We do not currently possess such a GSDME/GSDMD double knockout mouse, and generating one will be a long endeavor. Since its absence does not diminish the importance or the conclusions of the current work, we think that it should not warrant a delay in publication. We do plan to address this question in future studies.

1. It is clear that Ats3 regulates T6SS3, but not the T6SS1; however, there no evidence suggesting that Atg3 does not regulate other gene clusters. For example, have the authors performed RNA seq to compare the transcriptomes of WT and an Ats3 mutant? If not, the authors should refrain using the words "specific activation".

We thank the reviewer for this important note. Indeed, we lack additional data indicating that Ats3’s effect is indeed restricted only to T6SS3. Therefore, we modified the text accordingly and removed mentions of specific T6SS3 activation.

1. In figure 6B, it's unclear why the bacteria infecting cytochalasin D-treated cells grow more than the T6SS3 mutants in the absence of cytochalasin D.

The difference probably stems from the fact that phagocytosis, the major mechanisms by which BMDMs kill bacteria, is hampered in the presence of cytochalasin D, thus allowing bacteria to grow more than when the BMDMs phagocytose them. The results show that in the absence of cytochalasin D, an active T6SS3 counteracts the killing effect by BMDMs with functional phagocytosis.

Minor comments:

1. Figure 1A and other secretion assays: The Western blots include loading control (LC) blots. These are non-standard, non-informative, and not required with the inclusion of the western blots on the "cells" fraction. I would suggest removing these as they may confuse the reader.

We respectfully disagree. Loading controls are standard in bacterial secretion assays, and they are important since they confirm comparable loading and allow proper analysis of the results, especially since we aim to determine whether certain mutations affect the expression of T6SS components. Notably, some groups choose to blot for a cytoplasmic protein (e.g., RpoB in Allsop et al., PNAS, 2017; Liang et al., PLoS Pathogens, 2021) instead of showing overall loaded proteins, as shown in our figures.

1. Line 503: "xxx" should reflect the actual nucleotide nubmers_

We thank the reviewer for pointing out this typo._ This refers to the deletion made in tie1, in the region corresponding to nucleotides 485-584 of this gene. The text was corrected accordingly.

1. Since V. proteolyticus is an aquatic pathogen, have the authors tried to infect corals, fish, and crustaceans (or derived cells) with WT and effector mutants?

This is an interesting point, and indeed we are setting up such systems and we plan to perform such experiments in the future as part of follow up projects. However, these in vivo studies are beyond the scope of the current manuscript, as also noted by the reviewer in the cross-consultation comments: “…my previous comment on infecting aquatic animals or cells derived from them is non-standard and not necessary…”

1. Are the targeted host proteins in this study (performed with murine BMDM) conserved in the natural hosts for V. proteolyticus?

We hypothesize that the conservation is not in the pathway components that are activated upon infection, but rather in the ability of the host cell to sense danger (i.e., to sense the effect of T6SS3 effectors on the host cell or one of its components), which is the role of the NLRP3 inflammasome in mammalian cells. It is well documented that major differences in immune mechanisms exist between mammals and the potential natural marine hosts of V. proteolyticus (e.g., corals, arthropods, and fish); therefore, the conservation at the protein level is low. Nevertheless, basic signaling pathways, such as programed cell death, are conserved between the different phyla. For example, a caspase-1 homolog which was found in arthropods (Chu, B. et al. PLoS One (2014). doi:10.1371/journal.pone.0085343) probably induces an apoptotic-like cell death mechanism, similar to apoptosis in C. elegans. We now provide further discussion on this point in the text (lines 648-659).

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Referee #1

Evidence, reproducibility and clarity

This paper by Cohen et al described discovery of the function of novel genes in the T6SS operon of Vibrio proteolyticus, a Vibrio isolated from corals. V. proteolyticus also impacts other sea animals. The T6SS3 in particular is found to kill eukarytoic phagocytic cells following engulfment of bacteria into the phagocyte. This strategy of killing phagocytic cells following entry has been shown for other Vibrios. The net goal is protection of the population by the bystander effector. The study first shows that deletion of H-NS (a global negative regulator) stimulates T6SS facilitating ease of work by pushing the system to great cell killing. This allowed them to probe the mechanism of cell death and reveal it as NLRP3 dependent, capase 1 dependent pyroptosis via pore formation by Gasdermin D. Activation of the inflammasome is also linked to cleavage and release of IL-1beta. When GSDMD is absent, there was a slower cell killing by GSDME via capsase 3 activation. The stimulation of this system is additive by two newly recognized T6SS effectors Tie1 and Tie2.

The study is complete, the experiments are well conducted and well controlled. The experiments show reproducibility. The manuscript text is clear, Overall. I suggest no changes in the results or experiments and suggest only a few minor edits of the text.

Minor edits

Line 91. Is a bit misleading to say "many other vibrios" possess T3SS. This conveys that this is perhaps the majority, but T3SS in vibrios is at best 50/50. I think best just to delete this sentence.

Line 102. Revised to "Thus, in this study, we set out to..." Since the entire paragraph starts with "recent study" I missed that this was summary of new data rather than preview of new results.

Line 503. Correct "xxx-584" or more detail on what this means.

Line 603. Salmonella should be italicized.

Figures. The labelling of the figures is pretty complicated with the long genetic designations. Is it reasonable to for example name the ∆vprh/∆hns1 strain with an abbreviation (such as ∆VH)? Or instead create a strain name, common used approaches would be HC## (for Hadar Cohen) or TAU# for Tel Aviv University. If you go this route, be sure to update the strain list. The current method can be followed, the figures are just complicated.

Referees cross-commenting

With regard to Reviewer#2, I don't think mouse (or aquatic animal) studies are essential for this study. The work contributes nicely to our understanding molecular mechanisms of this T6SS system. As noted in my review, there are many additional lines of study that can be pursued from this work, including animal studies, but this should not preclude publication of this work that is itself an intact unit.

Significance

The work is significant in that it links T6SS to a eukaryotic killing system and discovers novel details regarding the mechanisms of death, that may impact our knowledge of other Vibrio T6SS (including V. cholerae) that also target eukaryotic cell actin. There are remaining questions that could be probed, but these are in my opinion major studies that would easily themselves comprise new papers if done properly and thus are not essential for this paper. These include the struture and biochemical activity of Tie1 and Tie2 and the mechanism of caspase-8 independent activation of caspase-3 to then cleave GSDME. Why NLRP3 is required for capase 3 activation is also an open question. I look forward to following this work for some time to come. The authors have revealed very interesting effectors and interesting cell biological process that will merit multiple years and multiple manuscripts to unravel. This work will be of interest to the community interested in bacterial toxin systems (microbial pathogenesis), the bacterial effector mechanism field (biochemistry and cell biology), and the inflammasome activation field (immune systems). The work will be of interest (with essentially no modification) directed at these fields of interest.

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Reply to the reviewers

Reviewer #1:

Major comments:

In general, the data support the conclusions. I cannot comment on the atomistic simulation experiment as it is outside of my expertise. I had some difficulties interpreting Figure 2 as the contrast in the colour panels made it difficult to assess the different staining patterns. I would recommend changing the blue to cyan for easier visibility. While I agree that there are some differences between Fig 2F and Fig 2G it is not simple for the non-expert to distinguish the gonadal mesoderm from the somatic mesoderm. I think the enlarged panels could do with also showing the overlap in staining, or at least a tracing of the different cell populations so that the gonadal mesoderm can be clearly defined. Please also add some scale bars to the figure. Figure 3 demonstrates clear differences in gonad morphology between male and female mutants but the contrast in the colour panels A-G could also be improved. Panels H-J are very clear.

Response: As suggested by Referees 1 and 3 we have modified the colour channels in all figures. We have also enlarged the figures taking away the uninformative region and focused around the enlarged gonads and added scale bars. For Fig 2F-G, we have added a close up of the region of interest both in colour and in black and white. These changes have increased the contrast and facilitate the data interpretation to non-expert readers.

The rescue experiment in Figure 4 is clearly presented but could the DLC3 mutants in the graph (panel b) please be named similarly to the schematic proteins shown in panel a.

Response: We have changed the names to maintain nomenclature uniformity.

I found the difference between the RhoGAP domain mutants and the StART domain mutants of Cv-c to be clearly defined, and correlate with DLC3 function. This is a very interesting result that indicates multiple molecular functions for the Cv-c /DLC family.

Response: The methods are well described, statistics adequate and the data well described._

Minor Comments:

My only suggestion for the text is to provide a more through description of the StART domain in the introduction.

Response: We have included the following paragraph in the introduction describing the StART domain:

“This family of proteins share different domains: besides the Rho GTPase Activating Protein domain (GAP), they present a protein-protein interacting Sterile Alpha Motif (SAM) at the N terminal end and a Steroidogenic Acute Regulatory protein (StAR)-related lipid transfer (StART) domain at the C terminal. StART domains have been shown in other proteins to be involved in lipid interaction, protein localization and function.”

Reviewer #2:

My only issue with the present study is to how well the present experimental findings in Drosophila translate to humans. As far as I can tell the present studies show that inactivating mutations in Cv-c in Drosophila result in failure of germ cell enclosure by somatic cells into the testis, resulting in sterility. In humans, and in experimental mouse transgenic lines, it has been well established that absence of germ cells does not of itself lead to failure of testis differentiation and onward development, nor does it lead automatically to sex reversal or impairment of masculinization. For the latter to occur, there must be impairment/failure of fetal Leydig cell function such that insufficient androgen is produced to effect genital/bodywide masculinization. Obviously, this will happen if no testis forms as appears to be the case in the new human DLC3 mutant reported in the present manuscript (although detail on this is unfortunately lacking). This appears to be different to the previous published DLC3/STARD8 mutant sisters, in whom the phenotype appears to reflect failure of steroidogenesis. Is the proposal that DLC3/STARD8 plays a role in both testis differentiation and in Leydig cell function (steroidogenesis) or is this due to different DLC3 genes? I think the authors need to address these key issues in their discussion, if only to highlight that there are at present many gaps in our understanding.

The reviewer says:

“As far as I can tell the present studies show that inactivating mutations in Cv-c in Drosophila result in failure of germ cell enclosure by somatic cells into the testis, resulting in sterility.”

Response: This sentence does not represent the spirit of our findings accurately and this probably reflects the fact that we stressed the interaction between somatic mesodermal cells and germ cells in Drosophila which probably concealed that the main defects in Cv-c mutants are caused by the abnormal interaction of the mesodermal cells with germ cells but also among themselves. Our study provides insights about a new conserved pathway required in the mesodermal cells for the maintenance of an already formed testis, and only indirectly can be considered to deal with sterility. We show that Cv-c is required in the mesodermal cells for the correct maintenance of the testis structure, that when it fails leads to the testis dysgenesis which, among other defects, releases the germ cells. We show that in the absence of Cv-c function in the testis, the mesodermal pigment cells do not form a continuous layer around the testis and the ECM surrounding the testis breaks. We also show that the interstitial gonadal cells fail to ensheath the germ cells and as a result of all these the germ cells become dispersed. These perturbations can be partially corrected by expression in the testis mesoderm of human DLC3 or Drosophila Cv-c that in both cases require a functional StART domain. Thus, our results suggest that Cv-c/DLC3 have a fundamental function on the mesodermal testis cells that has been conserved. These results indicate that, as in Drosophila, the primary cause for the gonadal dysgenesis in DLC3 human patients is due to the abnormal maintenance of the testis mesoderm cells, which include both Sertoli and Leydig cells. Thus, our proposal is that DLC3/STARD8 plays a role in testis maintenance through its function in mesodermal cells which will probably affects both Sertoli and Leydig cell function.

To clarify the issue raised by the referee we have modified both, the introduction and the discussion to highlight that although humans and Drosophila diverged millions of years ago there are similarities regarding gonad stabilisation.

We have modified the introduction to clarify this issue:

“Gonadogenesis can be subdivided into three stages: specification of precursor germ cells, directional migration towards the somatic gonadal precursors and gonad compaction. In mammals, somatic cells, i.e. Sertoli cells in male and Granulosa cells in females, play a central role in sex determination with the germ cells differentiating into sperms or oocytes depending on their somatic mesoderm environment. In humans, Primordial Germ Cells (PGCs) are formed near the allantois during gastrulation around the 4th gestational week (GW) and migrate to the genital ridge where they form the anlage necessary for gonadal development (GW5-6). Somatic mesodermal cells are required for both PGCs migration and the formation of a proper gonad. Once PGCs reach their destination, the somatic gonadal cells join them (around GW 7-8 in males, GW10 in females) and provide a suitable environment for survival and self-renewal until gamete differentiation {Jemc, 2011 #413}. Thus, mutations in genes regulating somatic Sertoli and Granulosa support cell function in humans are often associated with complete or partial gonadal dysgenesis in both sexes and sex reversal in males {Zarkower, 2021 #430; Knower, 2011 #418; Brunello, 2021 #399}. Other mesodermal cells, the Leydig cells, also play an important role in the testis by being the primary source of testosterone and other androgens and maintaining secondary sexual characteristics.”

Also we have added a paragraph in the discussion to emphasize this argument:

“We show that in the absence of Cv-c function in the testis, the mesodermal pigment cells do not form a continuous layer around the testis and the ECM surrounding the testis breaks. We also show that the interstitial gonadal cells fail to ensheath the germ cells and as a result of all these the germ cells become dispersed from the testis. These perturbations can be partially corrected by expression in the testis mesoderm of human DLC3 or Drosophila Cv-c that in both cases require a functional StART domain. Thus, our results suggest that Cv-c/DLC3 have a fundamental function on the mesodermal testis cells that has been conserved. These results indicate that, as in Drosophila, the primary cause for the gonadal dysgenesis in DLC3 human patients is due to the abnormal maintenance of the testis mesoderm cells, which include both Sertoli and Leydig cells”.

I would also suggest that the authors highlight another potentially more important spin-off from such studies, namely that understanding of the regulation of DLC3/STARD8 genes, and what might perturb their expression/action would appear to present a whole new area for exploration in relation to testicular dysgenesis/masculinization disorders.

Response: We have modified the last part of the discussion to introduce referee 2’s suggestion:

“Our work points to DLC3/Cv-c as a novel gene required specifically in testis formation. Adding DLC3 to the list of genes involved in 46X,Y complete dysgenesis opens up a new avenue to analyse the molecular and cellular mechanisms behind these disorders that could help in diagnosis and the development of future treatments”.

Reviewer #3 :

Major comments:

1. This study has shown the expression pattern of cv-c and the consequence of cv-c mutation on different aspects of gonad development. However, one major comment is there is no quantification of the expression levels as well as the scoring of the mutant phenotypes.
2. In Figure 2, for instance, I recommend that the authors display the quantification of the fluorescence intensity of the cv-c expression under all circumstances (in situ hybridization as well as protein-trap based GFP expression) to better depict the differences among the male vs female gonad.

Response: We don’t think quantifying the stainings will add much to the results. We believe that the changes performed increasing the images’ contrast and their amplification are sufficient to illustrate our statement about cv-c being expressed in testis but not in ovaries.

1. In Figure 3, the authors show the different gonad developmental defects associated with the cv-c mutation. Specifically, the authors show that the gonad mesoderm cells are displaced with the pigment cells failing to ensheath the germ cells. In addition, the authors also suggest that there is an increased frequency of germ cell blebbing, an indication of migratory activity. However, there is no quantification of these findings. I think the authors should display a quantitative estimation of % of the mutant gonad depicting these phenotypes vs the normal gonad to have a perspective of how penetrant the phenotypes are.

Response: As referee suggested, we have quantified bleb phenotype. The results are presented in figure 3, panel J.

1. In Figure 4, the authors attempt to rescue the Cv-C mutation linked gonadal defects by overexpressing different Cv-C protein variants. The rescue experiments are not very clear. The graph shows the % of normal testes under different genotypic combinations. It is not very clear what the authors mean by normal (in what context)? Since the mutation results in different defects of gonad development, I think recommend that represent the rescue in terms of these defects. It would be interesting to see for instance, what happens to the blebbing or germ cell ensheathment phenoype upon rescue. How many % of testes show the rescue as compared to cv-c mutants?

Response: The percentages are quantified considering if the testes have any germ cell outside the gonad. We have added a line to clarify this point in the figure legend: “…quantified as encapsulated gonads with all germ cells inside the testis as assessed by Fisher-test”.

Nevertheless, we are going to quantify the number of ECM breaks and show the results in the reviewed manuscript.

1. Did the authors try cell-specific depletion of cv-c and examined the consequence on gonad development?

Response: cv-c mutants are embryonic lethal because of Cv-c’s widespread requirement on various embryonic tissues during development. Induction of FRT clones in the embryonic testis mesoderm was unsuccessful because of the low number of divisions during embryogenesis. We also tried to knock down cv-c expression with 3 different RNAi lines. Unfortunately, overexpression of these RNAi with different testis Gal4 drivers did not decrease cv-c mRNA levels significantly in the mesoderm or in other tissues where cv-c is expressed. Despite these experiments unsatisfactory outcome, our finding that cv-c is expressed in the testis mesoderm cells, and the fact that we can rescue the testis phenotypes by expressing Cv-c with gonadal mesodermal specific Gal4 lines supports a testis mesoderm requirement of cv-c for its gonadal function.

1. Another major concern is the lack of mechanistic insight of cv-c. For example, how does loss of cv-c result in gonadal dysgenesis? The authors suggested that StART domains regulate via lipid binding. The authors could examine if StART domain function is dependent on lipid-mediated interactions.

Response: We agree with the referee that the molecular characterisation of the StART-mediated GAP-independent Cv-c function we have uncovered in this work is a very interesting finding that should be addressed by future work. However, such biochemical characterisation requires a complex approach to distinguish between the already known StART function regulating the GAP activity shown before (Sotillos Scientific Reports) and the new GAP-independent function we describe in the testes that falls beyond this work.

The central point of this manuscript is the demonstration that both DLC3/Cv-c are involved in male gonad formation, an important conserved function for both of them that had been overlooked by previous publication. Thus, DLC3 should be considered a new gene to be analysed in the future when studying gonadal dysgenesis. A second important point raised by our work is the demonstration that DLC3/Cv-c can perform RhoGAP independent functions, something that had never been described for these proteins.

Not withstanding this, in the revised version, we have added a new supplementary figure (1) related to the StART domain-lipid interaction analysed in-silico. The in-silico model shows that the DLC3-StART domain Ω1-loop structure displays the highest frequency of interaction with the membrane. This loop is conserved in the StART domains of several other STARD proteins and seems to modulate access to the ligand binding cavity. Ω-loops play multiple roles in protein function, often related to ligand binding, stability and folding. In this context, mutations in the proximity of the Ω1-loop, like the ones carried by the patients, may have drastic effects on overall protein stability that could affect the interaction between gonadal precursor cells.

1. Do the cv-c mutants survive to adulthood? If yes, then it would be interesting to know how the adult testis behaves in cv-c mutants. Does it result in sterility?

Response: Unfortunately, all studied cv-c mutants are embryonic lethal.

1. Ensheathment is required for proper germline development and defects in ensheathment can affect soma-germline communication and germline development. Germ cell ensheathment affects the proliferation of germ cells and display defective JAK/STAT signaling. It would be interesting to know if the germ cells in cv-c mutant gonad show the proliferation defect and impaired JAK/STAT signaling.

Response: This is an interesting suggestion. JAK/STAT signalling has a male specific function that could explain why cv-c gonadal defects are male specific. We are going to study how cv-c affects STAT signalling in the male gonad. We are currently preparing stocks combining 10XSTAT::GFP reporter with cv-c mutants and preparing samples for anti-STAT labelling. We will also analyse if embryos lacking STAT activation, activate cv-c expression in the testes.

1. I was also wondering if the authors have examined the number of germ cells in the mutant gonads.

Response: Yes, we have counted the number of germ cells in cv-c mutants and, if anything, there are more. We initially considered that an excess of GC proliferation could be the cause of gonad disruption. However, we have discarded this hypothesis as phospho-histone 3 stainings did not show a significant increase of GC divisions. Moreover, when we blocked cell proliferation in cv-c’ mutant gonads using UAS-p21, the testes phenotype was not rescued. We are unsure what could be responsible for the slight increase of germ cells observed.

1. In addition, I think the quality of the images should be improved.

Response: We have changed the colours used in the confocal images and amplified the relevant regions in all panels. We thank both referees for this suggestion as these changes have improved the figure contrast.

Minor comments:

1. cv-c mRNA in Figure 2 panels (Fig. 2D) should be in italics.

Response: We have changed it.

1. There is no scale bar in Figure panels. In addition, there is no scale bar in the zoomed images in Figure 2. Scale bars should be consistently put in the all the Figures, in particular on the first panels of the Figures.

Response: We have added scale bars to all panels.

1. In the line 677, the manuscript says "arrowhead". There are no arrowheads but the arrows.

Response: Corrected

1. Please be consistent with the labels in Figure panels: Vasa is shown in capital while Eya is not.

Response: Corrected

1. Please be consistent with the labeling of the Figure panels: Figure 3A vs Figure 4a.

Response: Corrected

1. What does the asterisk signify in Figure 2? There is no mention of asterisk in the Figure 2 legend.

Response: The meaning of the asterisk was explained in the figure legend.

1. There is no grey channel (sagittal view) for the panels Figure 3I and J.

Response: We have already included sagittal views in the figure.

1. Please be thorough in labeling the genotypes in Figures. For instance, Figure 4c depict the % of normal testis in cv-c delta StART. However, the correct genotype is twi>Cv-c StART. In addition, in Figure 4c graph, cv-c mut should be cv-cGAPmut.
2. Please be consistent with the depiction of the "START" domain of the protein throughout the manuscript. In figure 4c for instance, it is "START" in the graph while in the figure panel 4i, it is StART.
3. In Figure 4b, it is written DLC3-GA. Did the authors mean DLC3-S993N?
4. In line 723, it should be anti-beta catenin.

Response: As suggested, we have unified figure labelling.

1. The authors have shown two images to suggest that cv-c mutant gonad depict the germ cell blebbing (Figure 3I and J). I think it would be much better to put up a graph showing the number or percentage of cv-c mutant gonads displaying the germ cell blebbing than putting two images with the same information.

Response: We have already done the quantification and added the data as a graph in figure (3J).

1. The previous comment is also true for Figure 6H and I. In both the panels, the authors wish to show discontinuous ECM marked by Perlecan expression in cv-c mutant gonads. I think it would be better to display a score of the number of mutant gonads depicting the discontinuous ECM.

Response: We are repeating stainings to quantify Perlecan disruption in cv-c mutants and we will display the results as a graph in figure 6.

Author Response

Reviewer #1 (Public Review):

The layered costs and benefits of translational redundancy by Raval et al. aim to investigate the impact of gene copy number redundancy on E. coli fitness, using growth rate in different media as the primary fitness readout. Genes for most tRNAs and the three ribosomal RNAs are present in multiple copies on the E. coli chromosome. The authors ask how alterations in the gene copy number affect the growth rate of E. coli in growth media that support different rates of growth for the wild type.

While it was shown before that mutants with reduced numbers of ribosomal RNA operons grow at reduced rates in rich medium (LB), this study extends these findings and reaches some important conclusions:

1) In a poor medium (supporting slow growth rates), the mutants with fewer rRNA operons actually grow faster than the wild type, showing that redundancy comes at a cost.

2) The same is true for mutants with reduced gene copy number of certain tRNAs and correlates with slower rates of protein synthesis in these mutants.

3) That rRNA operon gene copy number is more decisive for growth rate than any tRNA gene copy number (>1).

In addition, measurements of strains with deletions of genes encoding tRNA-modification enzymes that affect tRNA specificity are included. While interesting, no unifying conclusion could be reached on the impact of these mutations on growth rate.

Thank you for this clear summary of our work.

The well-known "growth law" relationships between growth rate and macromolecular composition (RNA/protein ratio, for example) specifically concern steady-state growth rates. It is concerning that all growth rates in this work were measured on cultures that were only back-diluted 1:100 from overnight LB precultures. That only allows 6-7 doubling times before the preculture OD is reached again. The exponential part of growth would end before that, allowing perhaps only 3-4 generations of growth in the new medium before the growth rate was measured. Thus, the cultures were not in balanced growth ("steady state") when the measurements were made, rather they were presumably in various states of adapting to altered nutrient availability.

A detailed connection with exact growth rate laws indeed requires growth rate measurement in steady-state. Hence, we refrained from making such a connection in this manuscript, though it would be an interesting future avenue to explore. Our main goal here was to ask how E. coli growth rate is affected by external nutrient availability and internal translation components. For this, the key comparisons involve the WT vs. gene deletion mutations, and rich vs. poor growth media. For any given comparison, strains were tested under identical conditions and experimental protocols, and hence we can address our main questions without the need to obtain steady-state growth. As an aside, we note that the nutrient fluctuations inherent in such experiments may also be more relevant than steady-state growth for natural bacterial populations.

As noted by the reviewer, we measured fitness only in a relatively narrow growth regime of several doublings; but we do capture exponential growth by focusing on the early data points (representing the exponential phase) for our growth rate calculations. We have now explicitly mentioned this in the methods section “Measuring growth parameters”.

A second concern is the use of the term "tRNA expression levels" in the text in Figure 4. I believe the YAMAT-seq method reports on the fractional contribution of a given tRNA to the total tRNA pool. Thus, since the total tRNA pool is larger in fast-growing cells than in slow-growing cells, a given tRNA may be present at a higher absolute concentration in the fast than in the slow-growing cells but will be reported as "higher in poor" in figure 4, if the given tRNA constitutes a smaller fraction of the total tRNA pool in rich than in poor medium. For this reason, the conclusions regarding the effect of growth medium quality on tRNA levels are not justified.

Thank you for this important point. We agree that our phrasing was incorrect, and we have modified the relevant text and figures accordingly. The fractional contribution of a given tRNA isotype to the total tRNA pool is still useful to compare, and is justified as now rephrased.

Reviewer #2 (Public Review):

Raval et al. by creating a series of deletion mutants of tRNAs, rRNAs, and tRNA modifying enzymes, have shown the importance of gene copy number redundancy in rich media. Moreover, they successfully showed that having too many tRNAs in poor media can be harmful (for a subset of the examined tRNAs). Below, please find my comments regarding some of the methodologies, conclusions, and controls needed to stratify this manuscript's findings.

Figure 2 presents Rrel as a relative measurement (GRmut/GRwt). Therefore, I'm confused as to how Rrel can be negative, as shown in supplemental file 3 (statistics).

We apologize for the confusion. Supplemental file 3 shows details of the statistical analysis (not raw data), and we included the effect size here (mean difference between the WT and the mutant relative growth rate) along with statistical significance. Thus, if the rel R of a given mutant is 1.1, the mean difference would be (1–1.1) = –0.1, meaning that it is performing 10% better than the WT.

The “raw” relative growth rates are provided in source data files (labeled figure-wise), and there are no negative values there, as expected.

We have now explicitly (and separately) referenced the source and statistics data files in the data analysis section in the methods, and in each figure legend. We hope this avoids confusion and makes it easier for readers to find the correct file.

Does Figure 3 show the mean of 4 biological replicates or technical replicates? It should be stated clearly in the legend of figure 3.

All replicates are biological replicates until unless stated otherwise. This is now stated in the methods (lines 185-187), and in the figure legends.

Do all strains (datapoint on figure 3 left panel) significantly perform better than the WT in nutrient downshift? Looking at supplemental file 3 I see this is not the case. Please mark the statistically significant points. I suggest giving each set a different symbol/shape and coloring the significant ones in red.

We had considered indicating statistical significance in the plot, but decided not to do so because it was difficult to show the many potentially useful layers of information without cluttering the plot. One other practical difficulty was that each point in the figure represents two values: one from the upshift (Y axis) and one from the downshift (X axis). For some mutants the fitness difference was significant in only one direction, so it was not straightforward to indicate significance. Further, our main goal here was to show where strains from different deletion Sets (Figure 1) fall in this plot (i.e. which quadrant they occupy), and so we wanted to ensure that points were easily distinguished by Set. In the text we do not include statistically non-significant points in the summary of observed patterns, and refer readers to information on statistical significance provided in the supplemental file.

Another issue is that in the statistics of figure 2 (in supplemental file 3), positive values reflect cases where the mutant performs poorly compared to the WT, while in figure 3 the negative values indicate this. Such discrepancy is not very clear. And again, how can Rrel be negative?

As noted in response to an earlier comment, Rrel values (given in source data files) are not negative, but effect sizes (given in supplemental file with statistics) may be negative or positive since they show differences in the relative growth rate of WT and mutant. We agree that the discrepancy between the calculation of mean difference for Figs 2 and 3 was confusing. We have now fixed this: in both cases, negative mean difference values now indicate that the mutant performs better.

Both axes say glycerol. What about galactose?

The typo has been corrected.

Lines 414-419: The authors state that "all but one had a growth rate that was comparable to WT (16 strains) or higher than WT (10 strains) after transitioning from rich to poor media (i.e. during a nutrient downshift, note data distribution along the x-axis in Fig 3; Supplementary file 3). In contrast, after a nutrient upshift, 11 strains showed significantly slower growth in one or both pairs of media, and only 2 showed significantly faster growth than WT (note data distribution along the y-axis in Fig 3; Supplementary file 3)".

Looking at the Rrel values when transitioning from TB to Glycerol and vice versa suggests no direction in the effect of reducing redundancy. During downshift, four strains perform better, and three strains perform worse than the WT. During upshift, four stains perform better, and six strains perform worse. Only during downshift and upshift from TB to Gal and vice versa give a strong signal.

The authors should write it clearly in the text because the effect is specific to that transition/conditions and not of general meaning is written in the text (e.g., transition from every rich to every poor media and vice versa). I am convinced that the authors see an actual effect when downshifting or upshifting from TB to galactose and vice versa. In that case, the conclusion is that redundancy is good or bad depending on the conditions one used and not as a general theme.

Also, this is true just for some tRNAs, so I don't think the conclusion is general regarding the question of redundancy.

The fitness impacts of altered redundancy are best explained by a combination of multiple factors (in addition to nutrient availability): the number of tRNA genes deleted, number of tRNA gene copies remaining as a backup, availability of wobble or ME as backup, and codon usage. Thus, any of these variables alone would provide only partial explanation for the observed fitness effects of all strains.

In many tRNA deletion strains – especially single gene deletions – redundancy was not significantly lowered by the deletion, as we explain in the results section. These strains were therefore not expected to show major fitness impacts or follow strong nutrient dependent trends, and this is what we observe.

The same is true for nutrient upshift-downshift experiments, where a vast majority of strains were not expected to show a specific pattern because they do not show significant fitness impacts in general, nor do they show a strong correlation in relative fitness impacts vs. growth rate (Figure 1d). In addition, in these experiments the difference between the two media also matters. For example, comparing the maximum WT growth rate, M9 Gal is poorer than M9 Glycerol. Therefore, shifts between TB-Gal are nutritionally more drastic than TB-Gly shifts, and one would expect a larger fitness impact in the former (for strains with significantly altered redundancy). Hence, despite differences across media pairs, our broader conclusions about the impact of redundancy are generalizable as long as redundancy and nutrients are both substantially altered, e.g. due to deletion of 3 tRNA genes, deletion of tRNA+ME, or deletion of multiple rRNA operons.

Figures are indicated differently along the text. Sometimes they are written "figure X", sometimes FigX. Referring to the supplemental figures are also not consistent.

We have now corrected this.

Line 443-444: "In fact, 10 tRNAs were significantly upregulated in the poor medium relative to the rich medium".

This result contradicts the author's hypothesis. If redundancy is bad in poor media because the cells have more tRNAs than they need, the tRNAs level will be downregulated, not upregulated. How do the authors explain this?

This statement referred to the WT strain, and was meant to highlight that (as noted by the reviewer) some tRNAs appear to be upregulated in poor medium, which is counterintuitive. However, as noted by reviewer 1 (see their comment on the interpretation of YAMAT-seq data), we can only infer the relative contribution of each tRNA isotype to the total tRNA pool (rather than absolute up- or down- regulation). Thus, we have removed this specific sentence, and instead we focus on the mismatch between the media-dependent changes in the composition of the tRNA pool and the fitness effects of different tRNA isotypes (lines 475-482).

Line 445-447: "In contrast (and as expected), all tested tRNA deletion strains had lower expression of focal tRNA isotypes in the rich medium (Fig 4B, left panel), showing that the backup gene copies are not upregulated sufficiently to compensate for the loss of deleted tRNAs". It is great that the authors validated the expression in their strains. However, for accuracy, please indicate that it was done in four strains to avoid the impression that they did it in all the strains.

We have now reworded this sentence to remind readers that we measured 4 tRNA deletion strains in this experiment.

Finally, across the manuscript, the authors reveal that deleting some tRNAs or modifying enzymes can be deleterious in rich media or advantageous in poor media. However, I think this result and the conclusions derived from it could be more convincing if the authors would show in a subset of their strains that expressing the deleted tRNAs or modifying enzymes from a plasmid can rescue the phenotype.

Thank you for this suggestion. For a small subset of strains, we now include data showing that complementation from a plasmid indeed rescues the deletion phenotype (Fig 2 – Fig supplement 7).

Reviewer #3 (Public Review):

In this manuscript, Raval et al. investigated the cost and benefit of maintaining seemingly redundant components of the translation machinery in the E. coli genome. They used systematic deletion of different components of the translation machinery including tRNA genes, tRNA modification enzymes, and ribosomal RNA genes to create a collection of mutant strains with reduced redundancy. Then they measured the effect of the reduced redundancy on cellular fitness by measuring the growth rate of each mutant strain in different growth conditions.

This manuscript beautifully shows how maintaining multiple copies of translation machinery genes such as tRNA or ribosomal RNA is beneficial in a nutrient-rich environment, while it is costly in nutrient-poor environments. Similarly, they show how maintaining parallel pathways such as non-target tRNA which directly decodes a codon versus target tRNA plus tRNA modifying enzymes which enable wobble interactions between a tRNA and a codon have a similar effect in terms of cost and benefit.

Further, the authors show the mechanisms that contribute to the increased or reduced fitness following a reduction in gene copy number by measuring tRNA abundance and translation capacity. This enables them to show how on one hand reduced copy numbers of tRNA genes result in lower tRNA abundance in rich growth media, however in nutrient-limiting media higher copy number leads to increased expression cost which does not lead to an increased translation rate.

Overall, this work beautifully demonstrates the cost and benefits of the seemingly redundant translation machinery components in E. coli.

Thank you for the clear summary and encouraging comments.

However, in my opinion, this work’s conclusion should be that the seeming redundancy of the translation machinery is not redundant after all. As mentioned by the authors, it is known that tRNA gene copy number is associated with tRNA abundance (Dong et al. 1996, doi: 10.1006/jmbi.1996.0428), this effect is also nicely demonstrated by the authors in the section titled “Gene regulation cannot compensate for loss of tRNA gene copies”. Moreover, this work demonstrates how the loss of the seeming redundancy is deleterious in a nutrient-rich environment. Therefore, I believe the experiments presented in this work together with previous works should lead to the conclusion that the multiple gene copies and parallel tRNA decoding pathways are not redundant but rather essential for fast growth in rich environments.

The point is well taken. However, as described in the introduction, here we focus on functional redundancy at the cellular level, where there are multiple ways of achieving the same translation rate. Hence we say that translation components are redundant at this level of analysis. One of the key conclusions from our work is that such redundancy is context-dependent, i.e. it is essential when rapid growth is possible, but is costly and dispensable otherwise. Therefore, we show that the definition of redundancy itself changes with environmental conditions.

The following analogy may help convey this. There may be many ways to reach a flight on an airport: multiple entrances, multiple check-in and security check counters, multiple boarding gates, etc. On a deserted airport these may seem redundant and even costly to maintain. On the other hand, they have a utility when traffic is high. Hence even though from a purely architectural perspective the multiple routes are redundant, from a utilitarian perspective it depends on the flux of passengers.

Authors’ response (5 November 2022)

GENERAL ASSESSMENT

Piezo1 and Piezo2 are stretch-gated ion channels that are critically important in a wide range of physiological processes, including vascular development, touch sensation and wound repair. These remarkably large molecules span the plasma membrane almost 40 times. Cryo-EM and reconstitution experiments have shown that Piezos adopt a cup-like structure and, by doing so, curve the local membrane in which they are embedded. Importantly, membrane tension is a key mediator of Piezo function and gating, an idea well-supported several independent studies. Cells have varied three-dimensional shapes and are dynamic assemblies surrounded by plasma membranes with complex topologies and biochemical landscapes. How these microenvironments influence mechanosensation and Piezo function are unknown.

The current preprint by Zheng Shi and colleagues asks how the shape of the membrane influences Piezo location. The authors use creative approach involving methods to distort the plasma membrane by generating “blebs” and artificial “filopodia”. Overall, the work convincingly shows that the curvature of the lipid environment influences Piezo localization. Specifically, they show that Piezo1 molecules are excluded from filopodia and other highly curved membranes. These experiments are well controlled and the results fully consistent with previous structural and biochemical work. Furthermore, the work explores the hypothesis that a chemical modulator of Piezo1 channels called Yoda1 functions by “flattening” the channels, a movement previously proposed to be linked to mechanical gating. Consistent with this model, the authors show that Yoda1 application is sufficient to allow Piezo1 channels to enter filopodia. While the flattening model is provocative hypothesis, hard evidence awaits structural verification.

Overall, the preprint by Shi and colleagues will be of interest to scientists studying how mechanical forces are detected at the molecular level. The work introduces important concepts regarding how the shape of cellular membranes affects the movement and function of proteins within it. The technical advance for changing the shape of a plasma membrane is of note. 

We thank the reviewers for the accurate summary and positive assessments of our manuscript. We address each of the concerns below.

RECOMMENDATIONS

Revisions essential for endorsement:

As is evident from the comments below, our endorsement of the study is not dependent on additional experiments. However, we feel more experimental clarification is needed, that providing clearer images would be helpful, and, most importantly, we would like alternative conclusions and caveats to be mentioned.

1. Can the authors comment on the link between the conclusions that (1) the presence of filopodia prohibits Piezo1 localization (Fig 1) and (2) Piezo1 expression prohibits the formation of filopodia (Fig 3). As it stands, it is hard to understand if there is a cause and effect relationship here or if these are separate, unrelated observations? We recommend revising the discussion to clarify.

We now clarify the link between Piezo1’s curvature sensing (depletion from filopodia) and its inhibition effect on filopodia formation before presenting the current Fig. 5: “Curvature sensing proteins often have a modulating effect on membrane geometry. For example, N-BAR proteins, which strongly enrich to positive membrane curvature, can mechanically promote endocytosis by making it easier to form membrane invaginations (Shi and Baumgart, 2015; Sorre et al., 2012). Thus, we hypothesize that Piezo1, which strongly depletes from negative membrane curvature (Fig. 1, Fig. 2), can have an inhibitory effect on the formation of membrane protrusions such as filopodia.”

2. When comparing the images of Fig. 2A, B to those of Fig. 2C, D, it appears that bleb formation induces a drastic enrichment of Piezo1 in the bleb membrane. Is this due to low membrane tension in the bleb? If this is the case, it indicates that the level of membrane tension has a prominent role in determining the localization of Piezo1.

We apologize for this confusion due to our poor wording and figure presentation in the manuscript. By “Piezo1 clearly locates to bleb membranes” we didn’t mean to indicate that Piezo1 is enriched on bleb membranes as compared to the cell body. Rather, we meant to emphasize Piezo1’s localization to the *membrane* of the blebs rather than in the cytosolic space.

Cells in 2C, 2D are different from that in 2A and 2B and were presented with different image contrasts. We now include the images of the full cell for Fig. 2C and 2D as the current Figure S8. To focus on the equator of the bleb, the cell body was out of focus. However, there is no indication that Piezo1 density is significantly different between the bleb membrane and the intact parts of the plasma membrane.

We changed the main text to: “Similar to previous reports (Cox et al., 2016), bleb membranes clearly contain Piezo1 signal, but not significantly enriched relative to the cell body (Fig. 2C, 2D; Fig. S8).”

In line with this, it appears more Piezo1 proteins are localized in less tensed tethers. Thus, might your observations be equally consistent with tension rather than curvature as a key regulator of Piezo1 localization? We recommend adding this to your discussion.

We now explain the deconvolution between tension and curvature effects in detail. We also performed additional experiments to quantify the membrane tension in cells and blebs (current Fig. S9).

In the Results section, we add: “Tethers are typically imaged > 1 min after pulling, whereas membrane tension equilibrates within 1 s across cellular scale free membranes (e.g., bleb, tether) (Shi et al., 2018). Therefore, the sorting of Piezo1 within individual tension-equilibrated tether-bleb systems (Fig. 2C – 2G) suggests that membrane curvature can directly modulate Piezo1 distribution beyond potential confounding tension effects.”

In the Discussion section, we add: “In addition to membrane curvature, tension in the membrane may affect the subcellular distribution of Piezo1 (Dumitru et al., 2021). Particularly, membrane tension can activate the channel and potentially change Piezo1’s nano-geometries. This tension effect is unlikely to play a significant role in our interpretation of the curvature sorting of Piezo1 (Fig .2): (1) HeLa cell membrane tension as probed by short tethers (Fig. S9F; 45 ± 29 pN/ µm on blebs and 270 ± 29 pN/ µm on cells, with the highest recorded tension at 426 pN/ µm) are significantly lower than the activation tension for Piezo1 (> 1000 pN/µm (Cox et al., 2016; Lewis and Grandl, 2015; Shi et al., 2018; Syeda et al., 2016)). (2) With more activated (and potentially flatten) channels under high membrane tension, one would expect a higher density of Piezo1 on tethers pulled from tenser blebs. This is the opposite to our observations in Fig. 2C - 2G, where Piezo1 density on tethers was found to decrease with the absolute curvature, thus tension (eq. S6), of membrane tethers.”

3. Given the intrinsically curved structure of Piezo1, it is difficult to understand the model’s prediction that curved Piezo1 is not enriched in 25-75 nm invaginations. Where will Piezo1 normally reside in the plasma membrane? It would be helpful if this could be discussed.

The spontaneous curvature from our model _C_0 (_C_0-1 = 83 ± 17 nm, the value is updated after refitting to more data points collected for Fig. 2G) represents a balance between the intrinsic curvature of Piezo1 trimers (0.04 ~ 0.2 nm-1 as suggested by CryoEM studies(Haselwandter et al., 2022; Lin et al., 2019; Yang et al., 2022)) and that of the associated membrane (0 nm-1, assuming lipid bilayers alone do not have an intrinsic curvature). We now refer to _C_0 as the “spontaneous curvature of the Piezo1-membrane complex” throughout the manuscript, rather than the “spontaneous curvature of Piezo1”.

Our model, when extrapolated to membrane invaginations, predicts a weak enrichment of Piezo1 on ~100 nm invaginations (peak at 83 nm), but a depletion of Piezo1 on more highly curved invaginations. This is simply because it would be energetically costly to fit a protein-membrane complex to a curvature that is different from what the complex prefers (in the case of 25-75 nm membrane invaginations, the membrane curvature would be too high for the Piezo1-memrbane complex).

However, it is worth pointing out that Piezo1-membrane complex may not present the same spontaneous curvature on positively and negatively curved membranes. More importantly, we do not yet have direct evidence to show that this depletion indeed happens in the exact range of invagination curvature we predicted. We now acknowledge this limitation in the Discussion section: “However, it is worth noting that we assumed a zero spontaneous curvature for membranes associated with Piezo1 and that the spontaneous curvature of Piezo1-membrane complex is independent of the shape of surrounding membranes. These assumptions may no longer hold when studying Piezo1 in highly curved invaginations or liposomes (Lin et al., 2019).”

We also took this opportunity to verify the key prediction from the extrapolated model - that Piezo1 would enrich towards ~ 100 nm radius cell membrane invaginations. To achieve this, we utilized a recent development in nanotechnology, pioneered by Wenting Zhao and Bianxiao Cui’s labs (Lou et al., 2019; Zhao et al., 2017). An illustration of the experimental design and detailed findings are summarized in the current Fig. 3 and briefly discussed below.

In collaboration with Wenting Zhao’s lab, we cultured cells on precisely engineered nanobars with curved ends and flat central regions. For a labelled membrane protein of interest, the end-to-center fluorescence ratio would report the protein’s curvature sorting ability. We find that Piezo1 enriches to the curved ends of nanobars, whereas membrane marker signals are homogeneous across the entire nanobar (Fig. 3). The finding achieved strong statistical significance via hundreds of repeats on nanobars of the exact same geometry, a major technical strength of our chosen system. Furthermore, the enrichment of Piezo1 was observed on nanobars with 3 different curvatures (corresponding to diffraction-limited radii between 100 to 200 nm) and qualitatively agrees with our model (current Fig. S10). While further investigations on a wider range of membrane curvature are required to fully map out the sorting of Piezo1 on membrane invaginations, our data in the current Fig. 3 clearly verifies the prediction that membrane curvature can lead to enrichment of Piezo1 on cellular invaginations.  

We now refer to this new finding in the Abstract, along with the previously observed depletion of Piezo1 on filopodia. We present a detailed description of the experiment and associated findings in the Results and the Method sections.

4. It is currently unknown whether and how long Yoda1 might keep Piezo1 in a flattened state. Given that Yoda1 is highly hydrophobic, it might affect membrane properties instead of the curvature of Piezo1. These caveats should be discussed.

We thank the reviewers for pointing out the potential effect of Yoda1. We did additional experiments to confirm that on Piezo1-KO cells, Yoda1 molecules alone do not significantly alter the formation of filopodia, in contrast to observations in WT cells. This data suggests Yoda1 (at the concentration we use) is unlikely to significantly alter the mechanical properties of the plasma membrane. The data is now presented as Fig. 5E in the updated manuscript. We added: “In Piezo1 knockout (Piezo1-KO) cells, adding Yoda1 to the culture medium does not significantly change the number of filopodia (Fig. 5E), suggesting the agonist does not directly regulate filopodia formation without acting on Piezo1.”

5. The authors state that “Yoda1 leads to a Ca2+ independent increase of Piezo1 on tethers”. It has not been determined yet that Yoda1 leads to Piezo1 flattening (or even opening). In Electrophysiology experiments, unless there is pressure applied, Yoda1 does not lead to substantial currents. Therefore, the cartoon of Yoda1 flattening Piezo1(3H) is misleading. We recommend revising this. So far, the best experimental evidence on flattening is via purified channels reconstituted in various sizes of liposomes. However, it is plausible that the flattened shape is closed or open inactivated. Because most of the claims of this paper depend on the curved vs flattened shape of Piezo1, the authors should address these caveats carefully.

We thank the reviewers for pointing out the limitations in our current understanding of Yoda1. We agree that our data do not directly show the flattening of Piezo1 by Yoda1, rather it is consistent with the flattening hypotheses. We lowered the tone of our conclusion to Fig. 4 to: “Our study suggests this conformational change of Piezo1 may also happen in live cells (Fig. 4H).” We also added arrows in Fig. 4H to suggest that membrane tension helps the proposed flattening of Piezo1 by Yoda1.

We think our experiment may also provide new insights on the action of Yoda1: First, we note that only a small fraction of filopodia responded to Yoda1, and pre-stressing of the cell membrane was required to amplify the Yoda1 effect (current Fig. 4E). This observation is consistent with the reviewers’ notion that membrane tension is likely required to flatten Piezo1, even in the presence of Yoda1. Secondly, highly curved liposome or detergents can confine the shape of Piezo1 trimers. Therefore, the inability to observe Yoda1-induced flattening of Piezo1 in small liposomes is not necessarily in contradiction with our observation in the mostly flat cell membranes.

We add to the Discussion section: “Yoda1 induced flattening of Piezo1 has not been directly observed via CryoEM. Our results (Fig. 4) point to two challenges in determining this potential structural change: (1) Yoda1 induced changes in Piezo1 sorting is greatly amplified after pre-stretching the membrane (Fig. 4E), pointing to the possibility that a significant tension in the membrane is required for the flattening of Yoda1-bound Piezo1. (2) Piezo1 is often incorporated in small (< 20 nm radius) liposomes for CryoEM studies. The shape of liposomes can confine the nano-geometry of Piezo1 (Lin et al., 2019; Yang et al., 2022), rendering it significantly more challenging to respond to potential Yoda1 effects. This potential effect of membrane curvature on the activation of Piezo1 would be an interesting direction for future studies.”

6. Page 9: "Our study shows this conformational change of Piezo1 in live cells (Fig. 3H)." We recommend that this claim be removed as it seems too strong for the provided data.

We changed the sentence to: “Our study suggests this conformational change of Piezo1 may also happen in live cells (Fig. 4H).”

Additional suggestions for the authors to consider:

1. Based on the calculated spontaneous curvature of Piezo1-membrane C0 of 87 nm, is it possible to derive the curvature of Piezo1 protein itself and the associated membrane footprint? This would be a nice addition.

It is possible to do such an estimation, however, many (unverified) assumptions must be made, in addition to the ones already in our model. First, we need to assume a size of the Piezo1 trimers and of the Piezo1-membrane complex. If we assume Piezo1 trimers are ~170 nm2 in the plane of lipid bilayers (based on estimates from PDB) and that the complex takes on the shape of a 10 -20 nm radius half-sphere. Effectively, Piezo1 occupies an area fraction of 6.7%~27% in the Piezo1-membrane complex. Next, we assume that the membrane and the Piezo1 trimer have the same bending rigidity. Finally, we assume that the membrane itself does not have an intrinsic curvature.

With those assumptions, the intrinsic curvature of Piezo1 trimers (_C_p) would relate to the spontaneous curvature of membrane-Piezo1 complex (_C_0) following: _C_p-1 = _C_0-1 * (6.7%~27%). Knowing _C_0-1 = 83 ± 17 nm, we get _C_p-1 = 5.6 nm ~ 22.4 nm.

2. It is hard to see the filopodia and their localization in the figures. It would be better for readers and more convincing if clearer/higher resolution example images could be provided.

We now provide high resolution figures.

3. Can the authors better explain how the calculations done in panel 1C and S3D are done and their importance?

Each fluorescence trace along the drawn yellow line was normalized to the mean intensity on the corresponding flat cell body, so that the average fluorescence of the cell body has a y-axis value of 1. We think the intensity traces are important because image contrast can be adjusted, therefore Fig. 1A alone would not convincingly show that there are no Piezo1 on filopodia.

4. In Figure 2E, are these data from hPiezo1 or mPiezo1? In other cases, hPiezo1 is specified, this this may be a typo?

Corrected.

5. Figure 3 F&G: We assume these cells are the same in all panels, just visualized with either mCherry or eGFP in each condition. Accordingly, we would have expected more swelling in hypotonic conditions, and wonder if further evaluation may resolve this apparent discrepancy? If not, please provide more clarification.

This is a good point. Indeed, we do observe a significant swelling of the cell right after the hypotonic shock.

However, this effect is expected to be transient (volume of the cell would recover after ~ 1 min), see Figure. 1C here: https://www.pnas.org/doi/10.1073/pnas.2103228118. Our images in Fig. 3F and 3G were taken ~10 min after the hypotonic shock.

6. On a lighter note, we’d recommend not using in cellulo.

We changed in cellulo to “in live cells”

Reference List

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Dumitru, A.C., Stommen, A., Koehler, M., Cloos, A., Yang, J., Leclercqz, A., Tyteca, D., and Alsteens, D. (2021). Probing PIEZO1 Localization upon Activation Using High-Resolution Atomic Force and Confocal Microscopy. Nano Letters 21, 4950-4958.

Haselwandter, C.A., MacKinnon, R., Guo, Y., and Fu, Z. (2022). Quantitative prediction and measurement of Piezo's membrane footprint. bioRxiv

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(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Meillassoux claims that, because cognitive science is made of atoms, that makes it suspect -- so we need to use philosophy. That is a bad claim. Philosophy is also made of atoms too. Cognitive science solves how cognition works. It may not answer "why cognition works", but maybe that's a trick question that only philosophy can ask, but nobody can answer.

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

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Reply to the reviewers

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

The rapid syncytial nuclear cycles that occur during the first ~2.5 hours of Drosophila embryogenesis and give rise to the blastoderm are supported by large amounts of maternally deposited histone proteins which are stored in the egg cytoplasm for deposition into replicating DNA during each round of S phase. Although the H2A/H2B storage chaperone Jabba was identified by Michael Welte's lab several years ago, maternal H3/H4 storage chaperones have not been identified. Tirgar et al provide evidence that the Drosophila NASP protein provides histone H3 and H4 storage function during these earliest stages of Drosophila embryogenesis. The data include genetic analyses that NASP function is required maternally, but not zygotically, and molecular analyses that NASP binds H3 and that H3 and H4 levels are reduced in the embryo and late-stage oocytes in the absence of NASP. These data are convincing and support the conclusion that NASP is a maternally acting H3/H4 storage chaperone needed in the early embryo.

Two additional lines of investigation would strengthen this conclusion and perhaps increase the impact and appeal of the manuscript.

The first is a microscopic analysis of the nuclear division cycles in eggs derived from NASP mutant mothers. The authors report DAPI staining and assessment of nuclear cycles, but do not show these data. In fact, the two embryos shown in Figure 4B do not look like DAPI stained embryos-there are no nuclei apparent in the images. Loss of maternal histone causes defects in chromosome morphology that result in characteristic defects such as lagging chromosomes and the failure of sister chromatid segregation leading to fused daughter nuclei (see PMID: 11157774 for an example). These defects should not be difficult to detect via DNA staining or even using fluorescently labeled H2 type histones. Characterizing such defects would lend support to the hypothesis and I think is important for this paper.

We thank the reviewer for their constructive review and feedback. We have switched to Propidium Iodide (PI) staining to increase the signal-to-noise for DNA staining in early embryos. Given the improved signal we see with PI over DAPI, we will be able to provide both improved images of nuclear staining and assay for defects in chromosome morphology as suggested. We will include this data in the revised version of the manuscript. Second, determining the location of NASP in the early embryo might provide further insight into the mechanism of storage. i.e. is NASP located in the cytoplasm rather than the nucleus, perhaps in association with lipid droplets like Jabba? Do the antibodies the authors developed work in IF experiments to ask this question? At the moment what is shown is that NASP is present in 0-2 hour embryos via western blot analysis, supporting the conclusion that it functions in the early embryo as a storage chaperone. This analysis would be nice to have but is not essential in my view.

We have tried to use our antibody to monitor the localization of NASP in the early embryo. Unfortunately, the staining has yet to work. We will continue to alter fixation and permeabilization conditions in the early embryo with the goal of including this data in the revised manuscript. We have, however, been able to monitor NASP localization in Drosophila S2 cultured cells with our antibody. If we are unable to get the antibody staining to work in embryos, we will include the NASP localization data in S2 cells in combination with EdU labeling to mark cells in S phase.

Small points: Is NASP really a maternal effect "lethal"? Some of the eggs do hatch, and so some develop to stages where maternal histones are no longer necessary and zygotic production takes over (i.e. cycle 15). Perhaps consider the language used here.

We see the reviewers point with respect to the term ‘lethal’. We do see a very small fraction of progeny laid by NASPmutant mothers make it to adulthood, although they die shortly after hatching. We’ve removed the term ‘lethal’ and refer to NASP solely as a maternal effect gene. On this point, do NASP mutant females lay the same number of eggs as wild type? i.e. is there a requirement for oogenesis/egg production (other than depositing H3/H4 into the egg), or just for the early zygotic cycles?

We have noticed that NASP mutant mothers have lower fecundity. We have included this data in the revised manuscript as Supplemental Figure 2A.

The first paragraph of the results is redundant with much of the introduction, which I think could do a better job at describing in more detail the syncytial cycles and the special needs they have for histone storage and chaperone function versus the post-blastoderm embryonic cycles and the rest of development. i.e. make a better distinction between the first two hours of embryogenesis versus the rest of embryogenesis, and the when the switch from maternal to zygotic control of development and histone production occurs (cycle 15 at 3-4 hours AED).

We appreciate the reviewer for this suggestion. The manuscript has been edited to be less redundant and include details of embryogenesis as suggested. CROSS-CONSULTATION COMMENTS Seems like all reviewers are in general agreement, particularly about providing additional data regarding chromosome/nuclear behavior in the NASP mutants and NASP localization in the early embryo to increase impact of the study. While rescue of the NASP mutant phenotype with a transgene would be nice, as suggested by referee #2, I don't think it's essential given the genetic approaches employed.

Reviewer #1 (Significance (Required)):

see above

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

Tirgar et al. report on a functional characterization of the Drosophila homolog of the histone H3/H4 chaperone NASP. They generated a loss of function allele of NASP by CRISPR/Cas9, which induces a partial maternal effect embryo lethal phenotype. Using quantitative mass spectrometry, they demonstrate that NASP stabilizes reservoirs of H3 and H4 in the early embryo. The manuscript is very clear and confirms the functional importance of maternal NASP for the early embryo. Genetic analyses are well conducted (but see my comments below) and the impact of NASP maternal mutant on H3 and H4 stockpiles is convincingly established by both quantitative mass spectrometry and Western-blotting.

Major comments:

• Although the authors used two independent deficiencies of the NASP genetic region to characterize their NASP CRISPR alleles, it is relatively standard in this type of functional analyses to perform rescue experiments using a transgene expressing the WT protein.

We thank the reviewer for this suggestion. As discussed in the cross consultation, we agree that the use of the two different deficiency lines and the NASP1 CRISPR control are clear lines of evidence that the phenotypical data are due to lack of NASP.

• In WB analyses, NASP appears systematically shorter in the NASP[1]/Df genotype compared to WT. Can the authors comment on this?

While we reproducibly see this change in migration, we can only guess as to why this may be. One possible reason is that the NASP1 mutant protein could be missing a post-translational modification. Proteomic data from Krauchunas et al. (Dev Biol. 2012; PMC3441184) shows that NASP has the potential to be regulated by phosphorylation. Therefore, the NASP1 mutant protein could be missing a phosphorylation. Intriguingly, the 6bp insertion is next to a Thr residue that could affect its ability to be phosphorylated (if it is phosphorylated at all). Since we can only offer speculation, we do not feel comfortable adding this to the manuscript.

• The authors do not mention the centromeric histone H3 variant Cid in their analyses. Do they have evidence that it is not affected by loss of maternal NASP?

We thank the reviewer for raising this great point. Our mass spec data reveals that Cid levels stay the same in the absence of NASP in both embryos and stage 14 egg chambers. We have edited Figures 3D and 3E to include Cid. Unfortunately, we did not identify any Cid-specific peptides in our IP-mass spec data.

• The authors could have chosen to explore in more details the phenotypic defects of embryos derived from NASP mutant mothers. Instead, a single abnormal embryo is shown with no cytological details. This is a bit problematic since an earlier study (Zhang et al 2018, cited in the manuscript) actually provided more phenotypic details of embryos from NASP KD mothers.

This issue was also raised by Reviewer 1. We have switched to Propidium Iodide (PI) staining to increase the signal-to-noise for DNA staining in early embryos. Given the improved signal we see with PI over DAPI, we will be able to provide both improved images of nuclear staining and assay for defects in chromosome morphology as suggested. We will include this data in the revised version of the manuscript. - Similarly, the authors could have used their anti-NASP antibody to analyze the distribution of NASP during cleavage divisions. Does it behave like ASF1, for instance, which enters S phase nuclei at each cycle or does it remain in the cytoplasm? These are relatively simple experiments/analyses that could increase the significance of the study.

This point was also raised by Reviewer 1. We have tried to use our antibody to monitor the localization of NASP in the early embryo. Unfortunately, the staining has yet to work. We will continue to alter fixation and permeabilization conditions in the early embryo with the goal of including this data in the revised manuscript. We have, however, been able to monitor NASP localization in Drosophila S2 cultured cells with our antibody. If we are unable to get the antibody staining to work in embryos, we will include the NASP localization data in S2 cells in combination with EdU labeling to mark cells in S phase.

Minor comments:

• line 60: I suggest to introduce Drosophila in the next sentence, where it seems more appropriate (not all embryos develop "extremely rapidly").

We have edited the second sentence to state “the early Drosophila embryo”.

• line 68: the 50% estimation of free histones does not really make sense without defining the embryonic stage.

We have edited the manuscript to state the specific cell cycle in which there has been 50% free histones measured. - line 89: Are the authors specifically referring to Drosophila NASP?

Yes, we have edited the text to include Drosophila in this instance. - lines 99-106: I found this paragraph redundant with the introduction.

We appreciate this suggestion. It was also pointed out by Reviewer 1. We have made changes to the manuscript to address the redundancy.

• line 142: H3-H4

Thank you for noticing this. We have edited the text to include 4.

• line190-191: It seems to me that data of Figure S2C are already included in Fig. 2E.

The data in FigureS2C was performed with virgin females compared to the data in Figure 2E that was generated with non-virgin mothers. This was important to control the genotype of the embryos.

• line 232: it is surprising that the Zhang et al paper (reporting maternal KD of NASP) is only mentioned here. As a reader, I would certainly prefer to have it presented right from the introduction.

We have edited the manuscript to include this reference in the introduction.

• Figure 4B needs a scale bar.

Figure 4B will be replaced with better images of the embryo stained with PI. It will also include images of chromosome morphology/segregation. We will be sure to include scale bars.

• line 302: Mentioning the identity and function of known H3/H4 histone chaperones acting in the early embryo (ASF1, HIRA, CAF-1, ...) could provide perspective to the present study.

Thank you for this suggestion. We have edited the manuscript to include functions of other histone chaperones in the early embryo to provide context.

• line 304: in contrast to this statement, I found quite surprising and interesting that NASP is not absolutely essential for embryo development considering its role. This should be discussed.

In the absence of Jabba alone, upregulation of translation can compensate for the destabilization of H2A, H2B, and H2Av. It is only when translation is inhibited in embryos laid by Jabba mutant mothers that embryos die (Li.Z, et al. Curr Biol 2013). Therefore, it is possible that translation can partially compensate for the degradation of H3 and H4 in the absence of NASP. This may be why a fraction of embryos laid by NASP mutant mothers are able to hatch and why we still detect some H3 in embryos laid by NASP mutant mothers. We have edited the manuscript to discuss this more in depth.

CROSS-CONSULTATION COMMENTS I fully agree with the other reports. The NASP rescue experiment is just a suggestion but is not essential.

Reviewer #2 (Significance (Required)):

This work clarifies the identity and function of Drosophila NASP and clearly demonstrates that NASP is important for the stabilization of maternal stockpiles of H3 and H4 during early embryo development. The conservation of NASP function as a histone H3/H4 chaperone in Drosophila is not really a surprise but the merit of this study is to establish this assumption as a fact. It also establishes useful tools (mutant lines and antibody) for the fly community interested in this topic. The study however does not provide new insights about the dynamic distribution of NASP and the cytological consequences of its maternal depletion on the amplification of cleavage nuclei.

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

Summary: Rapid cell cycles in early embryogenesis is driven from maternally supplied stockpiles of RNA and protein, including histones H3 and H4. This study uses sequence homology searches, biochemical approaches (immunoprecipitation and mass spectrometry) and genetics to identify NASP (CG8223) as the H3-H4 chaperone in Drosophila. Using CRISPR technology, the authors generate a NASP mutant fly line and show using genetic crosses that NASP is a maternal lethal gene. Furthermore the study shows that NASP stabilises H3-H4 during oogenesis and embryogenesis and is required for early embryogenesis.

Major comments: The key conclusions of this study are very convincing. For example, the authors use multiple approaches to show H3-H4 specific interactions with NASP and that H3-H4 protein levels are reduced in mutants (Western analyses, quantitative MS). Analysis is carried out on two individual NASP mutant lines (one deletion that produces no protein, one insertion that still produces some protein acting as a control). All experiments are well controlled, executed and presented. Genetic crossing schemes are well presented and statistical analysis of progeny is clear.

• We thank the reviewer for their positive feedback of our manuscript. Minor comments: In Figure 1B - Authors could indicate amino acids shown or are they full length proteins?

We have edited the methods to include specific amino residues that are included for each structure.

In Figure 2B - Authors could (semi) quantify reduction in NASP1 mutant to show this is a gene dose effect?

We have now included the quantification of the Western blot in Figure 2B.

CROSS-CONSULTATION COMMENTS I agree with the other reports. Although I did not indicate it in my original report, I agree that more in depth analysis of nuclear or chromosomal defects in NASP mutant embryos would enhance the study.

Thank you for this suggestion. We are repeating the DNA staining in embryos and will include this new data in the revised version of the manuscript.

Reviewer #3 (Significance (Required)):

Excess soluble histones can be toxic and must be bound to chaperones. Until this study the chaperone responsible for H3-H4 stabilisation in rapidly cycling cells in Drosophila embryos was not known. Moreover, the NASP homolog had not yet been identified in Drosophila nor had its function been characterised. The findings are of interest to Drosophila researchers, the field of chromatin assembly, as well as those interested in early embryogenesis in animals.

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Reply to the reviewers

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

An exciting development in our knowledge about how the Arp2/3 complex controls the assembly of actin networks has come from the discovery that in addition to forming branched networks, Arp2/3 can nucleate linear filaments when it is activated by WISH/DIP/SPIN90. However, despite some excellent work largely done by the Nolen lab in yeast, many questions remain about how Arp2/3-mediated assembly of branched vs. linear actin filament. This is especially true in the complex environment of cells, were synergy and competition of different actin networks is used to control biological processes. Knowing the biochemical and physical properties of these different Arp2/3 assemblies will be key to figuring out how they work in cells. Here Cao et al. use an elegant microfluidics based single filament assay system to perform a comparative analysis of the stability of linear and branched Arp2/3 networks. They find interesting differences in how they respond to stabilizing and destabilizing factors. The most striking differences happens when force or aging is applied- both cause debranching of branched networks but have little effect on Spin90-Arp2/3 nucleated filaments.

We thank the reviewer for their positive comments.

Major comments:

As a comparative study on the stability of branched vs. linear Arp2/3 nucleated filaments, this manuscript is fairly complete. The key conclusions are well supported by rigorous experiments which can be reproduced by others based on the information provided. However, I am not seeing explicit information on performing biological replicates. This should be included in the manuscript. The use of statistics is largely fine; however I question the use of one statistical test on one figure (see minor comments below).

The revised manuscript is now explicit about biological replicates. We now specify the biological repeats of all our experiments in the figure legends, and we now show the results from new repeats in Fig 4 and Supp Fig S2 (please see also our response to the minor comments below, for more details).

I would not ask for additional experiments at this time. However, there is an analysis that would be important for interpreting the authors' claims- branch/filament length at the time of dissociation or destabilization of Arp2/3. This would help address if there was a physical tipping point for each type of structure that could explain potential differences they see. The authors should already have this data and the time to complete it would be negligible in delaying publication.

If we understand correctly, the “physical tipping point” mentioned by the reviewer would be a threshold force, where the Arp2/3-filament interface would become unstable. This is an interesting idea. Indeed, the applied force scales with the length of the filament (or branch), as well as with the flow velocity. In most of our experiments, however, the force applied to SPIN90-Arp2/3 and to branch junctions was kept constant and below 0.2 pN. This was done by exposing the filaments (or branches) to G-actin at the critical concentration, in order to minimize variations of their lengths. Therefore, by design, dissociation events in these experiments take place at the same length, ruling out the existence of a “tipping point”.

Our data provide another test of the reviewer’s hypothesis, thanks to the experiments where we specifically address the question of the impact of force (Fig 5 and Supp Fig S6), by varying length and flow rate. We found that the stability of SPIN90-Arp2/3 linear filaments was unaffected by force, and that debranching was steadily accelerated by force. In both cases, it thus appears that there is no detectable threshold.

One additional major comment is that the manuscript's title and abstract hint that this paper explores the differences in nucleation of branched vs. linear filaments by Arp2/3. However, the only figure that deals explicitly with nucleation in the paper is Figure 1, which is really just a confirmation that the mammalian proteins used in this study perform similarly to their yeast homologues (Balzer et al, Current Biology 2019). The authors might think about rewording the title/abstract to better reflect that paper really explores the differences in the stability of the two networks

This is a fair point. We have now modified the title into “Regulation of branched versus linear Arp2/3-generated actin filaments”.

Minor comments:

1 in 12 men and 1 in 200 women are red/green colorblind. Please change the coloring of the schematics and images so that they can be easily seen by all people. This is especially true of the schematics, which are important for understanding exactly what each assay is measuring.

We thank the reviewer for pointing this out. We have now made the schematics and images in Figs 1A, 2A, 2D and 4D colorblind-friendly.

The Introduction is a bit choppy and unfocused. It was difficult to deduce exactly where the paper was going from it. Please consider re-writing it for better clarity. The Discussion on the other hand was fantastic. Great job on interpreting your results in a larger context.

We have re-written large parts of the Introduction to make it clearer. We are glad the reviewer liked the Discussion, where we have nonetheless made some small changes in response to comments from the other reviewers.

Many figures- while the use of different lightness values of the same color is appreciated in conveying different concentrations of reagents used, there were several instances where it was very hard to read the one on the very bottom (ex. 2B, E; 3A; 5C, G).

We have now changed the colors in these figures, to make them clearer.

Figure 1- since this is a confirmation of previous results performed using the same proteins from other species, the title should reflect that (ex. VCA domains accelerate the nucleation of filaments by mammalian SPIN90-Arp2/3). Also, to me this figure is supplementary to the main message of the paper. The authors might think of moving it to Supplementary Information.

We have modified the title of Figure 1, now specifying “mammalian”, following the reviewer’s suggestion. However, we prefer to keep this figure as a main figure, rather than move it to Supplementary as proposed. Indeed, this figure does more than simply confirm previous results with mammalian proteins, since it compares different VCAs, which is new. These results are important because they are put in perspective with our results on the acceleration of linear filament detachment by different VCAs, later in the manuscript.

Figure 1- If the goal was to verify that G-actin recruitment by VCA was important for Spin90-Arp 2/3 nucleation by performing a competition experiment with profilin, why was the concentration of G-actin AND profilin increased between the experiments in 1B vs. 1C. It makes it hard to directly compare the results.

We now provide new data in Fig 1C, which can be directly compared to Fig 1B (only the profilin concentration was increased). It clearly shows that the effect of VCA disappears when the profilin concentration is increased.

Figure 4B-F- Here, it would be nice to see the distribution of all the individual results, which are hidden by the bar graph. Additionally, the Chi-square test is not the appropriate test for evaluating statistical significance between multiple groups. ANOVA followed by an appropriate post hoc test should be used here.

We now show the individual results in the bar graphs of figure 4. In this situation, we agree that the statistical significance should not be evaluated by a Chi-square test. We now indicate the p-values obtained from a paired t-test, which seems appropriate since we are comparing averages in pairs.

Figure 4G- Please quantify and show reproducibility.

We now show quantified repeats (shown in Fig 4, new panels H and I).

Figure 5- the piconewton forces used for these experiments is in line with measured forces that are applied to actin in cells (ex. Mehida et al, Nature Cell Biology 2021; Jiang et al, Nature 2003). The text would benefit if this was explicitly stated.

We now state this explicitly, when presenting these results.

Reviewer #1 (Significance (Required)):

The real significance of this work is in characterizing the differential stabilities of linear vs. branched Arp2/3 filaments in response to actin-binding proteins, mechanical stress, and aging. While both types of filaments respond similarly to actin-binding proteins, with nuanced differences, the most striking results came from applied force and aging experiments, with Spin90-Arp2/3 filaments being much more resistant to both. This has some very interesting implications for how these two types of assemblies might synergize in cells. Additionally, the results also have some exciting implications for the pointed-end regulation of actin filaments, which is still poorly understood in complex systems. Since the manuscript is A) more of a survey study on the factors that influence filament stability that does not go particularly deep into any particular mechanism of regulation and B) has no direct applicability to how the physical properties of branched and linear Arp2/3 nucleated actin filaments influence actin network activity in cells, the audience will likely by limited to actin enthusiasts. However, the work is still important in both what it reveals and implies.

We thank the reviewer for pointing out the novelty and the importance of our work. We agree that the significance of our paper lies in the characterization of the differential stabilities of linear vs. branched Arp2/3 filaments, in response to different physiological factors. One of the strengths of our approach is that we do not focus on one regulatory mechanism in particular. Rather, we reveal fundamental differences between the Arp2/3-generated filaments and how they can be regulated. Understanding these basic mechanisms is a prerequisite to understand the regulation of entire cytoskeletal networks.

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

The quantitative analysis can be improved. It appears that most of the data results from single experiments, with rate values and errors resulting from fitting of single experiments without repetitions. In Fig. 1C legend (p.5) the authors state "These experiments were repeated three times, with similar results", but the data is not used in the analysis and other experiments do not mention this point. This is particularly important for comparisons among different VCAs that are rather similar in nature. In Fig. 1B. N-WASP is more efficient in nucleating SPIN90-Arp2/3 complex-linear filaments followed by WASP and then WASH. In Fig. 2 B,C, N-WASP is the most effective in dissociating SPIN90-Arp2/3 complex linear filaments followed by WASH and then WASP. But in Fig. 2 E,F, WASH is by far the most effective in dissociating branches followed by N-WASP and then WASP. Therefore, the conclusion in the Discussion (p.12) "While these regulatory proteins similarly affect branched and linear Arp2/3-generated filaments, they do so with clear quantitative differences" is not supported by quantification. To remedy this problem the authors should include at least 3 repeats of each experiment in data analysis. Also, they could include an analysis of sequence differences among VCAs and discuss how these may correlate with the observed differences. For instance, one WH2 in WASP vs. two in N-WASP.

Indeed, we argue that the two forms of activated Arp2/3 differ in their sensitivity to different VCA motifs, based on how these VCA motifs rank in their ability to destabilize branched and linear filaments (the VCA motifs also rank differently in their activation and co-activation of Arp2/3 to nucleate branches and linear filaments, but this result does not contribute to our discussion of how proteins interact with the activated Arp2/3). Following the reviewer’s suggestion, we now show repeats of these experiments (new Supp Fig S2), clearly showing that N-WASP is the most effective in dissociating linear filaments while the differences are milder for dissociating branches, with WASH being at least as effective as NWASP. We now also discuss how this observation could relate to differences in sequence between VCAs (Discussion section and new Supp Fig S9).

Also, please note that, following a suggestion from Reviewer 3, we have now performed experiments with the CA-domains of NWASP (new Supp Fig S4C and S4D), which show that the V-domain plays an important role in debranching but plays no role in destabilizing SPIN90-Arp2/3 at filament pointed ends. These new results reinforce our statement that VCA affects branched and linear Arp2/3-generated filaments differently.

Reviewer #2 (Significance (Required)):

Arp2/3 complex is a 7-protein complex implicated in actin filament nucleation and branching. Arp2/3 complex-nucleated branched networks are found at several locations in cells and are responsible for processes such as cell motility.

Cao et al. compare the effect of several proteins on the filament nucleation activity of Arp2/3 complex, and the stabilization or destabilization of actin filament branches as well as linear actin filaments nucleated by SPIN90-Arp2/3 complex. The proteins tested include the VCA regions of three NPFs (N-WASP, WASP, and WASH) that activate Arp2/3 complex, GMF (a debranching protein) and cortactin (a branch stabilizing protein). For the most part, the study uses a single method, microfluidics-TIRF microscopy.

The main findings are:

1. VCA domains enhance nucleation of linear filaments by SPIN90-Arp2/3 complex in the presence of actin monomers.
2. However, VCA domains can also destabilize existing SPIN90-Arp2/3 complex linear filaments and branches, and this effect depends on the presence of of V-domain (WH2 domain that binds actin monomers).
3. The debranching factor GMF also destabilizes SPIN90-Arp2/3 complex linear filaments. Both GMF and VCA generate free pointed ends by dissociating Arp2/3 complex from pointed ends and SPIN90.
4. SPIN90-Arp2/3 complex linear filaments are less susceptible to force and aging than filament branches.
5. Cortactin stabilizes SPIN90-Arp2/3 complex linear filaments to higher degree than it does branches. These are novel and very interesting new observations of significant interest to the actin cytoskeleton field. Therefore, I recommend publication of this paper in EMBO J.

We thank the reviewer for their positive evaluation of our work.

I have one recommendation and one suggestion for improvement:

Major:

1. The quantitative analysis can be improved. It appears that most of the data results from single experiments, with rate values and errors resulting from fitting of single experiments without repetitions. In Fig. 1C legend (p.5) the authors state "These experiments were repeated three times, with similar results", but the data is not used in the analysis and other experiments do not mention this point. This is particularly important for comparisons among different VCAs that are rather similar in nature. In Fig. 1B. N-WASP is more efficient in nucleating SPIN90-Arp2/3 complex-linear filaments followed by WASP and then WASH. In Fig. 2 B,C, N-WASP is the most effective in dissociating SPIN90-Arp2/3 complex linear filaments followed by WASH and then WASP. But in Fig. 2 E,F, WASH is by far the most effective in dissociating branches followed by N-WASP and then WASP. Therefore, the conclusion in the Discussion (p.12) "While these regulatory proteins similarly affect branched and linear Arp2/3-generated filaments, they do so with clear quantitative differences" is not supported by quantification. To remedy this problem the authors should include at least 3 repeats of each experiment in data analysis. Also, they could include an analysis of sequence differences among VCAs and discuss how these may correlate with the observed differences. For instance, one WH2 in WASP vs. two in N-WASP.

This comment is identical to the reviewer’s first paragraph. We copy our answer here again, for convenience:

Indeed, we argue that the two forms of activated Arp2/3 differ in their sensitivity to different VCA motifs, based on how these VCA motifs rank in their ability to destabilize branched and linear filaments (the VCA motifs also rank differently in their activation and co-activation of Arp2/3 to nucleate branches and linear filaments, but this result does not contribute to our discussion of how proteins interact with the activated Arp2/3). Following the reviewer’s suggestion, we now show repeats of these experiments (new Supp Fig S2), clearly showing that N-WASP is the most effective in dissociating linear filaments while the differences are milder for dissociating branches, with WASH being at least as effective as NWASP. We now also discuss how this observation could relate to differences in sequence between VCAs (Discussion section and new Supp Fig S9).

Also, please note that, following a suggestion from Reviewer 3, we have now performed experiments with the CA-domains of NWASP (new Supp Fig S4C and S4D), which show that the V-domain plays an important role in debranching but plays no role in destabilizing SPIN90-Arp2/3 at filament pointed ends. These new results reinforce our statement that VCA affects branched and linear Arp2/3-generated filaments differently.

Minor:

In GST-pull-down experiments (Fig. 4G), the amount of Arp2/3 complex bound is analyzed by Western, which is rather unprecise. Is the amount of Arp2/3 complex so little that it cannot be quantified using regular SDS-PAGE? If that is the case, this would suggest rather low affinity of SPIN90 for Arp2/3 complex. How does this affect the proposed mechanism and experiments in the microfluidics chamber?

Indeed, the amount of pulled-down Arp2/3 is low and difficult to quantify by SDS-PAGE. This is consistent with previous reports which indicate a low affinity of SPIN90 for the Arp2/3 complex (Wagner et al. Current Biology 2013, Balzer et al. eLife 2020). This does not affect our conclusions, which we now confirm by showing quantified repeats of our pull-down experiments (new panels H and I, in Figure 4). In spite of this low affinity, which makes it difficult to saturate SPIN90 with Arp2/3, the SPIN90-Arp2/3 interaction is very stable and allows us to carry out our experiments in the microfluidics chamber over several tens of minutes (as was already the case in our previous study, Cao et al. NCB 2020).

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

Summary:

In this study, Cao and collaborators investigate the biochemical and mechanical differences between branched actin filaments nucleated by WASP-activated Arp2/3 complex and linear actin filaments nucleated by SPIN90-activated Arp2/3 complex. They use TIRF microscopy in a microfluidic chamber to show that the mammalian proteins, SPIN90 and WASP (or N-WASP or WAVE), like their yeast homologues, co-activate Arp2/3 complex to nucleate linear actin filaments. Using the same assays, they find the surprising result that the VCA segment of WASP proteins destabilizes the interaction between SPIN90 and Arp2/3 complex in linear actin filaments nucleated by Arp2/3 complex. They then show that VCA also destabilizes actin filament branches. The remainder of the study explores the influence of branch stabilizing/destabilizing proteins or mechanical stress on the stability of the interaction between SPIN90 and Arp2/3 complex on the pointed end of the actin filament. They find that like branch junctions, SPIN90-bound Arp2/3 is destabilized at the end of linear filaments by GMF and stabilized by cortactin. However, unlike branch junctions, SPIN90-Arp2/3 complex is not destabilized on filament ends by piconewton forces or by aging. They conclude that SPIN90- versus VCA-activated Arp2/3 complex adopt similar but non-identical conformations.

Overall, the paper is well written and the experiments, which are very challenging, are rigorously executed. The biochemical results are convincing, novel and unexpected. However, the work could be strengthened by more strongly connecting the biochemical observations to biological implications. In addition, there are some interpretations/conclusions that seem somewhat weakly supported, and the authors should consider revising. Nonetheless, given the quality of the work and the importance of the system, this manuscript will appeal to a broad audience.

We thank the reviewer for their positive comments. We have rewritten parts of the Discussion in order to better connect our observations to implications in cells. We address the concerns regarding our interpretations in the point-by-point, below.

Comments on evidence, reproducibility, clarity and significance:

The differences in the stability of SPIN90-Arp2/3 on linear filaments verses branch junctions led the authors to conclude that SPIN90- versus VCA-activated complexes adopt similar yet non-identical conformations. There are two problems with this conclusion:

1) This conclusion rests on the idea that the biochemical differences can only be due to differences in the "ground state" active conformations of the complex. Another possible scenario would be that the active conformations are the same, but the transition state or intermediate state structures within the debranching reactions are different, thus changing the kinetics of the debranching reactions.

We thank the reviewer for this remark, and we agree that conformational differences may also arise in the intermediate states, during dissociation (of the branch from the mother, or of the linear filaments from SPIN90). We now mention this possibility in our Discussion.

2.) There are already structural data showing conformational differences between the Dip1-bound Arp2/3 complex on the end of a linear filament and Arp2/3 complex at a branch junction. While there are some caveats to comparisons of the structures (e.g., the Dip1 structure includes the fission yeast SPIN90 protein (Dip1) and the fission yeast Arp2/3 complex while the branch junction contains mammalian proteins), these data offer much stronger evidence that the active states adopt (somewhat) different conformations than the data presented here.

We agree that the available structural data (in particular, Ding et al. PNAS 2022, which was not yet published when we submitted our manuscript, and which we now cite) provide a clear indication that active Arp2/3 adopts different conformations in branches and linear filaments. We have modified our text to make this point clearer.

The authors make comparisons between the Fäβler branch junction structure and the Shaaban Dip1-Arp2/3-filament structure. The Fäβler branch junction structure is a low resolution structure (9 angstroms) and should be interpreted with caution (see below). A much higher resolution of a branch junction structure was recently solved (Ding et al, PNAS 2022) and should be used for comparisons between the structures.

Ding et al. PNAS 2022 was not yet published when we submitted our manuscript. We now use it to compare the structures of active Arp2/3, and we have modified the text accordingly.

Pg 14 - The authors say differences between ARPC3-Arp2 and ARPC5-Arp2 contacts in the two structures are likely to cause the differences in interactions with GMF and VCA. Two concerns with this statement are: 1.) The basis for the conclusion that the ARPC5-Arp2 contacts are different (in Fäβler, et al.) is not solid (see Ding, et al) and 2.) The analysis is vague. To reasonably conclude that differences in the contacts would influence GMF and VCA interactions would require mapping out the structural connection between the ARPC3-Arp2 interaction site and the GMF or VCA binding sites. If there is no obvious connection between these sites, the conclusion that the differences in the ARPC3-Arp2 interface cause differences in VCA and GMF binding should be far more circumspect.

We have re-written this part of the Discussion section. In light of the new data by Ding et al., we agree with the reviewer that the conclusion that the ARPC5-Arp2 contacts are different is not solid. Our revised text makes it clear that we are not making any claims involving interactions within the Arp2/3 complex. Our point is simply that recent cryo-EM reports indicate conformational differences in Arp2 and Arp3 between the two activated forms of the Arp2/3 complex and that, since the CA-domain of NPFs bind to Arp2 and Arp3, it appears reasonable to make a connection with our results.

Pg 6. "These observations suggest that the ability of VCA to destabilize Arp2/3-nucleated filaments relies on the availability of its V-domain." It's possible that G-actin binding to V blocks the CA from accessing the branch junction. Therefore, it seems important to test whether N-WASP-CA can destabilize Arp2/3-nucleated actin filaments.

We thank the reviewer for this suggestion. We now present results from new experiments performed with the CA-domain of NWASP (new Supp Fig S4C,D). We find that the V-domain participates in the enhancement of debranching, but that it appears to play no role in the destabilization of SPIN90-Arp2/3 from the pointed end. It thus seems that the reviewer’s proposal is correct, and that G-actin binding to the V-domain blocks the CA-domain from accessing the branch junction. We now propose this interpretation in the text.

Pg 1 - The authors state that "It thus appears that linear and branched Arp2/3-generated filaments respond similarly to regulatory proteins, albeit with quantitative differences". It is worth considering if one should make a blanket statement that linear and branched filaments respond similarly to regulatory proteins when they have tested 3 in total.

We have rephrased this sentence. It now reads “… respond similarly to the regulatory proteins we have tested…”

Pg 3 - "More generally, the stability of SPIN90-Arp2/3 at the pointed end, which is important to understand the reorganization and disassembly of actin filament networks, remains to be established." In some ways this statement not quite accurate because Balzer et al previously showed that Dip1-Arp2/3 complex is very stable at the pointed end. Is the question here whether that stability is also conserved in mammalian systems? If so, that should be more directly stated.

We meant that, beyond observing that SPIN90 remains visible at the pointed end for some time (as in Balzer et al.), a lot remained unknown: its lifetime had not been quantified, and its sensitivity to the factors that affect branch junctions (proteins, aging, mechanical tension) had not been studied. We have rephrased the sentence in the manuscript to clarify this point.

The observation that VCA accelerates debranching and SPIN90-Arp2/3 dissociation is very interesting. However, it is uncertain if this biochemical activity has biological relevance, given that once nucleation occurs, Arp2/3 complex will move away from the membrane. While the authors mention in the discussion that debranching by VCA could be relevant when the network is compressed near the membrane, this argument is not particularly strong. Are there ways to strengthen this argument, or find another impact this finding might have on our understanding of Arp2/3 complex regulation?

We now mention another situation where branch junctions could encounter membrane-bound VCA domains: on the dorsal and ventral membrane surfaces of lamellipodia. We now cite the recent Kage et al. J Cell Science 2022 and Mehidi et al. NCB 2021, where WAVE has been observed in lamellipodia away from the leading edge.

The observation that SPIN90+Arp2/3-nucleated filaments are not sensitive to piconewton forces is also very interesting. The authors focus on the differences in the amount of surface area buried when discussing this result. However, if seems a key factor in the stability of the linear filaments would be the direction of the force relative to the complex and attached filament(s), which would be very different for a branch versus a linear filament. The authors should consider addressing this in their discussion.

The orientation of the applied force is an interesting point. In their study on debranching, Pandit et al. (PNAS 2020) report that their results are not affected by the angle of the applied force relative to the mother filament (their Fig S1D). We now specify this in our manuscript, when introducing our results on mechanical tension. Similarly, we found that anchoring SPIN90 to the coverslip surface by its N-terminus rather than its C-terminus, which likely affects the orientation of the applied force, had no impact on our results (Supp Fig S6A). We have now also added a sentence regarding this aspect in our manuscript, after presenting this result.

Fig 4, D-F: It is unclear how the authors determined which filaments were spontaneously nucleated versus those that were nucleated by SPIN90-Arp2/3 complex in these experiments. In reactions containing SPIN90 and Arp2/3 complex what fraction of the filaments will be spontaneously nucleated?

In our conditions, there is no detectable spontaneous nucleation. In control experiments where we flow in the same concentration of G-actin, in the absence of Arp2/3 or in the absence of SPIN90, we observe no filaments at all on the surface, over several fields of view, after 5 minutes. We now specify this in the Methods section.

Pg 9 - The observation that VCA negatively influences binding of SPIN90 to the complex is unexpected. What implications does this have for understanding how SPIN90 and VCA synergize to activate the complex?

It appears that the outcome depends on the context. The main role of VCA during co-activation of the Arp2/3 complex with SPIN90 seems to be to supply G-actin, as already proposed (Balzer, 2020) and confirmed by our results (Fig 1C). In the absence of G-actin, VCA is more likely to remove Arp2/3 from SPIN90 (Fig 4G,I). Similarly, when a filament is already formed, the presence of G-actin mitigates the removal of SPIN90-Arp2/3 from the pointed end by VCA (Supp Fig S4).

Fig 4B - Why is there greater nucleation when Arp2/3 complex and GMF are added together compared to renucleation in reactions that don't have any GMF? This is surprising, especially considering that GMF decreases binding of Arp2/3 complex to SPIN90.

Indeed, there is a small yet statistically significant difference in the re-nucleation fraction we measured in the presence of Arp2/3, with or without GMF (Fig 4B). This may be due to the different timescales of the two situations. In the absence of GMF, the detachment of filaments is slow and new filaments are nucleated from the initial Arp2/3 complexes, which remained bound to SPIN90 upon detachment of the first filaments. In contrast, in the presence of GMF, detachment is faster and accompanied by the departure of the initial Arp2/3, and a fresh Arp2/3 then binds to SPIN90 to nucleate a new filament. It is thus possible that, in the absence of GMF, a small fraction of the SPIN90 and/or their initially bound Arp2/3 complexes would denature over the time they spend at the bottom of the microchamber at 25°C, thereby leading to a slightly smaller re-nucleation fraction. A similar mechanism could be at play in the experiments with or without VCA, in addition to the enhancement of nucleation by VCA (Fig 4C).

Minor Corrections/Comments

Pg 3 "We show that Arp2/3 nucleation is similarly stabilized by cortactin and destabilized by GMF" Do the authors mean branches and linear filaments nucleated by Arp2/3 complex?

Yes, that is what we meant. This sentence has now been modified.

Pg 6- The cyan 3uM data and legend in figure 2B and E is probably too dim to see clearly.

The colors have been changed to improve readability.

Fig 4 B,C,E,F: It would be best to show the individual data points here if possible.

We now show individual data points in all these figure panels.

Pg 16 Please specify which antibody was used to anchor SPIN90.

The antibodies are Anti-GST for Nter anchoring of GST-SPIN90, and anti-His for Cter anchoring of SPIN90-His. We now specify this in the Methods section.

CROSS-CONSULTATION COMMENTS I agree with the points that the other reviewers raised.

Reviewer #3 (Significance (Required)):

Comments on significance are in the above section.

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Reply to the reviewers

We thank all three reviewers for their thoughtful and rigorous critique of our manuscript, which we feel has significantly improved the presentation of our work. Below we detail point-by-point responses to comments made by the three reviewers as well changes we have already made addressing the majority of minor and some major points.

Specification of the eye-field during gastrulation represents the earliest known stage of eye development. Using an optic-vesicle organoid model system, the overall goal of our work is to provide an unbiased characterisation of this critical, early developmental event in mammals and to gain insights into relevant gene regulatory mechanisms. A common theme to some of the reviewer comments is that this work doesn't provide much of an advance to the field and our findings are not particularly original. We feel that these comments are slightly harsh for the following reasons. Firstly, although some of our findings are not unexpected, to our knowledge, this is the first unbiased characterisation of the eye-field in a mammalian model system, and not based on knowledge gained through previous work in other non-mammalian vertebrate systems, e.g. Xenopus. Secondly, by generating both RNA-seq and ATAC-seq from a timecourse of organoid development we have been able to quantify dynamic patterns of gene-expression as the eye-field is established and simultaneously gain insights to the regulatory role of some of the key transcription factors, both of which are not present in the literature. Thirdly, by constructing careful, integrated analyses of our RNA-seq and ATAC-seq datasets we were able to generate specific hypotheses regarding cis-regulation of key genes, which we have then demonstrated are possible to efficiently test within the organoid system. In all, although we have been purposely careful not to overinterpret our results, we feel our work does represent a significant step towards understanding the mammalian eye field and additionally provides important datasets as well as an analysis framework to begin to quantitatively probe the regulatory mechanisms underlying the transition to an ocular fate. Given the relevance of this developmental event to clinical genetics research as well as to developmental biology we are confident that this work represents an important and significant advance to the literature.

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

Summary Owen et al. characterize the transcriptome and chromatin accessibility of mouse retinal organoids at early stages during which eye field-like cells are specified. Since cell specification and differentiation in retinal organoids largely mimic those processes in vivo, retinal organoids are viable models for studying the mechanisms of early eye development. Owen et al. utilize a previously established Rx-GFP cell line, bulk RNA sequencing, and bulk ATAC sequencing to dissect the mechanisms of early eye development in mice. Their findings are generally consistent with previous studies. Overall, the study is interesting for the field, but its conceptual and technical advances are moderate. In addition, a few major points need to be clarified.

Major points 1. The authors did not show any analysis of retinal organoids at stages when Vsx2 is expressed. This is a significant weakness since the chemically defined medium (CDM) used in Owen et al.'s study was previously shown to induce rostral hypothalamic differentiation (Wataya et al., 2008). Related to this notion, several eye-field transcription factors, such as Rax and Six3, are also expressed in the hypothalamus. Therefore, Owen et al. need to demonstrate that organoids in their modified differentiation system efficiently produce Vsx2-positive retinal progenitors, and samples of organoids at stages when Vsx2 is expressed should be included for RNA sequencing. If Vsx2 is not efficiently expressed in their organoids, the interpretation of results will be very different.

We thank the reviewer for their important comments here. There are several reasons why we are confident that our data and conclusions regarding the organoid eye-field are robust. Firstly, our RNA-seq data, in particular the differences between GFP-positive and GFP-negative cells, clearly show a coordinated up-regulation of the set of canonical eye-field TFs (not individually), which previous studies in Xenopus have shown is a prerequisite for differentiation into anterior eye structures (including retina). Secondly, we have checked that some of the later (in development) eye markers, including Vsx2, are differentially up-regulated (DeSeq2, logfc>1.5, FDRIn all, we are very confident that our approach of using the optic-vesicle organoids and generating molecular data from an organoid developmental timecourse (including sorting), is unpicking the ocular-fate transition event that we are interested in.

1. The authors state that "two differentiation medias were used for this work due to the differentiation becoming unstable after the initial experiments had been performed. The organoids used for RNA and ATAC-seq were grown in CDM media and the organoids with mutations introduced in potential CREs were grown in KSR media". Why the differentiation becomes unstable after the initial experiments? Differences in the two media cause additional complexities. Related to this notion, "WT Rx-GFP" in Figure 4B and 4E appears to show a different expression pattern compared to that in Figure 1A.

We were unable to identify the reason behind the destabilisation of differentiation in CDM media after the cell lines had been through CRISPR despite thorough testing. The differentiation of these cell lines was stabilised enough using KSR media such that every batch of organoids grown contained some organoids that expressed GFP in a pattern similar to what we had seen before and we carried on our experiments using this. We recognise that using two different media adds complexity, however we see the same patterns of organoid growth and GFP expression when differentiating untransfected WT Rax-GFP cells in both of these medias. We have edited Fig.S1 to include representative images of organoids grown in KSR media which can be directly compared to those grown in CDM shown in Figure 1A.

The reviewer has pointed out that the WT Rx-GFP organoids in Figure 6B and 6E show a different expression pattern to those in figure 1A. With the addition of the supplemental figure mentioned above it becomes apparent that these differences are not due to the change of media. We have clarified in the text that these WT cells have also been transfected so as to act as appropriate controls that have been treated identically to the CRISPR edited cell lines and that this has affected their differentiation capacity.

1. Is the deletion of Rax and Six6 regulatory elements homozygous? Sanger sequencing or amplicon sequencing is needed to show the deletion.

The deletions are homozygous (we have stated this in the manuscript text) and as suggested we have added a supplementary figure showing the Sanger sequencing traces for the WT and mutant cell lines used in this study.

1. The deletion of Rax and Six6 regulatory elements appears to cause minor changes in the expression of Rax and Six6 (Figure 6C, F). Therefore, the impact of findings in bulk RNA seq and bulk ATAC seq in this study is still unclear.

We have added a sentence to the text underlining that developmental genes are expected to be regulated by multiple enhancers. Our expectation is therefore, that in perturbing a single putative regulatory element for Rax/Six6, we will very likely not see the complete ablation of Rax/Six6 expression.

1. Retinal organoids and sorted cells are composed of heterogeneous cell populations. Bulk RNA seq and bulk ATAC seq do not have the power to dissect the complexity of heterogeneous cell populations. Single-cell RNA seq and single-cell ATAC seq are more powerful for this study.